eLife Assessment

This manuscript presents valuable experimental results describing the localisation and regulation of casein kinase CK1δ during the cell cycle. During the G2 phase of the cell cycle, the autophosphorylation of the C-terminal tail stabilises and inhibits the kinase which might protect CK1δ in the subsequent G1 phase. The results may be of interest to researchers working on casein kinase function and regulation but due to lack of some controls remain incomplete.

[Editors' note: this paper was reviewed by Review Commons.]

Reviewer #1 (Public review):

Summary:

Involved in various cellular pathways and processes, Ser/Thr kinase CK1δ is thought to be constitutively active and its tail autophosphorylation is suggested as a putative inhibitory mechanism of CK1δ kinase activity. Here, the authors investigate CK1δ's phosphorylation status, in relation to its location and dynamics throughout the cell cycle. Immunofluorescence and biochemistry studies showed that the subcellular distribution of CK1δ is dynamic and in equilibrium between centrosomal and nuclear pools. The authors argue that CK1δ phosphorylation protects it from degradation. Finally, the authors show differences in CK1δ phosphorylation status and location throughout the cell cycle. Combining their findings with the existing literature, they propose a model of CK1δ phosphorylation status, location and dynamics throughout the cell cycle.

Comments on latest version:

The authors have unfortunately taken a very defensive mode There are two themes that authors resort to: 1) We have published previously with some reagents - therefore these are well-established and we do not need to include controls anymore; 2) Independent biological replicates and statistics are only appropriate in some places, again because certain observations have been previously published (by the same authors) and well-established. In my opinion, this is not how rigorous research should be done. Specially with IF, it is essential in every experiment to have robust negative controls.

Reviewer #2 (Public review):

Summary:

In this study, Serrano et al. employed a combination of cell biological and molecular approaches to investigate the localization and regulation of Casein Kinase CK1 during the cell cycle using U20S cells. They show that CK1 dynamically localizes between the centrosomes and the nucleus but can be sequestered away from the centrosomes upon overexpression of its binding partner PER2. They provide evidence that CK1 WT but not a phospho-null mutant strongly accumulates in a hyperphosphorylated form upon inhibition of phosphatases (using Calyculin and Okadaic Acid) and thus conclude that CK1 tail phosphorylation protects the kinase from degradation. Using synchronized cells, they show that CK1 accumulates unphosphorylated in S-phase (APC/Cdh1 inactive) but phosphorylated at the G2-M transition. Immunostaining shows that CK1 localizes to the centrosomes during mitosis.

Strengths:

The authors reveal that the activity and abundance of dephosphorylated and phosphorylated CK1δ are regulated in a cell cycle-dependent manner. This suggests that these different pools are associated with distinct physiological functions.

Comments on latest version:

Unfortunately, problems with controls remain in the revised manuscript. At the very least, the authors should include all the necessary controls in their study instead of referring to previously published papers. I have asked for a detailed description of the kinase construct in which the phospho-Serine and Threonine of the C-terminal tail are substituted, but I did not see any more information in the revised version.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

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.

We selected the CK1δ antibody (abcam, ab85320 clone AF12G4) precisely because of its well-established specificity for CK1δ. In many well-cited studies [An et al., Nature Communications, 2022, PMID: 35810166], [Eng et al., PLOS One 2017, PMID: 28545154], some of which involve direct comparison with CK1α and CK1ε [Sinnberg et al., BMC Cancer, 2016, PMID: 27488834], [Beale et al., Journal of Biological Rhythms, 2019, PMID: 30898060], the CK1δ (ab85320) antibody is cited directly as the antibody used to specifically detect CK1δ.

Additionally, through our previous eLife paper, we have confirmed the observation from previous studies that clearly demonstrate that this CK1δ (ab85320) antibody can specifically recognize CK1δ and not even its closest homolog CK1ε. Given the high degree of conservation in the kinase region between CK1δ and CK1ε, this implies that this antibody is likely directed at the divergent C-terminal tail (see sequence alignments in Author response image 1). Given that CK1α C-terminal tail is even more divergent from CK1δ, along with its reliable use in the literature from multiple working groups, it is safe to assume that this antibody can reliably distinguish CK1δ from CK1α.

Author response image 1.

Protein sequence alignments between CK1δ, CK1ε, and CK1α highlighting high sequence conservation in the structured kinase domain and sequence divergence at the C-terminal tail.

b. Fig. 1: Statistical analyses are missing from the analysis.

We have clearly added statistical analysis showing significant differences of CK1δ localization at the centrosome.

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.

CK1δ colocalization is already well-established in the literature and additionally demonstrated in this study with the clear colocalization in Figures 1C and 1D. In Figure 2, we have chosen to report representative images which correspond to the typical phenotype we observe and can compare side-by-side which show clear and striking differences in terms of CK1δ localization between a) cells that form foci and lose CK1δ localization at a clear and distinct centrosome and b) cells that do not form foci and CK1δ is clearly localized to the apparent centrosome. By showing several fields-of-view, we demonstrate that this is the prevalent comparative phenotype.

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.

It is well-established that centrosomal duplication is a key hallmark of G2. Combined with our observations from Figure 2 showing that CK1δ to distinct puncta that one can only assume is the centrosome, and now showing in Figure 6, a clear duplication of these puncta. Importantly, this occurs in cells that also exhibit higher DAPI staining consistent with the duplicated and condensed genomic state when compared to other cells in the field of view, another hallmark of G2. Therefore, additional centrosomal staining and colocalization will only confirm what we already know about typical hallmarks of G2 and wider mitosis and the established CK1δ localization to the centrosomes.

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.

We have mentioned the number of independent biological replicates where we considered it appropriate in Figures 3, 4, and 5. Figure 1 A and B are representative fields-of-view which show a replicable phenotype and we have quantified 10 cells to show the statistical difference in CKδ colocalization to PCNT. Figure 1 C and D show individual representative cells used for the line plot analysis but as one can already see from Figures 1 and B, these observations are clearly reproducible. Figure 2 A is an additional representative photo from observations we have made in our previous eLife publication. Figure 2 B already shows multiple fields-of-view which show a replicable result. Figure 6, again, shows a representative series of cells which already clearly demonstrate the change in CK1δ localization over the course of mitosis.

(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.

I find it hard to seriously answer to these points. I do not know what kind of reagents the reviewer is used to work with. On every experiment we show as a sub-figure, we use the same CalA that clearly works as intended since we can clearly see a phosphorylation-induced gel shift of the kinase. This rules out aliquots losing their potency or supplier providing the wrong compound. We also show a clear negative control in showing the absence of the gel shift prior to CalA treatment.

On a separate note, we have no experiments with siRNA so we are unsure what the reviewer is referring to here. Of the 11 immunoblots we report here, each of which are representative of a triple replicate, only 1, Figure 3B, shows a split view on an equal exposure. Even then this was actually run on the same gel and this figure was simply spliced to simplify the message we want to convey. Therefore, we believe we have used the appropriate controls and level of rigor to make our observations and interpret them adequately.

(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.

We have clearly demonstrated that CKδ tail phosphorylation leads to kinase inhibition and refer the reviewer to our work in PNAS [Marzoll et al., PNAS, 2021; PMID: 35217617].

(5) It would be important to include statistical analyses for the immunofluorescence data in Fig. 1 and 2.

We have included statistical analysis where we considered it appropriate in Figure 1 A and B. In Figure 1 C and D, statistical analysis is not appropriate to apply to compare single line plots as the individual data are clearly distinct from one another. For Figure 2 A and B, again, we are showing this data to show what is already a clear difference in CK1δ centrosomal localization when we compare cells that either form PER-CRY foci or do not.

(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.

We respect the reviewer’s opinion on this matter. However, the earlier study was independently peer-reviewed and has already been published. The reviewer was not involved in the assessment of that work, and we therefore feel that a retrospective evaluation of its merits is beyond the scope of the present review. We would respectfully ask that the current manuscript be evaluated on the basis of the questions it addresses and the evidence presented here.

(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.

We respectfully point out that the purpose of the present review is to assess the manuscript under consideration, not to retrospectively reassess data that have already been published, such as those reported by Penas et al., even if this is the only study we cite in support of this particular point.

After checking the peer review received from Review Commons, we cannot see the “investigations in our original comment” that this reviewer is referring to.

Reviewer #2 (Public review):

In this study, Serrano et al. employed a combination of cell biological and molecular approaches to investigate the localization and regulation of Casein Kinase CK1 during the cell cycle using U20S cells. They show that CK1 dynamically localizes between the centrosomes and the nucleus but can be sequestered away from the centrosomes upon overexpression of its binding partner PER2. They provide evidence that CK1 WT but not a phospho-null mutant strongly accumulates in a hyperphosphorylated form upon inhibition of phosphatases (using Calyculin and Okadaic Acid) and thus conclude that CK1 tail phosphorylation protects the kinase from degradation. Using synchronized cells, they show that CK1 accumulates unphosphorylated in S-phase (APC/Cdh1 inactive) but phosphorylated at the G2-M transition. Immunostaining shows that CK1 localizes to the centrosomes during mitosis.

The manuscript has improved overall, but some sections are still inconclusive and require clarification.

Major comments:

Figure 1 is inconclusive. CK1 nuclear staining is highly similar in untreated cells and in cells treated with CHX + PF670462. The reduction in centrosomal staining in these cells is barely significant. However, the authors draw very strong conclusions from these data sets. In panel B, the cells appear to have been fixed incorrectly, and the anti-PCNT shows a strong background signal. Not convinced that immunofluorescence is the best approach to look at protein dynamics in vivo.

Figures 1 A and B are meant to show how CHX and PF670462 may affect CK1δ localization to the centrosome (stained by PCNT) over several cells whereas Figures 1 C and D are meant to more clearly show this effect in individual cells. This effect is indeed modest in the endogenous situation compared to the overexpressed which shows a clearer redistribution of CK1δ. We show this when we compare the quantification in Figure 1A and the colocalization analysis in Figure 1 C (right panel; showing that some CK1δ still colocalizes to the PCNT-stained centrosome) to their overexpressed counterparts. This however, only emphasizes the strength of our overexpression approach as it has allowed us to observe a more dramatic shift in CK1δ centrosomal localization.  

In Figure 2, panel B, the authors should co-stain the centrosomes of cells that co-express CRY1 and CK1, as some of these dots may represent the centrosomes.

In principle, we indeed cannot exclude the possibility that a CRY-stained foci may actually be a centrosome. However, we refer to our comments to Reviewer #1 and add our observation that these PER-CRY foci are clearly nuclear based on our earlier eLife publication and are therefore unlikely to be centrosomal. (If some of the dots represent centrosomes, this would mean that a fraction of CRY1 is recruited from the nucleus to the centrosome in the cytosol. There is no mechanism for this known.)

Figures 3B, please provide information on the non-phosphorylable CK1a mutant (it is mentioned as a variant in which all serine and threonine residues in the C-terminal tail were replaced by alanine). Specify the number of sites mutated and their exact position. Is this non-phosphorylable CK1a version catalytically active?

As said, all serine and threonine residues in the tail have been changed, and yes, the kinase is of course active.

Treatment of samples with inactivated PPase should be used as a control.

It is unclear what this experiment would control for and how its outcome would affect any of the conclusions of the present study.

Strengths:

The authors reveal that the activity and abundance of dephosphorylated and phosphorylated CK1δ are regulated in a cell cycle-dependent manner. This suggests that these different pools are associated with distinct physiological functions.

Weaknesses:

Unfortunately, some of the data are inconclusive, and there is no data/information linking the cell cycle regulation of CK1δ to its function during the cell cycle.

Although CK1δ continuously undergoes cycles of autophosphorylation and dephosphorylation, the kinase is predominantly found in its dephosphorylated, active state under steady-state conditions. This has obscured the physiological relevance of its well-established inhibitory autophosphorylation. We now identify mitosis as the cellular state in which this equilibrium shifts: autophosphorylated and consequently inhibited CK1δ accumulates. These findings resolve a longstanding question regarding the physiological function of CK1δ autophosphorylation and reveal it as a cell-cycle-regulated mechanism of kinase inhibition.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Most of our minor comments related to editorial issues have been ignored by the authors and the errors persist. Simple corrections will improve the manuscript and make it more readable.

We also found new minor errors as follows:

69-70: 'dependent on its kinase is activity' --> 'its kinase activity'

164: 'sites or targeted by' --> 'sites are targeted by'

179: 'PF670' instead of 'PF670462'

292: 'against higher the steady state levels' --> 'against the higher steady state levels' or 'against higher steady state levels'

We thank Reviewer #1 for their close reading of our text. We have adjusted the text accordingly.

eLife Assessment

This study provides an important insight into how the medial and lateral entorhinal cortices interact through distinct excitatory and inhibitory pathways. Using anatomical tracing, optogenetics, and electrophysiology, the authors show that glutamatergic medial entorhinal neurons provide broad excitatory input to lateral entorhinal, while long-range SST+ interneurons deliver selective inhibition to layer I. These findings reveal a novel layer- and cell-type-specific organization of medial to lateral entorhinal connectivity with implications for spatial and episodic memory. The evidence for the paper's overall conclusions is convincing.

Reviewer #1 (Public review):

The study addresses the organisation of synaptic connections from medial to lateral entorhinal cortex. Classic anatomical work has suggested these connections exist but very little is known about their identity or functional impact. The manuscript argues that these projections are mediated by glutamatergic neurons, providing excitatory input from MEC to all layers of LEC, and by SST+ve interneurons sending inhibitory projections to L1 of LEC. This appears the most likely interpretation of the data. Potential concerns about confounds due to spread of virus/tracer from the injection site are addressed in the supplemental figures. My view is that the weight of evidence favours the authors' interpretation although the evidence isn't quite compelling.

Knowing the configuration of projections from MEC to LEC is important for thinking about circuit mechanisms for spatial cognition and episodic memory. This study adds to an emerging view that MEC and LEC can interact directly, indicating that the cell-type level organisation of these interactions is asymmetric and identifying an intriguing long range inhibitory pathway.

Reviewer #2 (Public review):

Summary:

The manuscript by Nilssen et al. presents a comprehensive study of the circuitry linking the medial and lateral entorhinal cortices (MEC and LEC). Using a combination of anatomical tracing, optogenetics, and in vitro electrophysiology, the authors convincingly demonstrate that the MEC sends both glutamatergic and long-range inhibitory SST+ GABAergic projections to the LEC, with distinct laminar and cell-type-specific targeting. Notably, they reveal that SST+ inhibitory projections selectively suppress the activity of layer IIa neurons, whereas excitatory inputs preferentially engage neurons in layers IIb and III, thereby differentially modulating hippocampal-projecting populations.

Strengths:

The experiments are carefully executed, the results are compelling, and the conclusions are well supported by the data. This work will be of broad interest to researchers studying memory circuits, cortical inhibition, and the organization of long-range connectivity.

Weaknesses:

Although the in vivo relevance of these connections remains to be determined, this is an important and timely contribution to our understanding of entorhinal-hippocampal interactions.

Comments on revised version.

The authors have addressed my comments satisfactorily, and I am satisfied with the changes made in the revised version.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

The study addresses the organisation of synaptic connections from the medial to the lateral entorhinal cortex. Classic anatomical work has suggested these connections exist, but very little is known about their identity or functional impact. The manuscript argues that these projections are mediated by glutamatergic neurons, providing excitatory input from MEC to all layers of LEC, and by SST+ve interneurons sending inhibitory projections to L1 of LEC. This appears to be the most likely interpretation of the data, although in my opinion, more could be done to rule out the possible impact of the spread of the virus/tracer from the injection site.

While this concern might seem overly picky, the importance of this level of detail is nicely shown by the authors' previous work clarifying connectivity from postrhinal to entorhinal cortices through careful analysis of similar types of data (Doan et al. 2019). If additional analyses/data can address the concern here, then I think this will be an important set of fundamental results that will influence thinking about circuit mechanisms for spatial cognition and episodic memory. In particular, it will nicely add to an emerging view that MEC and LEC can interact directly, showing that the organisation of these interactions is asymmetric and identifying a potentially interesting long-range inhibitory pathway.

Reviewer #2 (Public review):

Summary:

The manuscript by Nilssen et al. presents a comprehensive study of the circuitry linking the medial and lateral entorhinal cortices (MEC and LEC). Using a combination of anatomical tracing, optogenetics, and in vitro electrophysiology, the authors convincingly demonstrate that the MEC sends both glutamatergic and long-range inhibitory SST+ GABAergic projections to the LEC, with distinct laminar and cell-type-specific targeting. Notably, they reveal that SST+ inhibitory projections selectively suppress the activity of layer IIa neurons, whereas excitatory inputs preferentially engage neurons in layers IIb and III, thereby differentially modulating hippocampal-projecting populations.

Strengths:

The experiments are carefully executed, the results are compelling, and the conclusions are well supported by the data. This work will be of broad interest to researchers studying memory circuits, cortical inhibition, and the organization of long-range connectivity.

Weaknesses:

Although the in vivo relevance of these connections remains to be determined, this is an important and timely contribution to our understanding of entorhinal-hippocampal interactions.

The request for validation of injection specificity and viral spread, as detailed in the comments and suggestions of the two reviewers has been provided in the revised version. We added supplementary figures 1,2 and 6 as well as an extra insert into the old supplementary figure 5, now supplementary figure 9.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Major Points:

(1) Interpretation of the retrograde labelling experiment in Figure 1A-C is challenging, as the spread of the tracer at the injection site is not shown. It's important to see the full dorsal-ventral extent of the injection site in order to establish that the labelling of neurons in MEC results from projections to LEC and not adjacent areas (including MEC).

As mentioned in our initial reply, we are fully aware of the risks associated with an incomplete assessment of injection sites and viral spread, so we provide a new Supplementary Fig. 1 showing 6 dorsoventral levels of the case shown in Fig. 1A. The injection site in case of FG often shows a core of damaged tissue with a halo of substantial unspecific fluorescence. Outside of the injection side, one only sees retrogradely labeled somata (often recognizable by FG signal clustered in lysosomes) and dendritic elements. As indicated in the legend, we report some tracer leakage along the needle track in temporal and perirhinal cortex, areas that receive only sparse MEC projections, but there is no apparent spread of the injection into MEC.

Numbers are also quite low. E.g., Figure 1A is N=1/2 for retrograde labelling experiments.

The reviewer would be correct if the experiments were meant to analyze MEC projections to LEC in full anatomical detail. This was not our intention (several papers addressed this pathway in detail), we merely aimed to distinguish between glutamatergic and potential GABAergic contributions to this pathway and to establish optimal coordinates in slices to prepare for the electrophysiological recording experiments. Two animals suffice for this purpose and using more would be against the aim of reducing the use of experimental animals as much as possible.

The rationale here for the use of AAV2-CAG-tdTomato as a retrograde tracer is unclear. My understanding is that this is more effective as an anterograde tracer. Some clarification and validation would be important.

The reviewer is correct that AAV2 is generally considered an effective anterograde tracer, but tracing the connectivity of entorhinal cortex with AAVs has been proven to be notoriously difficult, in particular retrograde tracing of inputs to layer II. In a neighboring lab in the centre, headed by Edvard and May-Britt Moser, it was established that AAV2 types show very efficient retrograde transport and that is why we decided to use the virus. Also, in our hands the virus showed excellent retrograde transport that served our purpose

(2) Interpretation of the anterograde experiments in Figure 1D-E would also benefit from showing evidence that the injection sites are restricted to MEC. It should be straightforward to make a supplemental figure showing labelling at all dorsoventral levels.

More careful analysis of the axon labelling in the dentate gyrus could also help make a case for the selectivity of the injection site for eGFP. In this case, only the intermediate portion of the molecular layer of the DG should be labelled. In the image shown, the labelled band is quite wide, but it's hard to tell if this reflects the plane of section or is because it also includes labelling in the outer molecular layer (which would be indicative of LEC expression).

We thank the reviewer for these two suggestions, and we have prepared a new Supplementary Fig. 2 in line with this.

Numbers are also on the low side for these experiments.

See our response above

(3) For optogenetic experiments in Figure 2, the selectivity of targeting of AAV to MEC is assessed through the specificity of labelling in the DG. This is great, but it's important to show that this specificity is maintained at all dorsoventral levels.

Higher resolution images of labelling in LEC could also be helpful. It's hard to tell from the images in 2A if labelling is axonal or is in the soma adjacent to the nuclear NeuN signal (which would indicate a lack of selectivity for MEC).

We thank the reviewer for these two suggestions and provide a new Supplementary Fig. 6, showing both the details of AAV1 being present only in neuropil in MEC not in somata as well as the specific labeling in the middle molecular layer of DG in detail. Including all dorsoventral levels would not provide additional information in view of the very well-established topographical organization of the entorhinal to dentate projection, reaching approximately 20 -25 % of the full long axis of DG (Van Groen et al., 2003)

In addition, we have again carefully screened all tissue from the electrophysiological experiments for possible leakage of virus from MEC to LEC. We decided to exclude recordings from one mouse, which had labelling in MEC that was close to the border with LEC. Neuron counts have therefore been adjusted (pages 7-9) and the example recording showing responses to TTX/4-AP exposure in Figure 2B has been exchanged.

(4) The analysis of excitatory and inhibitory opto-responses in Figure 2 is nice. It may be helpful to report quantification of the rise and decay kinetics of the synaptic currents. They appear much slower for the inhibitory input, which may be functionally important.

This would indeed be nice to add, but it would not significantly impact or change the main message of our study. Since the lab of the senior author (MPW) has been discontinued and the resources for conducting these analyses are not readily available anymore, we have found it difficult to comply with the reviewer’s request

(5) More direct evidence for SST axons projecting from MEC to LEC would strengthen the conclusions made. E.g., in experiments where the SST neurons are labelled, is it possible to follow the axons? Do they project as expected from the MEC to the LEC?

In our view the tracing data provide convincing evidence in support of a direct projection from MEC to LEC by SST neurons, as shown in horizontal brain sections where SST axons labelled in MEC of an SST^Cre mouse projects within Layer I from the site of origin in MEC to Layer I of MEC (Supplementary Figure 3). Similar visualizations were not possible to obtain in our electrophysiological experiments where semicoronal slices were used. This cutting angle has been shown to be optimal to preserve most of the axon and the dendritic tree of LEC neurons (Tahvildari and Alonso, 2005; Canto and Witter 2012), but does not maintain the projection from MEC to LEC.

Minor Points:

(1) "These layers are heavily innervated by medial entorhinal axons (Figure 1F...". I don't see a 1F.

This has been corrected; should have been Figure 1E.

(2) Methods should report series resistance values for patch-clamp experiments (range and mean).

Fully agree and this information has now been added on page 22 of the manuscript:

Under Voltage clamp: ‘Recordings with series resistance ≤ 25 MΩ were accepted, with an average of 16.2 MΩ for voltage clamp recorded neurons (range, 4.9 – 24.9 MΩ).’

Under Current clamp: ‘All recordings (series resistance: 18.9 MΩ, 5.0 – 66.7 MΩ; mean, range) were included for analysis.’

Reviewer #2 (Recommendations for the authors):

(1) Please specify in the figure or, alternatively, in the figure legend which virus was used in each group shown in Figures 2H and 2I. This is somewhat confusing, since Figure 2E illustrates a specific combination of viruses and mouse lines that only corresponds to part of Figure 2H. While this information is provided in the text, including it directly in the figure would help the reader.

We thank the reviewer for this excellent suggestion, and we have implemented this in the new version of figure 2.

(2) In Figure 4, regarding the inputs from PIR, cLEC, and PER to LEC, the inhibitory components recruited by each input were not examined as thoroughly as for the MEC inputs. In fact, some inhibitory interneurons were double-labeled in the GAD67 mice (Figure 4B), which could also influence the responses of LEC neurons, especially for PER inputs. Recordings in Figure 4C appear to have been obtained near the reversal potential for inhibition, which may have prevented the observation of inhibitory effects. The authors could discuss this point in the Results.

The reviewer is correct and this issue is now addressed in the relevant section in the results (page 11):

‘It should be noted, however, that it is possible that inhibitory effects could have been masked in some recordings, due to the resting membrane potential in our recordings being close to the theoretical chloride equilibrium potential. This could be particularly relevant for the inputs from PER, an area where we found LEC-projecting GABAergic neurons (Fig. 4B) and which is known to provide long-distance inhibition to LEC (Pinto et al., 2006; Apergis- Schoute et al., 2007).’

(2) A diagram summarizing the known connections among MEC, LEC, and the hippocampal formation, highlighting the relevant cell types, layers, and the new connections identified in this study, would be a valuable addition, perhaps as a supplementary figure.

We appreciate the suggestion, though find a full summary of known connectivity a bit overdone. Instead, we included a new figure 6 that summarizes the main new findings of the paper in the context of LEC projections to the hippocampal formation.

(3) Although the main focus is on MEC-LEC connectivity, the experiments examining interactions with other cortical areas and converging inputs would benefit from a discussion of how MEC-driven inhibition of LEC might influence those inputs and shape the resulting output to the hippocampus. Including a short paragraph addressing this in the Discussion section would strengthen the manuscript.

Excellent suggestion although we did speculate briefly in the result section on the possible effect. We have added a short paragraph in the discussion (page 15), reiterating the part in the results (page 13, last paragraph of results). We also briefly discussed the potential functional relevance of the suppression of the pathway from layer IIa to DG-CA3/CA2 versus the facilitation of activity in the pathway from layers IIb/III to CA1 and subiculum (last section of the discussion).

(4) Lastly, it would be interesting to know what the main source of activation is for the SST long-range LEC projecting neurons. Are these neurons recruited in a feedback manner by the activity of MEC excitatory cells? I realize this question is beyond the scope of the present study, but if the authors have any data or insights related to this point, including a brief discussion would be valuable.

This is an interesting thought, and we have included a new supplementary figure (supplementary Figure 5) showing data from experiments mapping monosynaptic inputs to MEC SST neurons using rabies virus. Although it was not possible to target only MEC SST neurons that project to LEC, the data show which are the main extrinsic inputs to the population of MEC SST neurons, most likely including those that project to LEC.

eLife Assessment

This important study introduces Hetlearn, a novel learning algorithm that demonstrates that an ensemble of simple sub-learners with varying learning rates can effectively manage inference in complex, unstable environments. While the theoretical framework and its proposed application to parallel memory traces in the insect mushroom body are intriguing, the evidence supporting the core claims is currently incomplete. To fully validate the authors' conclusions, further exploration is needed to rigorously define the boundaries of the model's hyperparameter space, along with a deeper justification and clarification of its biological plausibility.

Reviewer #1 (Public review):

The authors describe a learning algorithm that is meant to deal with the problem of inference in large, complex environments. They argue that simpler but ensemble learning systems with heterogeneous learning rates often perform better than more complex approaches. They also relate the ideas of their model to a circuit implementation in the mushroom body, an associative learning area in insects.

I found the argument about the value of sublearners remaining simple to be thoughtful and intriguing. I also appreciated the connection to biology and, although there remain details to be worked out, it seems that the proposed approach has what I'd call a "biologically plausible" instantiation.

Comments on the major claims:

The paper claims that algorithms that learn stochasticity and volatility "necessarily result in worse short-term performance than Hetlearn." The results with Autocovariance Least Squares and the model of Piray and Daw are consistent with this statement, but the authors seem to be making a more generic claim. Is there a rigorous justification of this? In particular, I found the section "Competing sublearners should stay simple" to straddle a line between opinion and fact, and I wasn't sure where it intended to be regarding that line.

Relatedly, regarding the statement just before that section: "The exponential convergence of Hetlearn weightings stands in contrast to the slow convergence of stochasticity/volatility estimates (Figures 2A and C), which result in poor initial performance of the Kalman learner." Is the claim here that the Kalman learner doesn't converge exponentially, or that it converges more slowly?

The paper would benefit from a comparison to other models of multiple learning systems with different timescales. The classic one would be the complementary learning systems ideas about hippocampus and neocortex (McClelland, McNaughten, O'Reilly 1995), and the many subsequent follow-ups. Two other relevant ones to consider are Roxin & Fusi 2013 and Lindsey & Litwin-Kumar 2024, which also consider multiple memory systems with different plasticity rates.

Comments on clarity:

(1) Page 2: There could be some more unpacking of the relationship between x and z in equations 1a, 1b. If z_t are time-varying, shouldn't theta, if it represents what is learned about "large-world factors," also depend on time?

The description of second-order conditioning on page 6 is confusing. Second-order conditioning tests whether S2 acquires a positive predicted value after pairing with S1, which had previously been paired with reward. The text makes it seem like the goal of second-order conditioning is to learn S2->S1->no reward.

(2) Page 6: "Representations decay on a slower timescale than stimulus presentation. Hence, the representation x2 after experiencing S2 → S1 holds traces of the S2 representation." I couldn't understand this. Maybe an equation would help?

(3) Page 7: The phrase "unconditioned stimulus" is introduced without being described. Is this a reward or punishment? What does it have to do with valence lower-case v, or value upper-case V? The authors seem to mix notations from different subfields, leading to a rather confusing description of the model.

Comments on relationship to biology:

(1) Page 6: It is assumed that Kenyon cells interact recurrently through plastic weights. This is an unconventional assumption for mushroom body models, and it is made without much discussion. The authors cite papers that argue for changes in the calyx during learning (although these effects are generally much weaker than the well-documented plasticity onto MBONs). However, KC-to-KC interactions are largely in the lobes, not the calyx. The authors should provide more discussion of this assumption. What happens if the recurrence is weak or absent? A relevant reference to consider is Manoim et al. Current Biology 2022, which shows that KC-to-KC interactions are inhibitory.

The model seems to imply that each MBON compartment encodes only one memory, or did I misunderstand? Is this necessary? Typically, it is thought that because of the sparse, decorrelated representations in the KCs, an individual MBON could store multiple associations without too much interference.

Reviewer #2 (Public review):

Summary:

The authors propose Hetlearn, a novel learning algorithm for unstable environments: instead of using statistically optimal methods to estimate the variability of the environment, simply have a range of "sub-learners" that learn at different rates, and rely more heavily on the sub-learners with a recent track record of success. This strategy is particularly helpful when the environment has unknown and fluctuating stochasticity (randomness around a constant mean reward) and volatility (the mean itself changes over time). For high stochasticity and low volatility, it's better to learn slowly to smooth out randomness; for low stochasticity and high volatility, it's better to learn quickly to catch onto the new trend. The authors show that existing methods work well when stochasticity and volatility are constant, or when methods can learn them over a long time, but that Hetlearn does better when stochasticity and volatility change over time or an agent has limited time or data to learn from.

They then propose that the fly mushroom body implements a form of Hetlearn, since it has different compartments that form parallel memory traces at different learning and forgetting rates. Here, the conclusions are less clear because their model doesn't appear to implement the key feature of Hetlearn (the differential weighting of sublearners based on recent success), and because their model has features that don't have an obvious biological equivalent in the real mushroom body.

Strengths:

The idea behind Hetlearn is clever and interesting, and it makes sense that a heuristic method like Hetlearn would outperform a theoretically optimal algorithm under conditions of limited data. The model is clearly defined, and they test it across a range of tasks and compare it to a range of different Kalman/particle filter learners. The application to the mushroom body is also an inspiring connection and takes advantage of the discovery of empirically described sublearners. The work will stimulate new ways of understanding how biological systems might implement heuristic tricks that may not be optimal under ideal conditions, but that succeed in "real world" conditions, and it will stimulate new thinking about the computational role of parallel memory traces in the mushroom body.

Weaknesses:

In the tests of Hetlearn vs. Kalman filters, it would be useful to more fully explore the parameter space. Specifically, in Figures 1-2, it would help define the boundaries of when Hetlearn is better or worse than Kalman filters, by systematically changing the parameters of the task (e.g. increasing/decreasing the amount of data available to the learner or the frequency of changing stochasticity/volatility), and changing the parameters of Hetlearn (the learning rates of the sublearners and the recency bias, i.e. how far back to track the recent success of the sublearners when weighting their outputs). For Figure 3, while they do check the performance when varying the recency bias, there are no conditions presented in which the particle filter does better. To define when Hetlearn is better, it is important to show when it is worse.

In the mushroom body model, there are several elements that have no apparent biological equivalent, and it's not clear whether they are incidental (in which case they could be removed to enhance biological realism) or essential to the model's performance (in which case the discrepancy should be discussed; perhaps the model can be reframed as a prediction for as-yet-undiscovered features). In addition, the model seems to lack the defining feature of Hetlearn (up/down-weighting sublearners according to their recent performance). Finally, the authors argue that Hetlearn explains experimental data better than existing models, but existing models could be easily and parsimoniously tweaked to accommodate these data, so the explanatory advantage of Hetlearn is unclear.

eLife Assessment

In this useful study, Millard et al. assessed the effects of nicotine on pain sensitivity and peak alpha frequency (PAF). They propose a solid experimental framework to test the modulatory effects of nicotine on PAF and pain sensitivity, but the evidence is incomplete to support the claims that the chosen experimental intervention may actually play a significant mechanistic role in pain sensitivity given the modest effect sizes observed. The work can be incorporated into the literature investigating the relationship between nicotine and pain and could be of broad interest to pain researchers.

Reviewer #2 (Public review):

Summary:

The study by Millard et al. investigates the effects of nicotine on peak alpha frequency and pain using a highly elaborate experimental design. According to the statistical analysis, the authors found a small covariate-corrected effect for prolonged heat pain and a small effect on global peak alpha frequency in response to nicotine treatment. However, the effect on heat pain was not found for pressure pain, was not mediated by peak alpha frequency, and appears mainly based on a worsening in the placebo condition rather than a clear reduction of pain after nicotine.

Strengths:

I very much like the study design and that the authors followed their research line by aiming to provide a complete picture of the pain-related cortical impact of peak alpha frequency. This is important work, even in the absence of clear statistical or mechanistic support for the main hypothesis. I also appreciate the preregistration of the study, the well-written and balanced introduction, and the additional analyses added during revision.

Weaknesses:

The weakness of the study revolves around two main aspects:

(1) Source separation would still have been more appropriate than electrode regions or global peak alpha frequency to extract the alpha signal. The added ICA analysis is appreciated, but in my view, it does not fully solve the problem. Different alpha sources, such as mu rhythm, occipital alpha, and lateralised alpha activity, are still not clearly disentangled. The main peak alpha frequency effect remains a small global, wide-band, sensor-space effect rather than a clearly source-specific sensorimotor effect.

(2) I still think the choice of nicotine is a major weakness of the study. The rationale for using nicotine as an intervention rests partly on previous reports of nicotine effects on experimental pain, but the most relevant cited meta-analysis already suggested that these effects are small and may be affected by publication bias. It is therefore not a clean way to test whether peak alpha frequency has a causal role in pain. The heat-pain result is also difficult to interpret as analgesia. Statistically, the placebo-controlled contrast may be significant, but in practice, the nicotine condition changed very little, and the effect seems mainly driven by worsening in the placebo group. In a real intervention, one gives the drug, not the difference between drug and placebo.

Impact:

The impact of the study could be to show what did not work to answer the authors' research question. The study is valuable because it provides a careful and largely negative mechanistic test: nicotine produced at most small effects, peak alpha frequency did not mediate pain, and pressure pain was not affected. The study would have more impact with a more direct intervention model and an analysis strategy that more clearly untangles the different alpha sources.

Author response:

The following is the authors’ response to the previous reviews

Public Reviews:

Reviewer #1 (Public Review):

Summary:

In this study, Millard and colleagues investigated if the analgesic effect of nicotine on pain sensitivity, assessed with two pain models, is mediated by Peak Alpha Frequency (PAF) recorded with resting state EEG. The authors found indeed that nicotine (4 mg, gum) reduced pain ratings during phasic heat pain but not cuff pressor algometry compared to placebo conditions. Nicotine also increased PAF (globally). However, mediation analysis revealed that the reduction in pain ratings elicited by the phasic heat pain after taking nicotine was not mediated by the changes in PAF. Also, the authors only partially replicated the correlation between PAF and pain sensitivity at baseline (before nicotine treatment). At the group-level no correlation was found, but an exploratory analysis showed that the negative correlation (lower PAF, higher pain sensitivity) was present in males but not in females. The authors discuss the lack of correlation.

In general, the study is rigorous, methodology is sound and the paper is well-written. Results are compelling and sufficiently discussed.

Strengths:

Strengths of this study are the pre-registration, proper sample size calculation, and data analysis. But also the presence of the analgesic effect of nicotine and the change in PAF.

Weaknesses:

It would even be more convincing if they had manipulated PAF directly.

We thank Reviewer #1 for their positive and constructive comments regarding our study. We appreciate the view that the study was rigorous and methodologically sound, that the paper was well-written, and that the strengths included our pre-registration, sample size calculation, and data analysis.

In response to the reviewer's comment about more directly manipulating Peak Alpha Frequency (PAF), we agree that such an approach could provide a more direct investigation of the role of PAF in pain processing. We chose nicotine to modulate PAF as the literature suggested it was associated with a reliable increase in PAF speed. As mentioned in our Discussion, there are several alternative methods to manipulate PAF, such as non-invasive brain stimulation techniques (NIBS) like transcranial alternating current stimulation (tACS) or neurofeedback training. These approaches could help clarify whether a causal relationship exists between PAF and pain sensitivity. Although methods such as NIBS still require further investigation as there is little evidence for these approaches changing PAF (Millard et al., 2024).

Reviewer #2 (Public Review):

Summary:

The study by Millard et al. investigates the effect of nicotine on alpha peak frequency and pain in a very elaborate experimental design. According to the statistical analysis, the authors found a factor-corrected significant effect for prolonged heat pain but not for alpha peak frequency in response to the nicotine treatment.

Strengths:

I very much like the study design and that the authors followed their research line by aiming to provide a complete picture of the pain-related cortical impact of alpha peak frequency. This is very important work, even in the absence of any statistical significance. I also appreciate the preregistration of the study and the well-written and balanced introduction. However, it is important to give access to the preregistration beforehand.

Comment on latest version:

I thank the authors for their efforts to respond to my previous concerns. I appreciate the additional analyses and the more cautious wording in several places. However, I still think the manuscript would benefit from a more direct interpretation of the findings.

Reviewer #3 (Public Review):

In this manuscript, Millard et al. investigate the effects of nicotine on pain sensitivity and peak alpha frequency (PAF) in resting state EEG. To this end, they ran a pre-registered, randomized, double-blind, placebo-controlled experiment involving 62 healthy adults who received either 4 mg nicotine gum (n=29) or placebo (n=33). Prolonged heat and pressure were used as pain models. Resting state EEG and pain intensity (assessed with a visual analog scale) were measured before and after the intervention. Additionally, several covariates (sex at birth, depression and anxiety symptoms, stress, sleep quality, among others) were recorded. Data was analyzed using ANCOVAequivalent two-wave latent change score models, as well as repeated measures analysis of variance. Results do not show ‘experimentally relevant’ changes of PAF or pain intensity scores for either of the prolonged pain models due to nicotine intake.

The main strengths of the manuscript are its solid conceptual framework and the thorough experimental design. The researchers make a good case in the introduction and discussion for the need to further investigate the association of PAF and pain sensitivity. Furthermore, they proceed to carefully describe every aspect of the experiment in great detail, which is excellent for reproducibility purposes. Finally, they analyse the data from almost every possible angle and provide an extensive report of their results.

The main weakness of the manuscript is the interpretation of these results. Even though some of the differences are statistically significant (e.g., global PAF, pain intensity ratings during heat pain), these differences are far from being experimentally or clinically relevant. The effect sizes observed are not sufficiently large to consider that pain sensitivity was modulated by the nicotine intake, which puts into question all the answers to the research questions posed in the study.

We would like to express our gratitude to Reviewer #3 for their thoughtful and constructive review, including the positive feedback on the strengths of our study's conceptual framework, experimental design, and thorough methodological descriptions.

We acknowledge the concern regarding the experimental and clinical relevance of some statistically significant results (e.g., global PAF and pain intensity during heat pain) and agree that small effect sizes may limit their practical implications. However, our primary goal was to assess whether nicotine-induced changes in PAF mediate pain changes, rather than to demonstrate large direct effects on pain sensitivity. Nicotine was chosen for its known ability to modulate PAF, and our focus was on the mechanistic role of PAF in pain perception. To clarify this, we have revised the discussion to better differentiate between statistical significance, experimental relevance, and clinical applicability. We emphasize that this study represents a preliminary step towards understanding PAF’s mechanistic role in pain, rather than a direct clinical application.

We appreciate the suggestion to refine our interpretation. We have adjusted our language to ensure it aligns with the effect sizes observed and made recommendations for future research, such as testing different nicotine doses, to potentially uncover stronger or more clinically relevant effects.

Although modest, we believe these findings offer valuable insights into the potential mechanisms by which nicotine affects alpha oscillations and pain. We have also discussed how these small effects could become more pronounced in different populations (e.g., chronic pain patients) and over time, offering guidance for future research on PAF modulation and pain sensitivity.

Recommendations for the authors:

Reviewer #2 (Recommendations for the authors):

I thank the authors for their efforts to respond to my concerns. I very much admire the thoughts and effort that the authors have put into this study. This is a great study design, a fantastic research idea and an important path to study the neurophysiology of pain.

I also understand that some of my suggestions are not compatible with the authors' current line of analysing their data. Since the authors did not change the analysis procedure and obviously could not change their experimental design, I would largely keep my public review.

However, acknowledge the different opinions and have a few remarks and suggestions.

(1) In agreement with reviewer 3, I would not consider the effect of nicotine to be meaningful. The random effect mentioned by the authors could have been addressed with a crossover design. In this case, the placebo and intervention could have been directly compared. Interindividual differences in pain perception are at least partially controlled for by analysing the difference between pre and post-gum. The distribution of the pre-post difference separately for placebo and nicotine would be a valuable addition to the manuscript. I still think the minimal effect of nicotine on pain is not meaningful and not interpretable. The relevance of any explanatory variable like stress could be by chance (PMID: 35296861). Reviewer 3 had a valid point (comment 6) and this is something that should be mentioned as clearly as possible: there was no effect of nicotine. For PHP the comparison with the placebo is irrelevant if there is no pre vs. post-effect.

It is fair to say that some issues could have been resolved using a cross-over design, however, the choice of a parallel design was made, in part, due to the desire to mask the presence of a placebo gum. Having a single session per participant allowed us to produce a deception that all participants were receiving nicotine gum, which was later revealed during a debrief. This aspect is far less feasible in a cross-over design. In future, different approaches could be used. And we appreciated the reviewers recognition that this cannot, of course, be changed at this stage.

Regarding the comments of 1) ’I would not consider the effect of nicotine to be meaningful’, 2) the minimal effect of nicotine on pain is not meaningful and not interpretable’, and 3) ’there was no effect of nicotine’, we discern that the latter differs considerably from the first two points. We would like to address this point by first calling into question what the reviewer(s) mean by meaningful, and highlighting that discerning this varies by context. Edenberg (2021) highlights that meaning can be situated within several contexts: statistical, biological (mechanistic), clinical, and public policy. We show the statistical context, and therefore would like to emphasise that we cannot state number 3) ’there was no effect of nicotine’.

Although the complexity of our analysis is not at the same scale, we appreciate the need for thousands of participants for brain-wide associations, as cited (PMID: 35296861 = Marek et al., 2022). The article referenced states that reproducible brain-wide association studies require thousands of individuals, and thus we would like to highlight that our work indicating the potential relevance of sex/stress greatly differs from this. Though it may be by chance, the potential for that chance is 0.05 from a statistical significance perspective. Certainly, no finding should be taken as truth without replication, but that does not mean we should not report our finding of a statistically significant effect of stress on change in PAF in our model.

Then, the question becomes, are we already at the point where the issue of ’how to go beyond statistical significance’ should be addressed? One could argue no, as this is the first study to assess this question of nicotine’s effect on PAF and pain at the same time. But we would like to argue yes, although only to the mechanistic/biological level, because the question of what is meaningful is dependent on the study goals (Edenberg, 2021). We aimed to gain mechanistic insight into the PAF-pain relationship.

We hoped to achieve some biological/mechanistic meaning in the present study, however, as outlined in the discussion, with small effect sizes for nicotine on PAF and nicotine on heat pain, and lack of a mediating effect, we may not have achieved this. Although, if replicated, even small magnitude effects can shape our understanding of relevant mechanisms underlying pain and aid future clinical perspectives (Edenberg, 2021; Ross & Bassett, 2024). Meaningfulness in clinical or public policy contexts should of course be in mind, but were clearly not the focus of this present work.

We have edited the manuscript to demonstrate the fact that our effect size is small.

We corrected the rounding to 2 decimals, and now also refer the reader to the supplementary materials table:

“Change in pain was reduced by a factor of -0.68 for the nicotine group compared to the placebo group when controlling for confounding variables (Figure 3). See Supplementary Material 3.2, Table 5, for full model output.”

We edited the abstract and the first paragraph of the discussion to make clear to the reader that the effect sizes were small. In our desire to keep the text clear and readable, we did not intend to overstretch our claims, and apologise if the manuscript was unintentionally portraying this overstretch. These are very important sections of the manuscript in which to mention such nuances, as these are the parts viewed most when readers do not wish to read the entire manuscript.

Abstract

“The nicotine group showed a small decrease in heat-pain ratings compared to placebo group when controlling confounders, and a small increase in PAF across the scalp from pre- to post-gum, both with and without confounder adjustment. These effects were most pronounced in the central-parietal and right-frontal electrodes.”

Discussion first paragraph

“Compared to placebo, our data demonstrate three key findings: 1) nicotine increased PAF speed; 2) nicotine reduced prolonged heat pain intensity but only when controlling for confounding and not for the prolonged pressure pain model, and 3) decreases in prolonged heat pain intensity were not mediated by changes in PAF. This suggests that changes in heat pain due to nicotine occur through mechanisms unrelated to change in PAF and require replication as the effects required control for confounding and the reduction was small in magnitude.”

Discussion section on effect of nicotine on PAF:

“In line with previous literature in non-smokers [38,47,48], we contribute additional evidence that chewing 4 mg of nicotine gum produces a statistically significant increase in PAF speed in non-smoking, nicotine-gum-naïve, pain-free, adult participants. An exploratory cluster-based permutation analysis indicated that the change in wide-window PAF (8–12 Hz) produced by nicotine, was most pronounced in a cluster of electrodes in the central-parietal region and a separate cluster of electrodes in the right-frontal region, rather than in the pre-registered sensorimotor ROI (i.e., Cz, C1, C2, C3, C4).”

Discussion section on the effect of nicotine on pain:

“While acknowledging the modest effect size, it’s essential to consider the context of our study’s focus. Assessing the clinical relevance of pain reduction is pertinent in applications involving the use of any intervention for pain management [71]. However, from a mechanistic standpoint, particularly in understanding the implications of and relation to PAF, the specific magnitude of the pain effect becomes less pivotal, as small effects can still have mechanistic or biological meaning without establishing clinical meaning [72]. Nevertheless, future research should examine whether effects on pain increase in magnitude with different nicotine administration regimens (i.e. dose and frequency).” 

Discussion section on relationship between PAF and pain:

“However, as this is the first study attempting to directly manipulate PAF, observing only small effects on pain, we cannot confidently state that a causal relationship between PAF and pain sensitivity does not exist, and future research should explore these relationships with larger sample sizes, larger doses of nicotine, and alternative PAF modulators.”

Discussion final paragraph:

“We have shown that, compared to placebo, nicotine gum produced statistically significant increases global PAF speed and decreases pain ratings during prolonged heat pain. However, the effects of nicotine on heat pain were not mediated by changes in PAF. Therefore, we find no evidence that PAF is causally related to pain. The implication of this is that changing PAF may not be a useful target for pain modulation, because pain sensitivity may not be dependent on state changes in PAF. However, this is the first study to test modulation of PAF as a mechanism for reducing pain intensity. Moreover, while effects on PAF appear small but robust, effects on heat pain required control for confounding to be observed. More randomised experiments on the effects of nicotine that use larger sample sizes, higher nicotine doses, and pharmacokinetic tracking, whilst also reducing mediator measurement error are needed to confirm the present findings and uncover whether these factors account for the lack of mediation effect seen here.”

(2) I still think the authors made a mistake in using nicotine. Their new wording did not convince me, and I doubt that any reader would buy the "mediation by design" phrase.

We addressed the reviewers previous comment (comment 1) on nicotine being a ‘mistake’, and no longer suggest there is a “large body of evidence suggests that nicotine is an ideal choice for manipulating PAF”. We have been clearer about our intention to assess mediation-by-design, with the manipulation of PAF being out primary aim. For example, this edit in the discussion:

“The choice of nicotine was driven by its potential to change PAF, but also, short-term nicotine use is thought to have acute analgesic properties in experimental settings, with a review reporting that nicotine increased pain thresholds and pain tolerance [51].”

In addition, we discussed the ’direct’ manipulation of PAF using non-invasive brain stimulation methods, and have now added further future research directions using methods other than nicotine or NIBS:

“Furthermore, there may have been other mediators that suppress the mediating effects of PAF within our model [66,82,83]. This is plausible, as nicotine is thought to act on pain through multiple pathways [52,54,84], and more direct PAF modulation could more definitively evaluate whether PAF is mechanistically linked to pain sensitivity. Future interventions to modulate PAF could use non-invasive brain stimulation (NIBS), such as transcranial alternating current stimulation (tACS) or repetitive transcranial magnetic stimulation (rTMS), to influence neuronal firing and thereby directly target the brain mechanisms theorised to generate PAF [85–87]. This approach has since been investigated following the initial preprint of

the present manuscript [88,89]. In addition, other approaches to modulating approaches could be considered, such as exercise [32–34], visual stimulation [35,36], cannabis [90,91], and neurofeedback [92,93], while considering their viability in terms of blinding, tolerability, and scalability.”

(3) I acknowledge the work of the authors on SNR, the frequency spectrum looks smooth enough to detect peaks. However, the problem of different alpha sources is not solved. This can be seen in the frequency spectrum, where some participants show two peaks. This is not the first time I have suggested this to the authors; the idea is not new. The fMRI analogue would be to average all GM voxels; instead of global alpha it would be "global brain activity". Some suggestions for a future approach that the authors might consider:

Run a group ICA and select topographies from there. This should simplify the (potentially arbitrary) selection process.

Consider filtering the data before running the ICA, at least >20 Hz to exclude muscle artefacts.

We respectfully note that the reviewer’s comment appears to overlook the substantial revisions we have already made in direct response to this issue. Specifically, we implemented ICA in the revised manuscript, using an automated, objective pipeline to identify components with a clear alpha peak and a topography aligned with a predefined sensorimotor template. This was explicitly done to address concerns about overlapping alpha sources and improve anatomical specificity.

Contrary to the reviewer’s implication, we did not rely solely on global analyses in the original or revised manuscript, as we also included pre-defined ROIs and data-driven ROIs from cluster-based permutation analysis. The additional ICA-based analyses—included in the first revision—produced results that were consistent with the original sensor-space ROI findings, supporting the robustness of the PAF–pain mediation effect regardless of the method used to isolate sensorimotor alpha.

We agree that group ICA could be a valuable complementary approach. However, it is not without limitations, particularly in EEG where inter-individual variability in source topographies is high. Our choice to perform ICA at the individual level and apply an automated selection criterion based on spectral and spatial features was deliberate, data-driven, and avoids the subjectivity involved in manual selection or group-level back-projection.

We have added a discussion of this point and fully acknowledge that future work may benefit from comparing multiple alpha sources (e.g., mu vs. occipital) more explicitly. However, we must emphasise that this is not a missing analysis—it is already included in the revised manuscript. In this second revision, we have added an additional reference to this supplementary analysis within the section previously titled “Exploratory cluster-based permutation anlaysis”, now titled “Exploratory data-driven analysis of alpha”, in case the previous reference to it was in a sub-optimal location:

“Lastly, use of in-house code developed to automatically extract a sensorimotor alpha component using independent component analysis (ICA) showed similar results to the sensorimotor ROI mediation analysis (Supplementary Material 3.11). This supports the robustness of the PAF-pain effect regardless of the method used to isolate sensorimotor alpha.”

We strongly disagree with the suggestion to apply a low-pass filter below 20 Hz prior to ICA. This would remove high-frequency content, including muscle activity—the very signals ICA is designed to isolate and separate from neural activity.

By removing muscle-related frequencies before ICA, the reviewer’s proposed approach would prevent ICA from identifying muscle components in the data. This is methodologically flawed. as ICA works best when it has access to the full spectral range of the signal, allowing it to separate statistically independent sources— including muscle, eye movements, and neural oscillations—based on their spatial and temporal structure (Onton et al., 2006). Thus the desired sensorimotor alpha component would be more distinct if the full spectral range is included. Low-pass filtering the data before ICA designed to identify alpha would severely compromise artifact removal, degrade component separation, and reduce the effectiveness of our preprocessing pipeline.

References for responses to reviewer 2

Edenberg HJ. Perspective on beyond statistical significance: Finding meaningful effects. Complex Psychiatry 2021;7:1–8. https://doi.org/10.1159/000517237.

Marek S, Tervo-Clemmens B, Calabro FJ, Montez DF, Kay BP, Hatoum AS, Donohue MR, Foran W, Miller RL, Hendrickson TJ, Malone SM. Reproducible brain-wide association studies require thousands of individuals. Nature. 2022 Mar 24;603(7902):654-60.

Ross LN, Bassett DS. Causation in neuroscience: keeping mechanism meaningful. Nature Reviews Neuroscience. 2024 Feb;25(2):81-90.

Reviewer #3 (Recommendations for the authors):

I would like to thank the authors for the time and dedication that they clearly put into addressing the reviewer's comments. As researchers, we alternate between both sides (as authors and reviewers) and we are all privy of how difficult these tasks can be.

For me as a reviewer, this is one of the tough times. I wanted to support this manuscript because it is clear that conducting the study had to be a monumental effort, and there were early indications that it was rigorously carried out. Specifically referring to rigor, I value preregistration as a tool to assess the strength of the hypothesis posed before conducting the study, and the severity with which the claims are tested. During my first review, I tried to access the preregistration and even provided my email address as a sign of transparency, but access was not granted. During my second review, the main file in the submission system contained two versions of the same manuscript (the first one corresponding to the old version with the wrong preregistration link). I was not initially aware of this and I apologize for the misunderstanding.

With respect to the rest of my observations, I see that the authors made concessions on small and less relevant issues (e.g. comments #1, #2, #3), but did not satisfactorily address the main ones (#4, #5, #6, #7, #8 and #9). Addressing those comments (which are in line with the issues noted by other reviewers), would probably have lead to a different interpretation of the results compared with what they state in the first paragraph of the discussion.

The main claims (abstract and first paragraph of the discussion) are " 1) nicotine increased PAF speed; 2) nicotine reduced prolonged heat pain intensity but not prolonged pressure pain intensity compared to placebo gum". Just by reading and contrasting the claims with the results, my assessment is that the strength of evidence is inadequate.

I was now able to review the analysis plan, which did not contain an estimation of the effect sizes (only effect directions) and did not have a proper sample size estimation (comment #4) and the main outcome was not, to my understanding, based in terms of the beta coefficients (as you replied to reviewer #1). I also do not think that the possibility of no effect or a false positive (comment #5) is fairly weighed in relation to these main claims in the abstract an first paragraph of the discussion.

I also do not consider the response to comment #6 as satisfactory, first because it is a mistake to consider that we (as reviewers) only interpret the 'mean results'. As we have detailed access to the data, we interpret these results in terms of signal-to-noise ratio, i.e., how large is the effect (signal) compared with the intra and interindividual variance (noise), and it should be clear for anyone working on this fields (pain and EEG) that not only the main effect is not experimentally relevant to support the claims (comments #6 and #7), but in some cases it is likely to have arisen from the unjustified inclusion of covariates (comment #8 and #9). I only raise the final strength of evidence in my assessment from 'inadequate' to 'incomplete', because of the additions to the discussion.

As a final thought, I would have been more than happy to support and recommend the reading of a manuscript that described a carefully designed and preregistered study, but in which the hypothesis were not corroborated by the data. I would have even marked the strength of evidence as compelling. Unfortunately, the preregistered hypothesis cannot be severely tested (at least not in terms of a frequentist framework) because the effects sizes were not predefined and the required sample size was not estimated, and what I see from the manuscript is that there is an effort to maintain claims that are not properly supported by the data and the final analysis. I recognized that I myself can also be in the wrong, so it will be left for eLife readers to make up their own minds.

We respectfully disagree with the assertion that our preregistered hypotheses "cannot be severely tested" due to the absence of predefined effect sizes and sample size estimation. First, the primary purpose of preregistration is to increase transparency and reduce analytical flexibility—not necessarily to formalize power calculations, especially when reliable effect size estimates are unavailable, as is the case in emerging areas of research such as this one (Nosek et al., 2018). Predefining effect sizes based on speculative or contextually irrelevant prior studies would have introduced unjustified assumptions and potentially distorted interpretation. In this case, we made the scientifically responsible choice to avoid anchoring our design on uncertain estimates. 

Second, our sample size is comparable to or larger than those used in prior published studies addressing similar questions, and our analytic pipeline followed the preregistered plan. The reviewer suggests that we are attempting to maintain unsupported claims; however, our discussion is careful to reflect the limitations of the findings, including their statistical uncertainty, and we do not overstate conclusions. Where effects were weak or absent, we reported this transparently and interpreted them cautiously.

Finally, while formal power calculations are useful under certain conditions, they are not a prerequisite for a study to be considered a "severe test" of a hypothesis—especially when the statistical approach is preregistered, data are handled transparently, and null results are acknowledged rather than hidden. The sample size was informed by resource and feasibility constraints (Lakens, 2022) and aligns with or exceeds that of comparable studies in the field (Bowers et al., 2015). We have now made this rationale explicit in the manuscript.

“The sample size was informed by resource and feasibility constraints [98] and aligns with or exceeds that of comparable studies in the field [38], covering 60 participants in total, with two extra in case of incomplete data identified during later data analysis.”

We therefore maintain that the study is a valid and informative contribution, regardless of whether the observed results confirm or disconfirm the hypotheses.

Nonetheless, below we have revisited previous comments (#4, #5, #6, #7, #8 and #9) that reviewer 3 stated were not satisfactorily addressed.

Previous comment 4) Availability of the pre-registration

We consider this point now addressed, as access to the OSF pre-registration was resolved. Moreover, we can assure the reviewer that their identity was not revealed, as the request for access was not received/seen.

Previous comment 5) Magnitude of pain change – possibility of a type 1 error.

Previous comment 5) To be perfectly clear, I trust the results of this study more than some of the cited studies regarding nicotine and pain because it was preregistered, the sample size is considerably larger, and it seems carefully controlled. I just do not agree with the interpretation of the results, stated in the first paragraph of the Discussion. Quoting J. Cohen, "The primary product of a research inquiry is one or more measures of effect size, not P values" (Cohen, 1990). As I am sure the authors are aware of, even tiny differences between conditions, treatments or groups will eventually be statistically significant given arbitrarily large sample sizes. What really matters then is the magnitude of these differences. In general, the authors hypothesize on why there were no differences on the pressure pain model, and why decreases in heat pain were not mediated by PAF, but do not seem to consider the possibility that the intervention just did not cause the intended effect on the nociceptive system, which would be a much more straightforward explanations for all observations.

Our previous response included the fact that N=62 is not an arbitrarily large sample size and our consideration of the possibility of a false positive. In addition, we agree that conclusions should not be made based on p-values alone. Therefore, we have added more careful descriptions to highlight the nuances of our findings to the reader.

We edited the abstract and the first paragraph of the discussion to make clear to the reader that the effect sizes were small. In our desire to keep the text clear and readable, we did not intend to overstretch our claims, and apologise if the manuscript was unintentionally portraying this overstretch. These are very important sections of the manuscript in which to mention such nuances, as these are the parts viewed most when readers do not wish to read the entire manuscript.

Abstract

“The nicotine group showed a small decrease in heat-pain ratings compared to placebo group when controlling confounders, and a small increase in PAF across the scalp from pre- to post-gum, both with and without confounder adjustment. These effects were most pronounced in the central-parietal and right-frontal electrodes.”

Discussion first paragraph

“Compared to placebo, our data demonstrate three key findings: 1) nicotine increased PAF speed; 2) nicotine reduced prolonged heat pain intensity but only when controlling for confounding and not for the prolonged pressure pain model, and 3) decreases in prolonged heat pain intensity were not mediated by changes in PAF. This suggests that changes in heat pain due to nicotine occur through mechanisms unrelated to change in PAF and require replication as the effects required control for confounding and the reduction was small in magnitude.”

Discussion section on effect of nicotine on PAF:

“In line with previous literature in non-smokers [38,47,48], we contribute additional evidence that chewing 4 mg of nicotine gum produces a statistically significant increase in PAF speed in non-smoking, nicotine-gum-naïve, pain-free, adult participants. An exploratory cluster-based permutation analysis indicated that the change in wide-window PAF (8–12 Hz) produced by nicotine, was most pronounced in a cluster of electrodes in the central-parietal region and a separate cluster of electrodes in the right-frontal region, rather than in the pre-registered sensorimotor ROI (i.e., Cz, C1, C2, C3, C4).”

Discussion section on the effect of nicotine on pain:

“While acknowledging the modest effect size, it’s essential to consider the context of our study’s focus. Assessing the clinical relevance of pain reduction is pertinent in applications involving the use of any intervention for pain management [71]. However, from a mechanistic standpoint, particularly in understanding the implications of and relation to PAF, the specific magnitude of the pain effect becomes less pivotal, as small effects can still have mechanistic or biological meaning without establishing clinical meaning [72]. Nevertheless, future research should examine whether effects on pain increase in magnitude with different nicotine administration regimens (i.e. dose and frequency).”

Discussion section on relationship between PAF and pain:

“However, as this is the first study attempting to directly manipulate PAF, observing only small effects on pain, we cannot confidently state that a causal relationship between PAF and pain sensitivity does not exist, and future research should explore these relationships with larger sample sizes, larger doses of nicotine, and alternative PAF modulators.”

Discussion final paragraph:

“We have shown that, compared to placebo, nicotine gum produced statistically significant increases global PAF speed and decreases pain ratings during prolonged heat pain. However, the effects of nicotine on heat pain were not mediated by changes in PAF. Therefore, we find no evidence that PAF is causally related to pain. The implication of this is that changing PAF may not be a useful target for pain modulation, because pain sensitivity may not be dependent on state changes in PAF. However, this is the first study to test modulation of PAF as a mechanism for reducing pain intensity. Moreover, while effects on PAF appear small but robust, effects on heat pain required control for confounding to be observed. More randomised experiments on the effects of nicotine that use larger sample sizes, higher nicotine doses, and pharmacokinetic tracking, whilst also reducing mediator measurement error are needed to confirm the present findings and uncover whether these factors account for the lack of mediation effect seen here.”

Previous comment 6) Magnitude of pain change

Previous comment (6) In this regard, I do not believe that an average *increase* of 0.05 / 10 (Nicotine post pre) can be considered a "reduction of pain ratings", regardless of the contrast with placebo (average increase of 0.24 / 10). This tiny effect size is more relevant in the context of the considerable inter-individual variation, in which subjects scored the same heat pain model anywhere from 1 to 10, and the same pressure pain model anywhere from 1 to 8.5. In this regard, the minimum clinically or experimentally important differences (MID) in pain ratings varies from study to study and across painful conditions but is rarely below 1 / 10 in a VAS or NRS scale, see f. ex. (Olsen et al., 2017). It is not my intention to question whether nicotine can function as an acute analgesic in general (as stated in the Discussion), but instead, if it worked as such under these very specific experimental conditions. I also acknowledge that the authors note this issue in two lines in the Discussion, but I believe that this is not weighed properly.

Our previous response included discussion of interpreting mean values, a correction to a table that showed the ”increase” erroneously displayed previously due to list-wise deletion in the analysis. We have further attempted to weigh this issue more thoroughly and to always highlight the nuances of our results, as seen in our response to your previous comment 5 above. In further consideration of the effect size, note that the bootstrapped 95% CI for the effect of gum on change in pain was [-1.28, -0.16], which indicates that the overall difference falls within this range when controlling for other factors in the model. Of course this means the difference may be as small as -0.16, but also may be as large as -1.28. Such an effect might have be considered clinically relevant. Replication of the results is therefore warranted.

Also, as outlined in our response to reviewer 2 comment 1, our intention was not to establish a clinical utility at this stage. We hoped to achieve some biological/mechanistic meaning in the present study, and if our present findings are replicated in future, even these small-magnitude effects can shape our understanding of relevant mechanisms underlying pain and aid the direction of future clinical perspectives (Edenberg, 2021; Ross & Bassett, 2024). Meaningfulness in clinical (e.g., MID) or public policy contexts should of course be in mind, but were not the focus of this present work.

Several additional changes were made to the manuscript to emphasise these points to the reader, which are also outlined in the second round of response to your first comment 5 above, as both this comment 6 and 5 focus on magnitude of pain change. We hope this point is now considered to be weighed properly.

Previous comment 7) Magnitude of PAF change

Previous comment (7) In line with the topic of effect sizes, average effect sizes for PAF in the study cited in the manuscript range from around 1 Hz (Boord et al., 2008; Wydenkeller et al., 2009; Lim et al., 2016), to 2 Hz (Foulds et al., 1994), compared with changes of 0.06 Hz (Nicotine post - pre) or -0.01 Hz (Placebo post - pre). MIDs are not so clearly established for peak frequencies in EEG bands, but they should be certainly larger than some fractions of a Hertz (which is considerably below the reliability of the measurement).

In our first response to this comment, we acknowledged this difference in magnitude, agreed that MIDs for PAF are not established, discussed the potential impact of bin size, and highlighted this issue in the revised manuscript text. Although, note that we have now slightly reduced the emphasis on the bin size:

“The ability to detect changes in PAF could be considerably impacted by the frequency resolution used during Fourier Transformations, an element that is overlooked in recent methodological studies on PAF calculation [16,95].”

In addition, we would now like to highlight some more details regarding the prior studies.

We aimed to determine whether nicotine gum could increase PAF in healthy, pain-free, non-smokers. In line with previous literature in non-smokers (Foulds et al., 1994; Harkrider and Champlin, 2001; Bowers et al., 2015), we contribute additional evidence that chewing 4 mg of nicotine gum produces small increases in PAF speed in non-smoking, nicotine-gum-naïve, pain-free, adult participants. The other three papers mentioned by the reviewer are not cited in our manuscript and compare healthy individuals to chronic pain patients (Boord et al., 2008; Wydenkeller et al., 2009; Lim et al., 2016), and are thus not relevant to this discussion on the effect of nicotine on PAF.

A cluster-based permutation analysis indicated that the change in wide window PAF (8-12 Hz) produced by nicotine, was most pronounced in a cluster of electrodes in the central-parietal region and a separate cluster of electrodes in the right-frontal region, rather than in the pre-registered sensorimotor ROI (i.e., Cz, C1, C2, C3, C4). The mediation analysis results showed minimal differences when these clusters of electrodes were used compared to global results (global: b = 0.085, p < .018), except for the expected stronger effect of nicotine on change in PAF alongside greater confidence in this effect (bs = 0.11-0.14, ps < .003). See Supplementary Material 3.8-3.10.

Previous work examining nicotine-induced changes in PAF in healthy non-smokers have used small samples (i.e. <= 20) with nicotine injections or patches (Foulds et al., 1994; Harkrider and Champlin, 2001), while a later investigation used 62 male participants and nicotine gum (Bowers et al., 2015). Therefore, the present study is the largest study to date on nicotine and PAF including non-smoking male and female participants. Bowers didn’t see effects as large as 1 or 2 Hz (approx. 10 or 20% increases) seen in studies with fewer participants, such as n=4 (Foulds et al., 1994) and n=20 (Harkrider & Champlin, 2001), and the magnitude and location of effect depended on the COMT (Bowers et al., 2015).

Bowers et al (2015) showed that the Met allele was related to nicotine-induced increases in PAF, whereas Val/Val homozygotes did not demonstrate PAF changes. In addition, the distribution of PAF increases varied depending on whether Met allele carriers were heterozygotes (i.e. Val/Met: frontal, central, and occipital electrodes) or homozygotes (i.e. Met/Met: parietal electrode). The largest difference between placebo and nicotine gum was 0.51 Hz (a 5.8% increase) at the Fz electrode for the Val/Met group and the smallest significant difference was 0.34 Hz (a 3.5% increase) at the Pz electrode for the Met/Met group.

This study from Bowers used 6mg of nicotine gum, whereas we used 4mg, which may contribute to the lower effect size seen in our study. Dose-dependent effects have not been assessed in non-smokers, but given the dose-dependent changes seen in smokers who abstained from cigarettes prior to EEG recording (Pickworth et al., 1989; Pickworth et al., 1988; Pickworth et al., 1986), the smaller effect sizes seen in the present study may be in line with Bowers study.

Though genetic analysis was not included in the present work, the use of a lower nicotine dose, inclusion of male and female participants, use of more electrodes (64 rather than 8), and unmeasured genetic variations in PAF’s response to nicotine could explain the smaller effect sizes compared to (Bowers et al., 2015).

We have written a condensed summary of this to include in the manuscript discussion:

”Research on nicotine-induced changes in PAF in healthy non-smokers has largely relied on small samples (≤20) using injections or patches [47,48], with Bowers and colleagues [38] providing the only larger study (n= 62 males) using 6 mg nicotine gum. Their results showed modest PAF increases (~0.34–0.51 Hz; 3.5– 5.8%) compared to the larger effects (1–2 Hz; ~10–20%) reported in earlier small-sample studies, with magnitude and scalp distribution influenced by COMT genotype: Met allele carriers exhibited nicotineinduced increases (Val/Met: frontal, central, occipital; Met/Met: parietal), while Val/Val homozygotes showed no change. The present study now the largest to include both male and female non-smokers found smaller effects, likely due to the lower nicotine dose (4 mg), consistent with dose-dependent PAF modulation reported in abstinent smokers [69]. Broader EEG coverage (64 vs. 8 electrodes), sex inclusion, and unmeasured genetic variation may also account for differences between the present study and Bowers and colleagues [38]. Interestingly, beyond nicotine’s main effect on PAF, our 2W-LCS mediation model indicated a significant influence of sex, with females showing greater PAF increases than males. Given that female participants were significantly lighter than males (Supplementary Material 3.4) and the model did not test the interaction between sex at birth and gum group, these finding should be interpreted cautiously and warrant further investigation.”

Previous comment 8) removing confounders calls to question robustness of the findings. Simmons paper

Previous comment (8) The authors also ran alternative statistical models to analyze the data and did not find consistent results in terms of PHP ratings (PAF modulation was still statistically significantly different). The authors attribute this to the necessity of controlling for covariates. Now, considering the effects sizes, aren't these statistically significant differences just artifacts stemming from the inclusion of too many covariates (Simmons et al., 2011)? How much influence should be attributable to depression and anxiety symptoms, stress, sleep quality and past pain, considering that these are healthy volunteers? Should these contrasting differences call the authors to question the robustness of the findings (i.e., whether the same data subjected to different analysis provides the same results), particularly when the results do not align with the preregistered hypothesis (PAF modulation should occur on sensorimotor ROIs)?

In addition to our previous response, we would like to add the following: Although we were previously unaware of the author recommendations from Simmons et al (2011) during initial preparation of this manuscript, we find we cover all points and have added a few improvements to ensure our adherence to this guideline is clear.

We cover all six recommendations for authors suggested in Simmons et al (2011):

(1) We decided to collect 62 participants prior to commencing data collection, this covered 60 participants in total, with two extra in case of incomplete data identified during data analysis.

(2) We had more than 20 participants per group. We have now outlined this decision in the methods section:

“The sample size was informed by resource and feasibility constraints [98] and aligns with or exceeds that of comparable studies in the field [38], covering 60 participants in total, with two extra in case of incomplete data identified during later data analysis.”

(3) We provide detailed methods, which outlines all the variables collected.

(4) We report all experimental conditions, and had no failed manipulations to report. We have now slightly adjusted the wording of our experimental protocol within the methods section to make this clear:

“Participants were randomly assigned to one of only two conditions, thus after the second resting-state EEG, either nicotine or placebo gum was administered with the chew procedure. Following completion of the chew procedure, the third resting state, the second pain assessments, and the fouth resting state were conducted.”

Regarding recommendation (5), listwise deletion was used, as already stated in the manuscript (see Methods, Statistical analysis, Mediation analysis, Assumptions), to exclude participants for whom only one timepoint was available in either the pain or PAF measures, and thus it is not possible to conduct analysis on participants with this missing data. Otherwise, no participants were removed for other reasons. 6) As we conducted analyses using pre-registered covariates determined based on a DAG, we repeated analyses without including these covariates in the form of RM-ANOVAs. The effect on PAF remains, however, as Simmons et al (2011) suggests, the fact we no longer observed a significant effect of gum on heat pain ratings may indicate that the finding is reliant on the presence of a covariate, which does not necessarily mean that the finding is not relevant. However, as reviewer 3 suggests, this should also cause us to question the robustness of the findings and the possibility of type 1 error. Therefore, we have adjusted text in the discussion as follows:

“This underscores the necessity of controlling for confounding variables, as nicotine may only produce pain reduction for those with higher stress, and calls for further investigation into the robustness of the effect of nicotine on heat pain ratings.”

Lastly, regarding the influence that should be attributable to our confounding health-related measures, given the healthy population, we still observe variation in several of these confounders. ’Healthy’ populations still score across a range on these scales, with cut-offs acting as suggestions for problematic symptomology. Assumptions testing confirmed the normality of these covariates, and lack of collinearity so that they could be included in our analyses. We have added a sentence to the Sample Characteristics in Results to outline the ranges reported for the confounding variables:

“Depressive symptoms ranged from 0-4 (out of a maximum of 6), anxiety from 0-6 (out of a maximum of 6), perceived stress from 2-18 (out of a maximum of 40), and sleep quality from 2-10 (out of a maximum of 10; i.e. “excellent sleep quality”).”

Previous comment 9) Exploratory sex analysis?

(9) Beyond that, I believe in some cases that the authors overreach in an attempt to provide explanations for their results. While I agree that sex might be a relevant covariate, I cannot say whether the authors are confirming a pre-registered hypothesis regarding the gender-specific correlation of PAF and pain, or if this is just a post hoc subgroup analysis. Given the large number of analyses performed (considering the main document and the supplementary files), caution should be exercised on the selective interpretation of those that align with the researchers' hypotheses.

To reiterate our previous response to this comment, we stated that sex was an exploratory analysis in the results and was chosen based on other PAF-pain literature, and had also adjusted part of the discussion to align with this. However, we have now seen the first paragraph of the discussion was not adjusted. Therefore, we hope the below edit has now adequately address the previous reviewer 3 comment 9:

“In addition, when assessing the whole sample, we found inconclusive evidence for 4) slower PAF speed at baseline being associated with higher pain ratings for both the heat and pressure pain models. However, during exploratory analysis we found moderate evidence that slower PAF speed at baseline is associated with higher heat pain ratings at baseline in males but not females. In contrast PAF was not associated with pressure pain ratings for males or females.”

References for response to reviewer 3

Boord P, Siddall PJ, Tran Y, Herbert D, Middleton J, Craig A. Electroencephalographic slowing and reduced reactivity in neuropathic pain following spinal cord injury. Spinal cord. 2008 Feb;46(2):118-23.

Bowers H, Smith D, De La Salle S, Choueiry J, Impey D, Philippe T, et al. COMT polymorphism modulates the resting-state EEG alpha oscillatory response to acute nicotine in male non-smokers. Genes, Brain and Behavior 2015;14:466–76.

Edenberg HJ. Perspective on beyond statistical significance: Finding meaningful effects. Complex Psychiatry 2021;7:1–8. https://doi.org/10.1159/000517237.

Foulds J, McSorley K, Sneddon J, Feyerabend C, Jarvis MJ, Russell MA. Effect of subcutaneous nicotine injections on EEG alpha frequency in non-smokers: A placebo-controlled pilot study. Psychopharmacology 1994;115:163–6.

Harkrider AW, Champlin CA. Acute effect of nicotine on non-smokers: III. LLRs and EEGs. Hearing Research 2001;160:99–110.

Lakens D. Sample size justification. Collabra: psychology. 2022 Mar 22;8(1):33267.

Lim M, Kim JS, Kim DJ, Chung CK. Increased low-and high-frequency oscillatory activity in the prefrontal cortex of fibromyalgia patients. Frontiers in human neuroscience. 2016 Mar 14;10:111.

Nosek BA, Ebersole CR, DeHaven AC, Mellor DT. The preregistration revolution. Proceedings of the National Academy of Sciences. 2018 Mar 13;115(11):2600-6.

Pickworth WB, Herning RI, Henningfield JE. Electroencephalographic effects of nicotine chewing gum in humans. Pharmacology Biochemistry and Behavior 1986;25:879–82.

Pickworth WB, Herning RI, Henningfield JE. Mecamylamine reduces some EEG effects of nicotine chewing gum in humans. Pharmacology, Biochemistry, and Behavior 1988;30:149–53.

Pickworth WB, Herning RI, Henningfield JE. Spontaneous EEG changes during tobacco abstinence and nicotine substitution in human volunteers. Journal of Pharmacology and Experimental Therapeutics 1989;251:976–82.

Ross LN, Bassett DS. Causation in neuroscience: keeping mechanism meaningful. Nature Reviews Neuroscience. 2024 Feb;25(2):81-90.

Simmons JP, Nelson LD, Simonsohn U. False-positive psychology: Undisclosed flexibility in data collection and analysis allows presenting anything as significant. Psychological science. 2011 Nov;22(11):1359-66.

Wydenkeller S, Maurizio S, Dietz V, Halder P. Neuropathic pain in spinal cord injury: significance of clinical and electrophysiological measures. European Journal of Neuroscience. 2009 Jul;30(1):91-9.

eLife Assessment

The identification of a pleiotropic EPAS1 enhancer that influences adipocyte responses to hypoxia and thermogenic stimulation provides a valuable contribution to our understanding of high-altitude adaptation in Tibetans. The data are solid, although additional experiments would strengthen the link between ENH5 activity and the mechanisms underlying high-altitude adaptation.

Reviewer #1 (Public review):

In the article, the authors set out to characterize in adipocytes an enhancer, ENH5, of the gene EPAS1, a gene that was found to show strong selection in Tibetan populations. They investigate whether this enhancer contributes to adipocyte response to environmental stress. The authors show that ENH5 is active in preadipocytes and that the Tibetan high-altitude allele confers reduced activity. They then use a mouse ENH5 knockout model to show a hypoxia/thermogenesis responsive phenotype of stronger transcriptional downregulation of aerobic respiration, electron transport chain, and adipogenesis pathways. The authors interpret these findings as evidence that ENH5 conditionally regulates adipocyte energetics and thermogenic response, potentially favoring energy conservation in Tibetans exposed to the demands of high-altitude hypoxia and cold. Overall, the paper presents an interesting potential connection between EPAS1-mediated high-altitude tolerance and energy metabolism; however, more work needs to be done to establish this connection.

Major comments:

(1) The authors use mouse ENH5 enhancer knockout (ENH5-KO) as the model of the Tibetan EPAS1 locus because the high-altitude allele of human ENH5 has lower transcriptional activity than the low-altitude allele (Figure 1A) and mouse ENH5 (musENH5) has enhancer activity (Figure 1D) in mouse preadipocytes. However, it is an overstatement to claim the functional role of Tibetan ENH5 haplotype only based on these data because musENH5 is neither identical to human ENH5 nor the murine high-altitude haplotype. The title should also be revised to better reflect the function of ENH5, like "An EPAS1 enhancer mediates hypoxic and cold response in mouse adipocytes". The authors should consider in some way to actually show that the Tibetan haplotype in ENH5-KO leads to expression changes. This could be done by inserting the haplotype into preadipocytes via CRISPR (realize this is a tough one) or if they have available cells from Tibetans or some eQTL or other similar datasets. The more closely they can connect this haplotype to EPAS1 expression, the more beneficial it would be for the article. As it stands, they currently have episomal luciferase assays showing reduction of enhancer activity in mouse preadipocytes of a human allele and a complete knockout of the mouse enhancer that doesn't recapitulate the Tibetan haplotype. A bit more work is needed to connect all of these to the Tibetan adaptation. As it stands now, this is all very circumstantial.

(2) In Figure 2A, the body weight of ENH5-KO normal diet is significantly lower until four weeks in male, and until 11 weeks and 18 and 19 weeks in female than that of WT. These are slight but significant differences between ENH5-KO and WT; therefore, the authors should describe and discuss this and how it could affect their results.

(3) For the mouse work, it is not clear why the authors did not do cold-exposure or some type of hypoxia experiment for the mice themselves. This will be helpful to support their claim, and if not done, or done without significant differences in the results, the authors should add and mention this. The RNA-seq work, while substantial, again provides circumstantial support.

(4) The authors used CL316243 as a β3-AR selective agonist to mimic thermogenesis in vitro. In humans, it is not β3-AR but β2-AR that mainly drives thermogenesis (Blondin et al., Cell Metabolism, 32, 287-300. e7). Therefore, the authors should describe the limitation due to the difference in mechanisms of action of thermogenesis between humans and mice, as they use the mouse cells as a human model.

(5) The authors note in the discussion that Figure 3's CL316243 stimulation intended to simulate a thermogenic reaction to cold temperatures also generated a change in OXPHOS pathways associated with hypoxia, thus making it difficult to separate the contribution of β3-adrenergic/thermogenic effect from an indirect local hypoxia response. The authors could further interrogate this effect by measuring canonical hypoxia-responsive genes, oxygen consumption, or performing an in vivo cold challenge.

(6) Figure 4: The authors mention that reduced aerobic respiration pathways are evidence for reduced thermogenesis, but it does not directly demonstrate altered thermogenesis correlates. They do not measure heat synthesis, oxygen consumption/respiration, uncoupled respiration, UCP1 protein levels or activity, mitochondrial changes, etc. Their evidence for changed thermogenesis stems from transcriptional changes in energy consumption pathways shared with hypoxia changes. They should tone down their findings.

(7) In the Discussion, the authors should interpret and discuss their data carefully. For example, in the GSEA analysis, the authors identified enriched gene sets in ENH5-KO. Therefore, the authors should discuss which genes might contribute to each pathway, since some genes show large logFC changes. In the current discussion, there is little mention of their results, and it mostly focuses on prospects.

Reviewer #2 (Public review):

Summary:

This study extends previous work on the adaptive EPAS1 locus by examining the pleiotropic activity of the ENH5 enhancer in adipocytes and its potential role in metabolic and thermogenic responses. The authors progress from demonstrating enhancer activity and evolutionary conservation to in vivo phenotyping and environmentally dependent transcriptional responses in primary adipocytes. The work provides an interesting example of how pleiotropic regulatory effects can contribute to the complexity of adaptation, with a single adaptive regulatory locus influencing multiple biological processes in an environmentally dependent manner.

Strengths:

The study is well executed and is clearly presented, with a logical experimental progression. A particular strength is the genotype-by-treatment interaction analysis demonstrating that ENH5 loss alters metabolic and adipocyte-associated transcriptional programs following both hypoxia and beta-3-adrenergic stimulation. The convergence of these responses is particularly interesting in the context of regulatory pleiotropy and suggests that selection at the EPAS1 locus may have consequences extending beyond the canonical hypoxia response. The inclusion of negative findings, including the absence of an overt baseline metabolic phenotype and the lack of an additive response to combined stimulation, also provides a balanced presentation of the results.

Weaknesses:

The principal conclusions are generally supported by the data, and the weaknesses are relatively minor and primarily relate to the scope of interpretation. The study assesses transcriptional programs associated with thermogenic signaling using CL316243 rather than directly measuring physiological thermogenesis. Nonetheless, CL316243 is a rational and well-established approach for experimentally inducting beta-3-adrenergic thermogenic signaling. In addition, the murine ENH5 knockout is a useful model of reduced enhancer activity that phenocopies the Tibetan ENH5 haplotype, but it is not genetically equivalent to the naturally occurring Tibetan ENH5 haplotype. The authors generally recognize these limitations, and they do not substantially detract from the central findings.

eLife Assessment

This study provides important insights into the regulation of neuroblast lifespan and proliferation in the Drosophila mushroom body, identifying Krüppel (Kr) as a key transcription factor promoting timely termination of these neuroblasts by regulating Imp/Syp transition and E93 expression. This study proposes that Kr acts antagonistic to Krüppel homolog 1 (Kr-h1), whose overexpression leads to prolonged mushroom body neuroblast proliferation and tumor-like expansion. The findings are impactful for researchers interested in temporal patterning and neural development. The methods and data analysis are solid.

Reviewer #1 (Public review):

Summary:

In this manuscript, the authors investigated factors required for neural progenitors to exit cell cycle before the adult stage. They first show that Kr is expressed in pupal stage MBNBs, and depletion of Kr from pupal stage NBs leads to retention of MBNBs into the adult stage. Then they demonstrate that these retained NBs maintain the expression of Imp, and co-depletion of Imp abolishes the extended neurogenesis. Further, they show that co-depletion of kr-h1 significantly reduces the retained MBNBs caused by loss of kr, suggesting antagonistic genetic interactions between these two. In addition, they demonstrate that over-expressing Kr-h1 leads to the striking phenotype of tumor-like neuroblast overgrowth in adult brains. In the revised manuscript, they provide evidence suggesting that Kr does not regulate Kr-h1 expression, but rather Kr and Kr-h1 may regulate the late temporal gene E93 expression in parallel.

Strengths:

(1) The authors leveraged well-controlled powerful genetic tools (including temporal control of RNAi knock down using the Gal80ts system), and provided strong evidence that Kr is required for the Imp to Syp transition and to promote the end of neurogenesis through E93 in mushroom body neuroblasts. Similarly, the experimental result of co-depleting Kr-h1 and Kr, and the striking phenotype upon Kr-h1 mis-expression, support the antagonistic roles played by Kr-h1 and Kr in this process.

(2) The sample sizes, quantification methods and p-values are well documented for all experiments. In most parts, the data presented strongly support their conclusions.

(3) Identification of two transcription factors with opposite roles in controlling cell cycle exit, and their possible interactions with the Imp/Syp axis, is highly significant for the study on how the proliferation of neural progenitors is regulated and limited before the adult stage.

Weaknesses:

(1) In the revised manuscript, Kr immunostaining was done in KrIf-1 mutant brains using tyramide signal amplification (TSA) to enhance the weak endogenous Kr signal, and they conclude that Kr is ectopically detected in MBNBs and their progeny. However, a wildtype control with TSA amplified Kr immunostaining was not provided, so it is not known whether the elevated signal comes from TSA amplification or the mutant condition. If Kr is indeed mis-expressed in MBNBs in the KrIf-1 mutant, the authors should provide a hypothesis to explain why both loss of Kr and mis-expression of Kr in MBNBs lead to the same NB retention phenotype.

Reviewer #2 (Public review):

In this paper, the authors study the role of Krüppel in regulating the termination and survival of mushroom body neuroblasts. They first confirm that adult wild-type brains have no proliferation and report that Kr mutants and Kr RNAi specifically in neuroblasts prolong MBNB lifespan, enabling continued neurogenesis in the adult brain. They further show that Kr acts during pupal stages to regulate the elimination to the mushroom body neuroblasts, as its depletion leads to neuroblast retention, revealing a previously unrecognised postembryonic function of Kr distinct from its established role in embryonic neurogenesis. Mechanistically, this is achieved by the regulation of the Imp/Syp transition and E93 expression. Finally, they show that Kr acts antagonistically to Kr-h1, which is expressed predominantly in larval stages. Together, these results identify Kr as a mushroom body neuroblast regulator coordinating intrinsic and extrinsic signal to regulate neuroblast termination.

Strengths:

The main strength of this paper is that it identified a novel regulator of Imp expression in the mushroom body neuroblasts. Imp is a conserved RNA binding protein that has been shown to regulate neural stem cell proliferation and survival in different animals.

Moreover, the authors provide a series of evidence that this regulator, Kruppel, acts by integrating extrinsic signals (ecdysone) with intrinsic timers (Imp-Syp transition) to regulate neuroblast termination.

Weaknesses:

No significant weaknesses were identified.

Reviewer #3 (Public review):

Summary:

Drosophila neuroblasts (NBs) serve as a well-established model for studying neural stem cell biology. The intrinsic genetic programs that control their mitotic potential throughout development have been described in remarkable detail, highlighting a series of sequentially expressed transcription factors and RNA-binding proteins that together constitute the temporal patterning system.

However, the mechanisms that limit the number of NB divisions remain largely unknown in a specific subset of NBs known as mushroom body neuroblasts (MB NBs). Unlike other NBs, which terminate proliferation before or shortly after the onset of metamorphosis, MB NBs continue dividing until the end of metamorphosis, ceasing only just before adulthood.<br /> In this study, the authors identify the transcription factor Krüppel (Kr), a member of the conserved Krüppel-like family, as temporally regulated in MB NBs. They demonstrate that Kr knockdown during pupal stages maintains expression of the RNA-binding protein Imp and results in prolonged MB NB proliferation into adulthood. Their data suggest that Kr contributes to the timely silencing of Imp during metamorphosis. The authors further identify Kr-h1, a related transcription factor, as a potential antagonist. While Kr-h1 appears dispensable for the timely termination of MB NBs under normal conditions, its overexpression leads to their continued proliferation and tumor-like expansion in adults.

This work provides the first evidence for a transcription factor-driven temporal regulation mechanism in MB NBs, offering new insight into the control of neural stem cell self-renewal. Given the evolutionary conservation of Krüppel-like factors, this study may have broader implications for the neural stem cell field.

Strengths:

(1)The study possibly identifies a new series of temporal transcription factors that are specific for mushroom body neuroblasts.

(2) The mechanism could be conserved in vertebrates.

Comment on revised version.

The authors have clarified the expression status of Kr in the KrIf-1 mutant, as well as the regulatory interactions among Kr, Kr-h1, and E93. My other concerns have also been satisfactorily addressed. I congratulate the authors on this excellent work and on discovering a novel mechanism that regulates temporal progression and the termination of division in mushroom body neuroblasts.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

In this manuscript, the authors investigated factors required for neural progenitors to exit the cell cycle before the adult stage. They first show that Kr is turned on in pupal stage MBNBs, and depletion of Kr from pupal stage NBs leads to retention of MBNBs into the adult stage. Then they demonstrate that these retained NBs maintain the expression of Imp, and co-depletion of Imp abolishes the extended neurogenesis. Further, they show that co-depletion of kr-h1 significantly reduces the retained MBNBs caused by loss of kr, suggesting antagonistic genetic interactions between these two. In addition, they demonstrate that over-expressing Kr-h1 leads to the striking phenotype of tumor-like neuroblast overgrowth in adult brains.

Strengths:

(1) The authors leveraged well-controlled, powerful genetic tools (including temporal control of RNAi knockdown using the Gal80ts system), and provided strong evidence that Kr expression in pupal stage MBNBs is required to repress Imp and promote the end of neurogenesis. Similarly, the experimental result of co-depleting Kr-h1 and Kr, and the striking phenotype upon Kr-h1 mis-expression, support the antagonistic roles played by Kr-h1 and Kr in this process.

(2) The sample sizes, quantification methods, and p-values are well documented for all experiments. In most parts, the data presented strongly support their conclusions.

(3) Identification of two transcription factors with opposite roles in controlling cell cycle exit, and their possible interactions with the Imp/Syp axis, is highly significant for the study on how the proliferation of neural progenitors is regulated and limited before the adult stage.

We thank Reviewer #1 for their thoughtful and constructive assessment of our manuscript. We are grateful that the reviewer recognised the strength of our genetic approaches, the significance of identifying Kr and Kr-h1 as opposing regulators of MBNB termination, and the value of linking these factors to the Imp/Syp axis. We have revised the manuscript substantially in response to the reviewer’s comments. In particular, we have further characterised Kr expression in the KrIf-1 mutant background, examined the relationship between Kr, Kr-h1 and E93, analysed Kr-h1 expression in MBNBs using a Kr-h1::GFP BAC reporter, revised the proposed model, improved figure presentation and corrected typographical errors throughout the manuscript.

Weaknesses:

(1) The nature of the KrIf-1 allele is not clear. It is mentioned that this allele leads to misexpression of Kr in various tissues. However, it is not clear if Kr is mis-expressed or lost in MBNBs in the KrIf-1 mutant. If Kr is mis-expressed in MBNBs in the KrIf-1 mutant, then it would be difficult to explain why both loss of Kr and mis-expression of Kr in MBNBs lead to the same NB retention phenotype. The authors should examine Kr expression in MBNBs in the KrIf-1 mutant.

We agree that clarifying the nature of Kr expression in the KrIf-1 mutant background is important. We have therefore performed additional Kr immunostaining in KrIf-1 mutant brains using tyramide signal amplification (TSA) to enhance the weak endogenous Kr signal. These new data show that Kr is ectopically detected in MBNBs and their progeny in KrIf-1 mutant late pupal and adult brains (Fig. S3G, H), and quantification of TSA-enhanced Kr signals further supports Kr misexpression in MBNBs during late pupal stages (Fig. S3I). We have added these data to the revised manuscript. These results indicate that the KrIf-1 phenotype is associated with aberrant Kr expression in MBNBs rather than a simple loss of Kr expression. We agree with the reviewer that it may appear counterintuitive that both Kr depletion and Kr misexpression can lead to MBNB retention. We now discuss this point more explicitly. Our interpretation is that MBNB termination requires tight control of Kr activity during a narrow developmental window. Loss of Kr prevents the normal progression of the Imp-to-Syp transition and E93 activation, whereas ectopic or mistimed Kr expression in KrIf-1 mutants may also interfere with the same termination programme. Thus, both reduced Kr activity and inappropriate Kr expression can disrupt the precisely regulated Kr-dependent transition required for timely MBNB cell-cycle exit and elimination.

We have revised the Results and Discussion to make this interpretation clearer and to avoid describing KrIf-1 simply as equivalent to Kr loss of function.

(2) Some parts of the regulations and interactions between Kr, Kr-h1, Imp, Syp, and E93 are not well-defined. For example, the data suggest that Kr is turned on in the pupal stage MBNBs, and is required to end neurogenesis through repressing Imp and Kr-h1. To further support this conclusion, the authors can examine if Kr-h1 expression is up-regulated in kr-RNAi.

The authors suggested that Kr-h1 may act upstream or in parallel to Imp/Syp, but also suggested that Kr-h1 may repress E93. The expression of Imp, Syp, and E93 can be examined in brains with Kr-h1 mis-expression to determine where Kr-h1 acts. If Imp expression is elevated when Kr-h1 is mis-expressed, then Kr-h1 may act upstream of Imp. If Imp/Syp expression does not change, then Kr-h1 may act on the E93 level.

We thank the reviewer for this helpful suggestion. We agree that the regulatory relationships between Kr, Kr-h1, Imp/Syp and E93 were not sufficiently defined in the original manuscript. In the revised manuscript, we have therefore clarified which relationships are supported by our data and which remain unresolved.

During revision, we placed particular emphasis on the relationship between Kr, Kr-h1 and E93, because our genetic interaction data showed that co-depletion of Kr-h1 partially suppresses MBNB retention caused by Kr depletion (Fig. 5A). This indicated that Kr and Kr-h1 functionally oppose each other during MBNB termination. We therefore asked whether this functional antagonism could be explained by a simple linear pathway in which Kr promotes termination by suppressing Kr-h1, which in turn antagonises E93.

We first tested whether Kr-h1 regulates E93 in the MBNB lineage. Kr-h1 depletion increased E93 expression in the MBNB lineage, whereas Kr-h1 overexpression strongly reduced E93 expression (Fig. S5B). These data support the conclusion that Kr-h1 antagonises E93 expression in this lineage, consistent with the established antagonistic relationship between Kr-h1 and E93 in other developmental contexts.

We next examined whether Kr regulates this Kr-h1–E93 axis by suppressing Kr-h1 expression. To address this, we used a functional Kr-h1::GFP BAC reporter. Kr-h1::GFP was readily detected in larval MBNBs but was strongly downregulated during pupal development, consistent with the MBNB-lineage-specific RNA-seq dataset of Liu et al. (2015). However, Kr depletion did not significantly increase Kr-h1::GFP levels in late pupal MBNBs (Fig. 5B and Fig. S5C). Moreover, despite the absence of detectable Kr-h1::GFP upregulation, Kr depletion strongly reduced E93 expression in the progeny region of the MBNB lineage, while the weak E93 signal detectable in MBNBs themselves was not substantially altered (Fig. 5B).

These results argue against a simple linear pathway in which Kr promotes MBNB termination by directly repressing Kr-h1 expression. Instead, they suggest that Kr supports E93 expression within the MBNB lineage through a mechanism that does not require detectable upregulation of Kr-h1. Thus, Kr and Kr-h1 functionally oppose each other during MBNB termination, but they are unlikely to act through a simple linear Kr–Kr-h1–E93 pathway. We have revised the model accordingly, proposing that Kr and Kr-h1 act through convergent or parallel mechanisms to regulate the MBNB termination programme.

Regarding the Imp/Syp axis, the original manuscript had already shown that Kr depletion causes persistent Imp expression in adult MBNB lineages and that co-depletion of Imp suppresses MBNB retention caused by Kr depletion. These data supported the conclusion that persistent Imp expression is required for MBNB retention following Kr depletion. In the revised manuscript, we strengthened this conclusion by analysing Imp and Syp expression during late pupal development, when MBNBs normally undergo cell-cycle exit and elimination. We found that Kr-depleted MBNBs maintain higher Imp expression and show reduced Syp expression compared with controls (Fig. 4A, B), supporting the idea that Kr promotes MBNB termination by facilitating the normal Imp-to-Syp transition.

We also considered whether Kr-h1 acts upstream of the Imp/Syp transition. Kr-h1 overexpression caused persistent Imp expression in proliferating adult NBs (Fig. 5E). However, this manipulation produced a severe tumour-like overgrowth phenotype and likely represents a strongly non-physiological state. We therefore do not conclude that Kr-h1 normally acts upstream of Imp/Syp during MBNB termination. Rather, our revised interpretation is that Kr promotes MBNB termination through the Imp-to-Syp transition and by supporting E93 expression, whereas Kr-h1 counteracts termination at least in part by repressing E93. How the Imp/Syp and E93-associated pathways converge during MBNB termination remains an important question for future work.

We have revised the Results, Discussion and Fig. 6D model accordingly, distinguishing experimentally supported relationships from more speculative connections.

Reviewer #2 (Public review):

Summary:

In this paper, the authors study the role of Kruppel in regulating the survival of mushroom body neuroblasts. They first confirm that adult wild-type brains have no proliferation and report that Kruppel mutants and Kruppel RNAi in neuroblasts show a few proliferative clones; they show that these proliferative clones are localized in the mushroom body. They then show that Kruppel is expressed mostly during pupal stages and acts by downregulating the expression of Imp, which has been shown to positively regulate neuroblast proliferation and survival. Expectedly, this also affects neuronal diversity in the mushroom body, which is enriched in gamma neurons that are born during the Imp-expression window. Finally, they show that Kr acts antagonistically to Kr-h1, which is expressed predominantly in larval stages.

Strengths:

The main strength of this paper is that it identified a novel regulator of Imp expression in the mushroom body neuroblasts. Imp is a conserved RNA-binding protein that has been shown to regulate neural stem cell proliferation and survival in different animals.

We thank Reviewer #2 for their critical assessment of our manuscript and for the specific suggestions regarding manuscript framing, figure clarity, public dataset analysis and textual accuracy. We have revised the manuscript extensively in response to these comments. In particular, we have clarified that our study does not aim to describe physiological adult neurogenesis in Drosophila, but rather investigates how normally terminating neural progenitors can retain or regain neurogenic potential when the developmental termination programme is disrupted. We have also revised the text to avoid overstatement about functional integration of adult-born neurons, improved figure presentation, removed the incomplete targeted-screen framing, added analysis of public MBNB-lineage transcriptomic data, and corrected multiple textual and citation issues.

Weaknesses:

(1) The main weakness of the paper is that the authors want to test adult neurogenesis in a system where no adult neurogenesis exists. To achieve this, they force neuroblasts to survive in adulthood by altering the genetic program that prevents them from terminating their proliferation. If this was reminiscing about "adult neurogenesis", the authors should at least show how adult neurons incorporate into the mushroom body even if they are born much later. On the contrary, this more likely resembles a tumorigenic phenotype, when stem cells divide way past their appropriate timing.

We appreciate this important point and agree that Drosophila does not normally show substantial physiological neurogenesis in the adult central brain under standard conditions. We have therefore revised the manuscript to clarify the framing of our study. Our aim is not to claim that Kr depletion reveals a normal physiological adult neurogenesis programme, but rather to identify developmental mechanisms that normally terminate MBNB proliferation and restrict latent neurogenic potential in the adult brain.

We note, however, that the original manuscript already provided evidence that the persistent proliferative cells induced by Kr depletion or the KrIf-1 mutation are associated with the MB lineage and generate neuronal progeny in young adult brains. EdU-positive clones were detected predominantly in the dorsoposterior MB cell body region (Fig. 2A, B). These clones generally contained a single Mira- and insc>GFP-positive NB-like cell, including mitotic cells with cortical Mira localisation (Fig. 2C, D), together with surrounding Elav-positive neuronal progeny (Fig. 2E). In addition, persistent mitotic cells in KrIf-1 mutant brains were found in the MB cell body region marked by mb247>GFP and OK107>GFP, and showed Mira localisation consistent with dividing MBNBs (Fig. 2F-H). Thus, although we have not directly demonstrated mature circuit integration, the original data support the conclusion that Kr depletion and the KrIf-1 mutation allow MBNBs to persist beyond their normal termination window and generate neuronal progeny within the MB region.

At the same time, our data do not establish the precise neuronal identity, connectivity or functional incorporation of the newly generated progeny into mature MB circuits, nor do they determine the long-term behaviour of these progeny in older adult brains. We have therefore revised the text and Discussion to avoid overinterpreting these cells as fully integrated adult-born MB neurons, and now state that these issues remain important questions for future work.

We also agree that prolonged progenitor proliferation can become pathological in some contexts. However, we do not think that the Kr-depletion and KrIf-1 phenotypes are equivalent to tumour-like overgrowth, at least under the conditions analysed here. In young adult brains, retained MBNBs remained spatially restricted to the MB cell body region, and each EdU-positive clone generally contained only a single NB-like cell with asymmetric Mira localisation, surrounded by Elav-positive neuronal progeny (Fig. 2C-E, G, H). This pattern is more consistent with persistent asymmetric MBNB divisions than with tumour-like expansion. This contrasts with Kr-h1 overexpression, which caused extensive tumour-like NB overproliferation with impaired neuronal differentiation; we now describe this latter phenotype as tumour-like NB overgrowth (Fig. 5C-E). We have revised the manuscript to distinguish these phenotypes more clearly.

(2) Moreover, the figures are, in many cases, hard to understand, and the interpretation of the figures doesn't always match what one sees. The manuscript would benefit from better figures; for example, in Figure 2C, Miranda expression in insc>GFP in Kr-IF-1 is not visible.

We thank the reviewer for pointing out the need to improve figure clarity. We have revised the figure presentation throughout the manuscript to improve readability, including increasing label size, improving panel labelling and ensuring that the interpretation in the Results is consistent with the corresponding figure panels and legends.

Regarding the specific concern about Fig. 2C, we agree that the Mira signal was not sufficiently clear in the merged image. We have therefore added a Mira-only single-channel panel to Fig. 2C to allow the relevant signal to be evaluated more directly. We have also revised the text to clarify that retained MBNBs were identified based on combined positional, morphological and marker criteria, rather than by Mira signal alone.

(3) The authors describe a targeted genetic screen, but they don't describe which genes were tested, how they were chosen, and why Kruppel was finally selected.

We agree that the original description of a targeted genetic screen was insufficient. Because the screen was preliminary and incomplete, we concluded that presenting partial screening information would not be sufficiently informative and could overstate the scope of the present study. We have therefore removed the screen-based framing from the revised manuscript. Instead, the revised manuscript presents Kr as a candidate selected for focused functional analysis based on its known role in neuroblast temporal regulation and the strong MBNB retention phenotype observed upon Kr depletion and in the KrIf-1 mutant background.

(4) The authors argue that Kr does not behave as a typical tTF in MBNBs. However, they show no expression in the embryo, limited expression in the larva and early pupa, and a peak around P24-P48. This sounds like a temporally regulated expression of a transcription factor. Importantly, they mentioned that they tested their observations against different datasets (FlyAtlas2, modENCODE, and MBNB-lineage-specific RNA-seq data), but they don't provide the data.

We thank the reviewer for this helpful comment. We agree that our original wording could have been clearer. Our intention was not to argue that Kr cannot have a temporally restricted function in MBNBs, but rather that Kr does not behave like a canonical temporal transcription factor whose expression undergoes a strong stage-specific switch in this lineage.

We have revised both the text and the corresponding quantification. In the original version, Kr signal levels in pupal MBNBs appeared to vary modestly across pupal stages. However, after reanalysing cytoplasmic and nuclear Kr signals separately using Welch’s ANOVA followed by Dunnett T3 multiple-comparison correction, no pairwise comparisons reached statistical significance (Fig. 3E, F). Thus, the revised quantification does not support a significant temporal change in Kr protein levels during the pupal stages analysed, and we have avoided describing Kr as showing a clear pupal expression peak.

As requested, we have also included the public MBNB-lineage RNA-seq analysis in the revised manuscript as Fig. S5A. This analysis shows that Kr transcript levels remain low across the analysed developmental stages, in contrast to the stronger temporal changes observed for other regulators, including larval Kr-h1 expression followed by pupal downregulation, reciprocal induction of E93, and marked increases in Syp expression. Because FlyAtlas2 and modENCODE have limited spatial resolution for MBNB-specific expression, we now focus this comparison on the MBNB-lineage-specific RNA-seq dataset.

We have therefore revised the manuscript to describe Kr as a postembryonic regulator required for pupal MBNB termination, rather than as a conventional temporally induced tTF in this lineage. In our revised interpretation, Kr expression is low and not detectably strongly temporally induced in MBNBs, whereas Kr function is temporally required during pupal MBNB termination, as supported by the Gal80ts knockdown experiments.

(5) Finally, the contribution of Kr to the neuronal composition of the mushroom body is expected (since Imp is known to regulate neuronal diversity in the MB), but the presentation in the paper is very incomplete.

We agree that, given the known role of Imp/Syp in MB neuronal temporal identity, altered MB neuronal composition is a plausible consequence of disrupted Kr function. However, we also agree that our study does not directly determine the precise neuronal identities, connectivity or functional properties of the progeny produced by persistent MBNBs. We have therefore revised the manuscript to present this aspect more cautiously.

In the original manuscript, we had shown that Kr depletion and the KrIf-1 mutation affect MB morphology. In the revised manuscript, we have clarified the presentation of these data and added new analysis of the severe MB defects caused by Kr-h1 overexpression (Fig. 6C). We now describe these phenotypes as changes in MB morphology and lineage progression, rather than as direct evidence for altered neuronal composition.

In the Discussion, we state that persistent Imp expression in Kr-depleted MBNBs could bias neuronal progeny toward earlier identities or delay their transition to later identities, but we explicitly note that neuronal identity and connectivity were not directly analysed. We also state that future studies will be required to determine whether prolonged MB neurogenesis alters MB circuit function, learning, plasticity or ageing. Thus, we have revised the manuscript to avoid overstating the contribution of Kr to MB neuronal composition.

Unfortunately, based on the above, I am not convinced that the authors can use this framework to infer anything about adult neurogenesis. Therefore, the impact of this work is limited to the role of Kruppel in regulating Imp, which has already been shown to regulate the extent of neuroblast division, as well as the neuronal types that are born at different temporal windows.

We understand the reviewer’s concern and have revised the manuscript to avoid implying that our data establish physiological adult neurogenesis in Drosophila. Instead, we now frame the study as identifying mechanisms that normally terminate MBNB proliferation and restrict latent neurogenic potential in the adult brain.

We respectfully note, however, that the impact of this study is not limited to showing that Kr regulates Imp. First, we identify Kr as a postembryonic regulator required for timely MBNB termination during pupal development. Second, we show that both Kr depletion and the KrIf-1 mutation allow MBNBs to persist beyond their normal termination window and generate neuronal progeny in the adult MB region. Third, we show that Kr promotes not only the Imp-to-Syp transition but also proper E93 expression within the MBNB lineage. Finally, we identify Kr-h1 as a functionally opposing KLF-family factor that represses E93 and can drive tumour-like NB overgrowth when misexpressed. We have revised the manuscript to present these conclusions more clearly and cautiously.

Reviewer #3 (Public review):

Summary:

Drosophila neuroblasts (NBs) serve as a well-established model for studying neural stem cell biology. The intrinsic genetic programs that control their mitotic potential throughout development have been described in remarkable detail, highlighting a series of sequentially expressed transcription factors and RNA-binding proteins that together constitute the temporal patterning system.

However, the mechanisms that limit the number of NB divisions remain largely unknown in a specific subset of NBs known as mushroom body neuroblasts (MB NBs). Unlike other NBs, which terminate proliferation before or shortly after the onset of metamorphosis, MB NBs continue dividing until the end of metamorphosis, ceasing only just before adulthood.

In this study, the authors identify the transcription factor Krüppel (Kr), a member of the conserved Krüppel-like family, as temporally regulated in MB NBs. They demonstrate that Kr knockdown during pupal stages maintains expression of the RNA-binding protein Imp and results in prolonged MB NB proliferation into adulthood. Their data suggest that Kr contributes to the timely silencing of Imp during metamorphosis. The authors further identify Kr-h1, a related transcription factor, as a potential antagonist. While Kr-h1 appears dispensable for the timely termination of MBNBs under normal conditions, its overexpression leads to their continued proliferation and tumor-like expansion in adults.

This work provides the first evidence for a transcription factor-driven temporal regulation mechanism in MB NBs, offering new insight into the control of neural stem cell self-renewal. Given the evolutionary conservation of Krüppel-like factors, this study may have broader implications for the neural stem cell field.

Strengths:

(1) The study possibly identifies a new series of temporal transcription factors that are specific for mushroom body neuroblasts.

(2) The mechanism could be conserved in vertebrates.

We thank Reviewer #3 for their positive and constructive assessment of our study. We are grateful that the reviewer recognised the significance of identifying Kr as a regulator of mushroom body neuroblast termination, and the potential broader relevance of KLF-family transcription factors to neural stem cell regulation.

In response to the reviewer’s comments, we have substantially revised the manuscript. In particular, we have added new data on Kr expression in the KrIf-1 mutant background, Kr-h1 expression in MBNBs, and the regulation of E93 by Kr and Kr-h1. We have also incorporated public MBNB-lineage transcriptomic data to place Kr, Kr-h1, E93, Imp and Syp within the known temporal progression of the MB lineage. Finally, we have revised the proposed model to distinguish experimentally supported interactions from open mechanistic questions.

Weaknesses:

Some proposed regulatory interactions, particularly between Kr, Kr-h1, and other temporal factors like Imp, Chinmo, and E93, have not been thoroughly investigated, which weakens the support for the proposed model. Additional experimental validation is needed to confirm these relationships and strengthen the mechanistic framework.

We agree with the reviewer that some regulatory relationships in the original model required further experimental support. In response, we have added new data and revised the model substantially to distinguish experimentally supported interactions from unresolved mechanistic links.

In the revised manuscript, we provide additional analysis of the Imp/Syp axis after Kr depletion, direct evidence for Kr-h1 expression in MBNBs, and new data showing that Kr-h1 antagonises E93 expression in the MBNB lineage. We also found that Kr depletion reduces E93 expression in the progeny region of the MBNB lineage without significantly increasing Kr-h1::GFP levels in MBNBs, arguing against a simple linear pathway in which Kr promotes termination by directly repressing Kr-h1. Together, these results support a revised model in which Kr promotes MBNB termination by facilitating the Imp-to-Syp transition and supporting E93 expression, whereas Kr-h1 functionally opposes termination at least in part through E93 repression.

Recommendations for the authors:

Reviewing Editor Comments:

The majority of the reviewers agreed that a few major important points should be addressed, in particular:

(1) Better characterization of the nature of the KrIf-1 allele.

(2) Better define the regulations and interactions between Kr, Kr-h1, Imp, Syp, chinmo, and E93.

(3) More information about the genetic screen performed.

(4) The timings of expression of Kr in pupal MBNBs and of KrIf-1.

The reviewers also found that a general proofreading of the manuscript would greatly benefit its readability and comprehension and suggested several small corrections and more detailed explanations.

We thank the Reviewing Editor and Senior Editor for their careful assessment of our manuscript and for summarising the major points that required revision. We have addressed these points as follows.

(1) Better characterisation of the nature of the KrIf-1 allele

We agree that clarifying the nature of the KrIf-1 allele was important. We have now examined Kr expression in KrIf-1 mutant brains using TSA-enhanced Kr immunostaining. These new data show ectopic Kr signal in MBNBs and their progeny in KrIf-1 mutant late pupal and adult brains (Fig. S3G–I), supporting the conclusion that the KrIf-1 phenotype is associated with Kr misexpression rather than simple loss of Kr expression. We have revised the Results and Discussion to explain that MBNB termination requires precise control of Kr activity, and that both Kr depletion and inappropriate Kr expression can disrupt this termination programme.

(2) Better definition of the regulatory relationships between Kr, Kr-h1, Imp, Syp, Chinmo and E93

We have strengthened this part of the manuscript by combining the genetic evidence already present in the original manuscript with new expression analyses of temporal and hormone-responsive regulators. The original manuscript already showed that co-depletion of Imp suppresses MBNB retention caused by Kr depletion, supporting Imp as a key downstream effector of Kr. In the revised manuscript, we further show that Kr depletion causes persistent Imp expression and reduced Syp expression in late pupal MBNBs (Fig. 4), supporting the conclusion that Kr promotes MBNB termination by facilitating the Imp-to-Syp transition.

We have also added new data on Kr-h1 and E93. Kr-h1 depletion increases E93 expression in the MBNB lineage, whereas Kr-h1 overexpression reduces E93 expression (Fig. S5B), supporting an antagonistic relationship between Kr-h1 and E93 in this lineage. In addition, Kr depletion reduces E93 expression in the surrounding progeny of the MBNB lineage without detectably increasing Kr-h1::GFP levels in late pupal MBNBs (Fig. 5B). These data argue against a simple linear Kr-Kr-h1-E93 pathway and instead support a model in which Kr and Kr-h1 function through convergent or parallel mechanisms to regulate MBNB termination.

Regarding Chinmo, we agree that it is an important temporal factor. However, Chinmo is best characterised in this context as an early temporal fate regulator acting downstream of the Imp/Syp programme in MB lineages, where Imp and Syp regulate Chinmo translation post-transcriptionally (Liu et al., 2015). Because our study focuses primarily on late pupal MBNB termination, and because we were unable to obtain reliable Chinmo antibodies or reporter lines within the timeframe of this revision, we did not directly analyse Chinmo expression. We have therefore removed Chinmo from the main model and revised the Discussion to focus on the experimentally supported Imp/Syp and Kr-h1/E93 axes.

(3) More information about the genetic screen

We agree that the original screen-based description was not sufficiently informative. Because the targeted screen was preliminary and incomplete, we have removed the screen-based framing from the revised manuscript. Instead, we now present Kr as a candidate selected for focused functional analysis based on its known role in neuroblast temporal regulation and the strong MBNB retention phenotype observed upon Kr depletion and in the KrIf-1 mutant background.

(4) Timing of Kr expression in pupal MBNBs and in KrIf-1

We have clarified the timing of Kr expression in MBNBs. In wild-type brains, weak Kr signals were detected in MBNBs during pupal development using two Kr antibodies and a Kr::GFP BAC reporter, and these signals were reduced by Kr RNAi (Fig. 3E, F and Fig. S3F). We also analysed MBNB-lineage RNA-seq data, which show relatively low but persistent Kr transcript levels during postembryonic development (Fig. S5A). In the KrIf-1 background, TSA-enhanced Kr staining revealed ectopic Kr expression in MBNBs and their progeny during late pupal and adult stages (Fig. S3G–I). We have revised the manuscript to describe these expression patterns more clearly and to avoid overinterpreting weak embryonic or larval Kr signals.

We have also proofread the manuscript, corrected typographical errors, standardised figure references and nomenclature, improved figure legends and revised several figures for clarity.

Reviewer #1 (Recommendations for the authors):

(1) The authors identified Kr from a targeted genetic screen. Information about how many factors and what factors they have screened will also be very helpful to readers.

We thank the reviewer for this suggestion. In the original manuscript, we briefly referred to a targeted genetic screen that led us to focus on Kr. However, because this screen was preliminary and incomplete, we agree that including partial screening information would not be sufficiently informative and might overstate the scope of the present study. We have therefore revised the manuscript to remove the screen-based framing and instead present Kr as a candidate selected for focused functional analysis based on its known role in neuroblast temporal regulation and the strong MBNB retention phenotype observed upon Kr depletion and in the KrIf-1 mutant background.

(2) In Figure 2C wild type brains, what are the Mira+ cells and insc>GFP+ cells? There seems to be one cell that expresses both. Could it be a dormant NB?

We thank the reviewer for pointing this out. We agree that a small number of weakly Mira-positive and insc>GFP-positive cells can occasionally be observed in adult control brains, as well as in KrIf-1 mutant brains. These cells were few in number, were generally located outside the stereotyped MBNB region, and showed much weaker marker signals than the retained MBNBs observed after Kr depletion or in KrIf-1 mutants. Because they did not appear to express other NB markers examined in this study, such as wor>GFP, we did not investigate them further. Their identity therefore remains unclear, and we cannot exclude the possibility that they represent rare dormant or NB-like cells in the adult brain.

We have revised the text and figure legend to clarify that the retained MBNBs analysed in this study were identified based on their stereotyped MB-region position and strong NB-marker expression.

(3) Kr is normally expressed in stage 10 embryonic NBs. Have stage 10 embryos been examined to make sure that there is no Kr expression in MBNBs?

We thank the reviewer for this important point. We agree that Kr expression in early embryonic neuroblasts is well established. Early embryonic MBNBs can in principle be identified using a detailed positional and combinatorial marker map, as shown by Kunz et al. (2012), who traced individual MBNBs from late embryonic stages back to stage 9 using combinations of Dac, Ey, Svp-lacZ and Rx, together with morphological and positional criteria. However, reliable identification of MBNBs at such early stages is technically challenging in our assay, because our analysis depended on simultaneous detection of OK107>GFP, Mira and Kr, and OK107>GFP/Mira-based identification of the MB lineage was more robust at later embryonic stages. We therefore focused our embryonic Kr analysis on stages at which MBNBs could be confidently identified by their position and marker expression.

In these embryos, Kr was broadly detected in surrounding embryonic CNS cells, including thoracic NBs, but was not robustly detected in OK107>GFP- and Mira-positive MBNBs (Fig. S3A, B). We cannot fully exclude the possibility that MBNBs transiently express very low levels of Kr at earlier embryonic stages before they can be reliably identified in our assay. However, our temporally controlled Gal80ts experiments show that Kr depletion during the pupal stage, but not during earlier embryonic or larval stages, is sufficient to cause MBNB retention in adult brains (Fig. 3C, D). Thus, any transient embryonic Kr expression, if present, is unlikely to be the main cause of the adult MBNB retention phenotype described here.

We have revised the text to avoid overinterpreting the absence of embryonic Kr expression and to emphasise that the critical requirement for Kr in this study occurs during pupal MBNB termination.

(4) In Figure S3C, Kr expression seems to be cytoplasmic. Also in S3D, the expression of KrGFP in NBs is not obvious. Overall, Kr expression in pupal MBNBs is much more convincing than the larval expression.

We agree with the reviewer. Kr expression in larval MBNBs is weak and less convincing than the pupal signal. We have therefore revised the manuscript to describe larval Kr expression more cautiously. In the revised text, we state that Kr was weakly detected in larval MBNBs by antibody staining and that the Kr::GFP BAC reporter showed stronger signals in cells adjacent to MBNBs, likely corresponding to GMCs or immature neurons that may have inherited Kr::GFP from MBNBs.

We now base our main conclusion primarily on the pupal-stage data. At this stage, weak Kr signals were detected in MBNBs using two independent Kr antibodies and the Kr::GFP BAC reporter, and Kr depletion reduced the antibody signal (Fig. 3E, F and Fig. S3F). Importantly, this expression pattern is consistent with our functional data showing that pupal-stage-specific Kr depletion is sufficient to induce MBNB retention in adult brains, whereas earlier embryonic or larval depletion did not produce the same phenotype (Fig. 3C, D). Thus, both the expression and temporal knockdown data support a critical role for Kr during pupal MBNB termination.

We also discuss the observation that Kr signals in pupal MBNBs appear partly cytoplasmic, raising the possibility that Kr may not act solely as a canonical nuclear transcription factor in this context, or that its localisation may be dynamically regulated during MBNB termination. Thus, we agree that the pupal expression data provide the strongest support for Kr expression in MBNBs, and we have revised the text accordingly.

(5) A thorough proofreading is needed to correct the typos.

We apologise for the typographical and formatting errors in the original manuscript. We have thoroughly proofread the revised manuscript, corrected typographical errors, standardised figure references and gene/protein nomenclature, and revised multiple sections for clarity and readability. We have also revised the figure legends and improved figure presentation where possible.

Reviewer #2 (Recommendations for the authors):

(1) The authors should proofread for typos; there are quite a few ("survivial", "fount", "mitoic", "persistenc").

We apologise for these typographical errors. We have thoroughly proofread the revised manuscript, corrected typographical errors and formatting problems, and revised multiple sections for clarity and readability.

(2) In line 59, "adult eclosion" is incorrect. MBNBs also cease dividing before adult eclosion.

We thank the reviewer for pointing this out. We have revised the wording to avoid the incorrect phrase “adult eclosion” and now state that MBNBs normally terminate during late pupal development, before adulthood.

(3) In line 70, this progression of transcription factors is seen in the mammalian retina, not the brain.

We thank the reviewer for this correction. We have revised the relevant sentence to more accurately describe temporal patterning in mammalian neural progenitors, including the well-characterised example of retinal progenitor temporal progression and broader examples of temporal competence changes in cortical development.

(4) In lines 73-75, I don't think that any of the cited papers show that Cas triggers cell cycle exit. Ref 11 shows that, in UAS-Cas, NBs persist (as the authors also say in lines 79-81).

We agree that the original wording was too strong and potentially misleading. We have revised this section to state more generally that temporal transcription factors can influence NB proliferation and NB lifespan, rather than claiming that Cas directly triggers cell-cycle exit. We have also adjusted the discussion of Cas and Svp to better reflect the cited literature.

(5) In lines 133-134, it should be Figure 2A, B instead of Figure 3A, B.

We thank the reviewer for identifying this error. We have corrected the figure reference.

(6) Figures 1B and 1C are impossible to read. The x-axis should be reorganized and grouped into positive and negative CCRs to make a better argument. Moreover, the purpose of this figure is unclear. We already knew that neurons are postmitotic and all adult clusters are neurons. IF there were any NBs in the adult, they would be so few that they would be invisible with this resolution.

We thank the reviewer for this comment. We agree that the dot plots are dense, because they summarise the expression of 112 selected cell-cycle regulator (CCR) genes across multiple adult and larval brain cell clusters. In preparing the revised manuscript, we have ensured that the figure legends explain the meaning of colour intensity and dot size, and that the submitted PDF preserves sufficient resolution for the gene and cluster labels to be read upon enlargement.

In the original figures, CCR genes were arranged according to broad functional categories. We have not forced all CCR genes into a simple positive-versus-negative classification, because the function of many CCRs is context-dependent. For example, APC/C components can contribute to either mitotic progression or G1 maintenance depending on co-activator context, and mitotic regulators such as Polo and Aurora kinases regulate multiple aspects of mitosis rather than acting simply as positive cell-cycle drivers. We therefore present the genes according to broad functional categories and discuss representative examples of positive and inhibitory regulators in the Results and figure legends, rather than implying that every CCR can be assigned unambiguously to one of two categories.

Regarding the purpose of these analyses, our aim was not simply to restate that adult neurons are postmitotic, nor to claim that scRNA-seq can definitively exclude extremely rare adult progenitors. Rather, we used published scRNA-seq datasets to compare CCR expression programmes across adult and larval brain cell populations in an unbiased manner. The analysis shows that no adult brain cluster displays a coordinated larval NB-like positive CCR expression programme, whereas such a programme is readily observed in larval NB clusters. We have clarified this point in the text and acknowledge the limitation that very rare or non-canonical progenitor-like cells may not be detected by this approach.

(7) The survival assays are confusing. Do the authors believe that the presence or absence of 2-3 clones in the adult brain of a few cells would lead to such a limited survival?

We thank the reviewer for raising this point. We agree that the survival assay required clearer explanation and should be interpreted cautiously. In this experiment, E2F1-Dp and Cdk2-CycE were expressed using TH-Gal4 to test whether forced activation of positive cell-cycle regulators can drive postmitotic neurons into aberrant cell-cycle re-entry. Although only a small number of pH3-positive cells may be detected at any single time point, this represents only a snapshot of an ongoing process and may underestimate the cumulative number of affected cells over time.

TH-Gal4-positive dopaminergic neurons are relatively limited in number, but they include functionally important neuronal populations involved in motor behaviour, arousal, sleep/wake regulation and ageing-associated behavioural decline. Therefore, broad induction of aberrant cell-cycle re-entry and apoptosis within these neurons could plausibly affect organismal survival. However, we agree that the survival phenotype should not be overinterpreted. We cannot exclude the possibility that TH-Gal4 expression outside dopaminergic neurons, developmental effects of the manipulation, or other indirect consequences contribute to the reduced survival. Moreover, the precise cause of death was not determined in this study. We have therefore revised the manuscript to present the survival assay as supporting evidence that inappropriate activation of positive cell-cycle regulators is deleterious in postmitotic neurons, rather than as a direct mechanistic explanation for organismal lethality.

(8) In Figure 2, how many of the proliferative clones are found in the mushroom body. Is it all of them?

We thank the reviewer for this question. In Fig. 2, EdU-positive proliferative clones were scored based on their stereotyped position in the dorsoposterior MB cell body region. Under the conditions analysed, the scored clones were consistently detected within this MB region, and their number did not exceed four per brain hemisphere, consistent with the expected number of MBNBs (Fig. 2A, B). In addition, the identity of these clones as retained MBNB lineages was supported by NB marker expression, Mira localisation, insc>GFP expression where applicable, and their association with MB lineage markers such as mb247>GFP and OK107>GFP in KrIf-1 mutant brains (Fig. 2C-H). We have clarified this point in the revised text and figure legend.

(9) In Figure 2C, why are there so many Miranda-positive cells?

We thank the reviewer for this question. We agree that several Mira-positive cells can be observed in Fig. 2C, including in control brains. The identity of these additional Mira-positive cells remains unclear. They did not consistently co-express the canonical NB markers examined in this study, such as insc>GFP or wor>GFP, and therefore do not appear to represent canonical proliferative NBs. However, we cannot exclude the possibility that some weak Mira-positive cells represent rare dormant or NB-like cells in the adult brain. We have revised the text and figure legend to clarify this point.

(10) In Figure 3C, the authors argue that Kr has an opposing function in NB regulation during larval stages, however, the Kr mutant (which is in both larval and pupal stages) has the highest number of EdU-positive clones. Moreover, conditions 2 and 9 have a comparable (low) number of EdU positive clones, although condition 2 has Kruppel downregulated in all stages.

We thank the reviewer for this comment. We agree that this part of the temporal knockdown experiment required more careful interpretation, and we have revised the manuscript to avoid overinterpreting small quantitative differences among individual temperature-shift conditions.

First, Fig. 3C does not include a Kr mutant condition. We assume that the reviewer is referring to the constitutive insc>KrIR condition grown at 29°C throughout development (condition 1). This condition does not contain tub-Gal80ts and may therefore produce stronger and more continuous Kr RNAi induction than the Gal80ts-based temporal knockdown conditions. In addition, for practical reasons, flies in all conditions were initially kept at 25°C during egg laying to obtain sufficient embryos before being shifted to the indicated temperature regime, including condition 2. These differences may explain why condition 1 produced the highest number of EdU-positive clones. For this reason, we do not interpret condition 1 as a temporal-control condition and do not use it for direct quantitative comparison with the Gal80ts-based conditions.

Second, regarding the comparison between conditions 2 and 9, we agree that these conditions should not be used to infer a simple relationship between the total duration of Kr knockdown and the number of retained MBNBs. We therefore avoid using these differences to infer an additional larval function of Kr. Instead, we now interpret this temporal knockdown experiment more conservatively: Kr depletion during the pupal period is sufficient to induce MBNB retention in adult brains, whereas depletion restricted to earlier embryonic/larval stages or later adult stages has little or no effect.

Thus, the key conclusion supported by these data is the pupal-stage requirement for Kr in MBNB termination, rather than detailed comparisons among all temperature-shift conditions. We have revised the text accordingly.

Overall, we have revised the manuscript to address the reviewer’s concerns by narrowing the framing of adult neurogenesis, clarifying the distinction between persistent MBNBs and tumour-like overgrowth, improving figure presentation, removing the incomplete screen description, adding public dataset analysis, and correcting textual and citation errors. We believe these revisions make the scope and conclusions of the study more precise.

Reviewer #3 (Recommendations for the authors):

Major Points

(1) Targeted screen: The authors mention performing a targeted genetic screen. Please specify which transcription factors were tested.

We thank the reviewer for this suggestion. In the original manuscript, we briefly referred to a targeted genetic screen. However, this screen was preliminary, incomplete, and included a broader set of candidate regulators rather than a systematically completed transcription-factor collection. We therefore agree that listing a partial set of tested factors would not be sufficiently informative and could overstate the scope of the present study.

We have therefore removed the screen-based framing from the revised manuscript. Instead, the revised manuscript presents Kr as a candidate selected for focused functional analysis based on its established role in neuroblast temporal patterning and the strong MBNB retention phenotype observed upon Kr depletion and in the KrIf-1 mutant background. We also no longer use the preliminary screen as part of the evidence supporting our conclusions.

(2) KrIf-1 allele : The authors report that KrIf-1 mutants retain MB NBs in adults, a phenotype resembling Kr loss of function. They propose that this results from Kr deregulation. However, KrIf-1 is a neomorphic allele known to cause ectopic expression in imaginal discs, raising the possibility that Kr is upregulated, not downregulated, in MB NBs. The authors should present experimental data on Kr expression in MB NBs in the KrIf-1 background to clarify this point.

We agree that clarification of Kr expression in the KrIf-1 background is important. We have therefore performed additional Kr immunostaining in KrIf-1 mutant brains using tyramide signal amplification (TSA) to enhance the weak endogenous Kr signal. These new data show that Kr is ectopically detected in MBNBs and their progeny in KrIf-1 mutant late pupal and adult brains (Fig. S3G, H), and quantification of TSA-enhanced Kr signals further supports Kr misexpression in MBNBs during late pupal stages (Fig. S3I).

These results indicate that KrIf-1 is associated with ectopic or aberrant Kr expression in MBNBs, rather than simple loss or downregulation of Kr expression. We have revised the manuscript to clarify this point and no longer interpret KrIf-1 as a simple Kr loss-of-function condition. Although both Kr depletion and KrIf-1 lead to MBNB retention, our revised interpretation is that MBNB termination requires precise temporal and spatial control of Kr activity. Kr depletion disrupts the normal Imp-to-Syp transition and reduces E93 expression in the MBNB lineage, whereas ectopic or mistimed Kr expression in KrIf-1 mutants may also interfere with the termination programme. Thus, both reduced Kr activity and inappropriate Kr expression can perturb the tightly regulated transition required for timely MBNB cell-cycle exit and elimination.

(3) Line 258 - OK107>GFP subset (Fig. 2G): Please clarify why only a subset of EdU-positive clones co-express OK107>GFP. Is this due to EdU labeling other NB lineages not related to the mushroom body?

We thank the reviewer for raising this point. We do not think that the OK107-negative EdU-positive clones represent unrelated NB lineages. The EdU-positive clones analysed in Fig. 2G were located in the dorsoposterior MB cell body region and were associated with Mira-positive NB-like cells, supporting their identification as persistent MBNB-lineage clones.

The reason that only a subset of EdU-positive clones clearly co-express OK107>GFP is likely that, while OK107-Gal4 strongly labels MB neurons and lineage cells, its activity in MBNBs and very young progeny appears to be weaker or more variable at the stages analysed. Thus, the absence of strong OK107>GFP signal in some EdU-positive cells does not necessarily indicate that these clones belong to non-MB lineages.

We have revised the text and figure legend to clarify this point.

(4) Line 261 - Early adulthood mitotic activity: The statement that NBs retain mitotic activity during early adulthood (citing Technau, 2007; Li and Hidalgo, 2020) is misleading. To my knowledge, this mitotic activity has only been reported in glial cells, not NBs. Please revise accordingly.

We thank the reviewer for pointing this out. We agree that the original wording was misleading, because it could be read as implying that normal NBs retain mitotic activity during early adulthood. We have revised the text accordingly. The revised manuscript now refers more cautiously to the previously described early-adult period during which rare residual cell-cycle or proliferative activity has been reported in the adult Drosophila brain, without attributing this activity to normal persistent NBs.

(5) Line 313 - Public dataset analysis: The manuscript mentions analysis of publicly available data, but no results are presented. Please include these findings.

We agree and have now included the public dataset analysis in the revised manuscript. We analysed a published MBNB-lineage-specific RNA-seq dataset and present the expression profiles of selected temporal regulators in Fig. S5A.

This analysis shows that Imp and chinmo transcripts are high during larval stages and decrease during pupal development, whereas Syp is strongly upregulated during the same period. Kr transcript levels remain relatively low throughout the analysed larval and pupal stages and do not show strong temporal induction. In contrast, Kr-h1 is highly expressed during larval stages and sharply downregulated after the larval-to-pupal transition, whereas E93 is strongly induced during pupal development.

These expression profiles support the idea that MBNBs undergo a major temporal transition during pupal development, including the Imp/Syp transition and reciprocal changes in Kr-h1 and E93 expression. They are also consistent with our experimental finding that Kr-h1 antagonises E93 expression in the MBNB lineage. We have added this analysis to the Results and incorporated it into the revised model.

(6) Figure 3A - Kr localization: Kr is detected predominantly in the cytoplasm, which contrasts with its function as a transcription factor. Is cytoplasmic localization typical for Kr? Please discuss.

We thank the reviewer for this important observation. We agree that the weak Kr signal in pupal MBNBs appears partly enriched in the cytoplasm, which is unexpected for a canonical nuclear transcription factor. We have revised the Discussion to address this point.

Because this signal was reduced upon Kr RNAi, we think that it is likely to represent a Kr-dependent signal rather than nonspecific background. However, we do not yet know whether the apparent cytoplasmic enrichment reflects dynamic regulation of Kr localisation, a non-canonical aspect of Kr function in postembryonic MBNBs, or technical limitations associated with detecting very low endogenous Kr levels. We therefore avoid overinterpreting the cytoplasmic signal, but note that Kr localisation and activity in pupal MBNBs may be more complex than expected for a canonical nuclear transcription factor. Future studies will be required to determine how Kr activity and localisation are regulated in pupal MBNBs.

(7) Temporal Kr knockdown experiment: The result that Kr knockdown during pupal stages - but not earlier - leads to MB NB persistence is interesting but counterintuitive. Given the limitations of RNAi (e.g., leaky expression, incomplete knockdown), MARCM clones for Kr mutants would provide stronger evidence and improve confidence in this conclusion.

We agree that MARCM analysis of Kr mutant MBNB clones would provide a valuable independent test of the temporal RNAi results. We attempted to establish this approach during revision, but it proved technically difficult within the available timeframe.

A major practical limitation is that MBNBs are very few in number, with only four per brain hemisphere. Conventional MARCM or flip-out approaches therefore generate stochastic clones that are inefficient for reliably recovering and analysing MBNB clones. We also explored the possibility of using MB-lineage MARCM reagents reported in a previous study (Rossi & Desplan, 2020), but the available stocks were not directly compatible with the FRT chromosome required for our Kr mutant analysis. Generating the necessary compatible stocks and recovering sufficient MBNB clones would require substantial additional crossing and screening.

For this reason, we were not able to include Kr mutant MARCM data in the revised manuscript. Instead, we base our conclusion on several complementary lines of evidence, including temporal Gal80ts-based Kr RNAi, two independent Kr RNAi lines, the reduction of Kr signal upon Kr RNAi newly added in this revision, and the independent KrIf-1 phenotype, which supports the idea that precise regulation of Kr activity is required for MBNB termination.

(8) OK107-GAL4 activity: Please indicate early in the manuscript that OK107-GAL4 is not active in MB NBs but is active in their progeny. This would clarify the rationale for using the pan-NB driver insc-GAL4 for manipulating MB NBs.

We thank the reviewer for this suggestion. We have revised the manuscript to clarify the use of OK107-Gal4 and insc-Gal4 earlier in the Results and in the relevant figure legends.

Although OK107-Gal4 activity is not completely absent from MBNBs, its activity in MBNBs is stage-dependent and weaker or more variable than in MB neurons and their progeny. We therefore used OK107-Gal4 mainly to visualise MB structures and MB lineage regions, whereas insc-Gal4 was used for robust NB-specific manipulation. This clarification should help explain why insc-Gal4, rather than OK107-Gal4, was used for MBNB-targeted knockdown experiments.

(9) Figure 5A - Mira+ cell numbers: There appears to be an excess of Mira+ cells compared to the expected number of MB NBs. Please explain this observation.

We thank the reviewer for pointing this out. In Fig. 5A, we quantified the number of EdU-positive clones, not the total number of Mira-positive cells. As shown in Fig. 2, proliferative cells retained in Kr-depleted or KrIf-1 mutant adult brains were identified as persistent MBNBs based on combined criteria, including EdU incorporation, NB marker expression such as Mira and insc>GFP, NB-like morphology, and stereotyped location in the dorsoposterior MB region.

We agree that additional Mira-positive cells can be observed in adult brains, including in control and Kr-depleted brains. However, these cells were not associated with EdU-positive proliferative clones and did not consistently express canonical NB markers examined in this study. Their identity therefore remains unclear, and they were not scored as retained MBNBs.

(10) Line 430 - Kr-h1 over-expression phenotype: The amplification phenotype caused by Kr-h1 overexpression is reminiscent of that caused by chinmo overexpression (Narbonne-Reveau et al., 2016), suggesting that Kr-h1 may promote chinmo and Imp expression. Also, what is the expression pattern of Kr in the supernumerary adult MB NBs following Kr-h1 overexpression? Is Kr silenced? Investigating this would help clarify the regulatory links between Kr, Kr-h1, and Imp/chinmo.

We agree that the Kr-h1 overexpression phenotype is reminiscent of NB amplification phenotypes associated with forced or aberrant activation of early temporal growth programmes, including those linked to Chinmo. Narbonne-Reveau et al. showed that Chinmo can promote NB amplification and tumour growth, and that Chinmo, Imp and Lin-28 form a growth-promoting module in neural tumours. Consistent with this idea, our revised manuscript shows that Kr-h1 overexpression causes extensive tumour-like NB overgrowth, impaired neuronal differentiation and persistent Imp expression (Fig. 5C–E).

Although we did not analyse Chinmo expression in this revision, we did examine Imp expression following Kr-h1 overexpression and found persistent Imp expression in tumour-like NB cells (Fig. 5E). These data are consistent with the idea that excessive Kr-h1 activity can reinforce a progenitor-like state. However, we have interpreted this result cautiously, because Kr-h1 overexpression produces a severe tumour-like phenotype with impaired asymmetric division and neuronal differentiation. Thus, persistent Imp expression in this context could reflect either a more direct effect of Kr-h1 on early temporal programmes or an indirect consequence of the strongly perturbed progenitor-like state.

We also did not directly analyse Kr expression in supernumerary NB-like cells following Kr-h1 overexpression. This is an interesting question, but the severe tissue disruption caused by Kr-h1 overexpression would make it difficult to distinguish a physiological regulatory effect on Kr from an indirect consequence of tumour-like overgrowth. In addition, endogenous Kr signals in MBNBs are weak, making it technically challenging to reliably quantify changes in Kr expression in this strongly perturbed condition.

We have therefore revised the Discussion to clarify that the Kr-h1 overexpression phenotype should be interpreted mainly as evidence that excessive Kr-h1 activity can oppose MBNB termination and maintain Imp-positive progenitor-like cells, rather than as evidence for a defined normal regulatory pathway from Kr-h1 to Chinmo, Imp or Kr. In parallel, our revised loss-of-function and expression analyses show that Kr depletion causes persistent Imp and reduced Syp expression, that Kr supports E93 expression in the MBNB lineage (Fig. 5B), and that Kr-h1 antagonises E93 expression (Fig. S5B). Because Kr depletion did not significantly increase Kr-h1::GFP expression (Fig. 5B), we no longer present a simple linear model in which Kr promotes MBNB termination by repressing Kr-h1 expression.

(11) Kr-h1 expression in MB NBs: Please provide direct evidence that Kr-h1 is expressed in MB NBs during development.

We agree that direct evidence for Kr-h1 expression in MBNBs is important. We have therefore analysed Kr-h1 expression using a functional Kr-h1::GFP BAC reporter. Kr-h1::GFP was clearly detected in MBNBs during third-instar larval stages, with nuclear enrichment, but became barely detectable in late pupal MBNBs (Fig. 5B and Fig. S5C).

This developmental downregulation is consistent with the published MBNB-lineage RNA-seq dataset, which shows high Kr-h1 transcript levels during larval stages and strong reduction after the larval-to-pupal transition (Fig. S5A). Together, these data provide direct evidence that Kr-h1 is expressed in MBNBs during development and is downregulated before MBNB termination.

(12) Figure 6D - Model validation: The model in Figure 6D is appealing, but many of the proposed interactions remain untested. For example:

- It is not established that Kr-h1 antagonizes E93 or vice versa in MB NBs.

- The antagonistic relationship between Kr and Kr-h1 has not been experimentally confirmed.

- The temporal expression of Kr-h1 in MB NBs is unknown.

- The repression of E93 by Kr-h1 is unlikely to fully explain the MB NB amplification phenotype.

We thank the reviewer for this helpful critique. We have substantially revised Fig. 6D and the accompanying text to distinguish experimentally supported interactions from unresolved regulatory links.

First, we have now tested the relationship between Kr-h1 and E93 in the MBNB lineage. Kr-h1 depletion increased E93 expression, whereas Kr-h1 overexpression reduced E93 expression (Fig. S5B), supporting the conclusion that Kr-h1 antagonises E93 expression in this lineage. Reciprocal antagonism between Kr-h1 and E93 has been reported in other insect developmental contexts. However, because we did not directly test whether E93 represses Kr-h1 in MBNBs, we now present this possible E93-to-Kr-h1 regulation as an unresolved or putative interaction rather than as an experimentally established relationship in our system.

Second, we have clarified the relationship between Kr and Kr-h1. Our genetic data show that Kr-h1 knockdown partially suppresses MBNB retention caused by Kr depletion (Fig. 5A), indicating that Kr and Kr-h1 have opposing functions during MBNB termination. However, although Kr depletion reduced E93 expression in the MBNB lineage, it did not detectably increase Kr-h1::GFP levels in late pupal MBNBs (Fig. 5B). We therefore no longer present Kr as a direct upstream repressor of Kr-h1. Instead, the revised model proposes that Kr promotes MBNB termination by supporting the Imp-to-Syp transition and E93 expression, whereas Kr-h1 opposes termination at least in part by repressing E93.

Third, we now provide direct evidence for Kr-h1 expression in MBNBs using a functional Kr-h1::GFP BAC reporter. Kr-h1::GFP was detected in larval MBNBs and became strongly reduced during pupal development (Fig. 5B and Fig. S5C). This temporal pattern is also consistent with the published MBNB-lineage RNA-seq dataset, which shows high Kr-h1 transcript levels during larval stages and downregulation after the larval-to-pupal transition (Fig. S5A).

Finally, we agree that repression of E93 by Kr-h1 is unlikely to fully explain the strong tumour-like NB overgrowth caused by Kr-h1 overexpression. In the revised manuscript, we show that supernumerary tumour-like NB cells induced by Kr-h1 overexpression retain high Imp expression (Fig. 5E). This suggests that excessive Kr-h1 activity can oppose MBNB termination and maintain an Imp-positive progenitor-like state.

However, we interpret the Kr-h1 overexpression phenotype cautiously, because this strong gain-of-function condition causes severe tumour-like overgrowth and may not accurately reflect the physiological regulatory relationship between Kr-h1 and the normal MBNB termination programme. We have therefore revised the Discussion to state that Chinmo, an early temporal factor linked to the Imp/Syp programme, may be relevant to the persistent progenitor-like state observed after Kr depletion or Kr-h1 overexpression. However, because we did not directly analyse Chinmo expression in this study, we do not include Chinmo in the main model and leave this question for future work.

Minor Points

(1) OK107-GAL4 activity: Please check and indicate early on in the manuscript that OK107-GAL4 is not active in MB NBs (although being active in their progeny). It would clarify why the authors keep using the pan NB insc-GAL4 to manipulate MB NBs.

As described in our response to Major Point 8, we have clarified earlier in the Results that OK107-Gal4 strongly labels MB neurons and the MB lineage, but is not a robust or consistent driver in MBNBs at the stages relevant to our functional assays. We therefore used OK107-Gal4 primarily for visualising MB structures and MB lineage regions, whereas insc-Gal4 was used for robust NB-specific manipulation.

(2) CCR list: Please clarify how the list of candidate cell cycle regulators (CCRs) was compiled.

We have revised the Materials and Methods to clarify how the list of candidate cell-cycle regulators was compiled. Briefly, the CCR list was manually curated to include core cell-cycle regulators, cyclins and CDKs, DNA replication factors, checkpoint regulators, mitotic regulators, APC/C and ubiquitin-proteasome components, and non-canonical CDKs with known roles in transcriptional regulation.

(3) Line 77-78 - Cas and Svp: The statement that Cas and Svp regulate neurogenesis termination by directly regulating cell cycle regulators needs references. As far as I know, the direct targets of Cas and Svp remain unidentified.

We agree that the original wording was too strong. We have revised the text to state more generally that temporal transcription factors, including Cas and Svp, influence NB proliferation and lifespan, without implying that they directly regulate known cell-cycle target genes.

(4) Line 410: Please add references to support this statement.

We have added the appropriate reference to the original genetic modifier screen by Abrell et al., 2000, in which Kr-h1 mutations were identified as enhancers of the KrIf-1 eye phenotype. We have also revised the wording to state that this finding suggests a functional interaction between Kr and Kr-h1, rather than using it alone as evidence for a direct regulatory relationship.

(5) Typos and minor edits:

- Line 38: "capable" (spelling)

- Line 102: Replace "unexplored" with "explored"

- Line 106: "potential" (spelling)

- Line 243: "mitotic" (spelling)

- Line 260: "KrIf-1" (correct gene formatting)

We have corrected the typographical errors and formatting issues indicated by the reviewer, including spelling errors and KrIf-1 gene formatting. We have also proofread the manuscript throughout.

eLife Assessment

This paper provides a valuable observation that imiquimod, a compound often used to induce a psoriasis-like skin inflammation in mice, has a TLR7-independent effect acting through the unfolded protein response and binding to Gelsolin. These solid findings expand our understanding of imiquimod-mediated inflammation and are of interest to the field of skin immunology.

Reviewer #2 (Public review):

Summary:

This paper shows that imiquimod, a compound often used to induce a psoriasis-like skin inflammation in mice, has a TLR7-independent effects that induce the unfolded protein response and amplify cytokine expression in dendritic cells. Although these effects of imiquimod have been described in the literature before, this study provides more detailed evidence and different contexts to this observation. These findings add to existing literature that imiquimod has a pleotropic mechanism of action involving changes in mitochondrial functions and cellular stress responses. Specifically, the authors show that imiquimod can induce calcium signaling in immune cells and potentiate two branches of the unfolded protein response in a TLR7-independent and MyD88-independent manner. They also show that some of these effects might be partially mediated by direct binding of imiquimod to Gelsolin. These findings expand our understanding of imiquimod-mediated inflammation and are useful for the field of experimental skin immunology and mouse models of psoriasis. However, molecular and cellular mechanisms connecting Gelsolin to the unfolded protein response and skin inflammation presented in this paper requires further investigation in the context of TLR-mediated inflammation.

Strengths:

(1) TLR7-independent effects of imiquimod to the expression of genes and proteins involved into the unfolded protein response are well demonstrated.

(2) Gelsolin is identified as a new imiquimod-binding protein in mouse cells.

Weaknesses:

(1) Effects of imiquimod on mitochondrial Ca signaling are not clear form the presented data.

(2) The mechanism of action connecting imiquimod to Gelsolin on the unfolded protein response and cytokine production remains not fully explained.

(3) It remains unclear if Gelsolin contributes to regulating TLR7 (or other types of TLR-mediated) inflammation in vivo.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

The study is technically extensive and employs a wide range of experimental approaches, including in vivo analyses, cell-based assays, and transcriptomic data integration. The authors provide a detailed characterization of inflammatory and stress-related pathways activated following IMQ exposure in mouse skin. These datasets may be informative for researchers specifically interested in IMQ-induced dermatitis or in stress responses triggered by chemical skin irritants.

We sincerely thank the reviewer for this positive assessment of our study. We appreciate the recognition of the breadth of our experimental approaches, including the integration of in vivo analyses, cell-based experiments, and transcriptomic analyses, as well as the acknowledgement that our findings provide useful insights into IMQ-induced dermatitis and stress responses triggered by chemical skin irritants. We have carefully considered the reviewer's comments and have substantially revised the manuscript to address the concerns regarding the interpretation and disease relevance of our findings. Detailed responses to the specific points raised are provided below.

Strengths:

The study is technically extensive and employs a wide range of experimental approaches, including in vivo analyses, cell-based assays, and transcriptomic data integration. The authors provide a detailed characterization of inflammatory and stress-related pathways activated following IMQ exposure in mouse skin. These datasets may be informative for researchers specifically interested in IMQ-induced dermatitis or in stress responses triggered by chemical skin irritants.

We sincerely thank the reviewer for this positive assessment and for recognizing the breadth of our experimental approaches and the potential value of our findings for researchers studying IMQ-induced dermatitis and stress responses.

Weaknesses:

A major limitation of the manuscript is its exclusive reliance on the IMQ model, which does not adequately represent the immunological drivers, cellular interactions, or therapeutic responsiveness of human psoriasis, despite the manuscript's framing. IMQ-induced inflammation is dominated by innate immune activation and mouse-specific pathways, whereas human psoriasis is driven primarily by IL-23/IL-17-mediated interactions between keratinocytes and Th17/Tc17 cells. As a result, conclusions drawn entirely from IMQ-based experiments have limited relevance to human disease biology.

Consistent with this issue, the manuscript places strong emphasis on pathways such as TLR signaling, inflammasome activation, and IL-1-associated responses, none of which are established as central drivers of plaque psoriasis in patients. Therapeutic strategies targeting these pathways have failed to achieve clinical efficacy comparable to IL-23 or IL-17 blockade, yet this translational gap is not adequately addressed.

The in vitro keratinocyte experiments further limit interpretability. Stimulation of keratinocytes with IMQ is not an accepted model of psoriasis-relevant keratinocyte activation, and the study does not demonstrate induction of well-established psoriasis signature gene programs. Without this validation, it is difficult to assess the relevance of the observed cellular stress responses to human disease.

The RNA-sequencing analyses raise additional concerns regarding rationale and interpretation. The basis for selecting specific mouse and human datasets is unclear, including the use of unpublished or non-psoriasis inflammatory datasets. Key methodological details related to data processing, normalization, cross-species comparison, and statistical analysis are insufficiently described. In addition, the limited number of differentially expressed genes identified does not align with the extensive psoriasis transcriptomic literature, raising concerns about analytical rigor.

Finally, the manuscript emphasizes a small number of genes described as "psoriasis-associated" while failing to demonstrate regulation of widely accepted psoriasis signature genes known to correlate with disease activity and therapeutic response in patients.

We thank the reviewer for this thoughtful and comprehensive assessment of our study. We carefully considered each of the concerns raised regarding the interpretation and translational relevance of our findings and have substantially revised the manuscript accordingly.

Specifically, we have tempered our interpretation throughout the manuscript to clearly distinguish IMQ-induced dermatitis from human plaque psoriasis and to emphasize that our conclusions should be interpreted primarily within the context of the IMQ-induced inflammation model. To improve the relevance of our findings to psoriasis biology, we performed additional experiments using IL-17A- and TNF-α-stimulated primary keratinocytes and incorporated these data into the revised manuscript. We also expanded the description of our RNA-seq analyses, including dataset selection, analytical procedures, and cross-species comparison, and clarified the rationale for selecting representative UPR-responsive genes for validation. In addition, we revised the Introduction and Discussion to more appropriately position the roles of inflammasome signaling, IL-1-associated pathways, and Gelsolin in the context of IMQ-induced inflammation and human psoriasis.

We believe that these revisions substantially strengthen the manuscript and address the reviewer's major concerns. Detailed responses to each specific point are provided below.

Reviewer #2 (Public review):

Summary:

This paper shows that imiquimod, a compound often used to induce a psoriasis-like skin inflammation in mice, has a TLR7-independent effects that induce the unfolded protein response and amplify cytokine expression in dendritic cells. Although these effects of imiquimod have been described in the literature before, this study provides more detailed evidence and different contexts to this observation. These findings add to existing literature that imiquimod has a pleotropic mechanism of action involving changes in mitochondrial functions and cellular stress responses. Specifically, the authors show that imiquimod can induce calcium signaling in immune cells and potentiate two branches of the unfolded protein response in a TLR7-independent and MyD88-independent manner. They also show that some of these effects might be partially mediated by direct binding of imiquimod to Gelsolin. These findings expand our understanding of imiquimod-mediated inflammation and are useful for the field of experimental skin immunology and mouse models of psoriasis. However, the molecular and cellular mechanisms connecting Gelsolin to the unfolded protein response and skin inflammation presented in this paper require further investigation in the context of TLR-mediated inflammation.

We sincerely thank the reviewer for this thoughtful and balanced assessment of our study. We greatly appreciate the recognition that our work provides additional mechanistic insight into the TLR7-independent actions of IMQ and expands current understanding of IMQ-induced inflammation, mitochondrial dysfunction, and unfolded protein response signaling. We also appreciate the recognition that our findings may be valuable for the fields of experimental skin immunology and mouse models of psoriasis. In response to the reviewer's comments, we have further revised the manuscript to clarify the rationale for investigating Gelsolin, to better distinguish IMQ-induced inflammation from human psoriasis, and to more appropriately discuss the limitations of our mechanistic interpretation. Detailed responses to the specific points raised are provided below.

Strengths:

(1) TLR7-independent effects of imiquimod on the expression of genes and proteins involved in the unfolded protein response are well demonstrated.

(2) Gelsolin is identified as a new imiquimod-binding protein in mouse cells.

We sincerely thank the reviewer for these positive comments. We greatly appreciate the recognition that our study provides clear evidence for the TLR7-independent effects of IMQ on unfolded protein response signaling and identifies Gelsolin as a novel IMQ-binding protein. We are grateful for the reviewer's positive assessment of these findings.

Weaknesses:

(1) Effects of imiquimod on mitochondrial Ca signaling are not clear from the presented data.

(2) The mechanism of action connecting imiquimod to Gelsolin on the unfolded protein response and cytokine production remains not fully explained.

(3) It remains unclear if Gelsolin contributes to regulating TLR7 (or other types of TLR-mediated) inflammation in vivo.

We thank the reviewer for these thoughtful comments. We have carefully considered each of the concerns raised regarding the interpretation of mitochondrial Ca²⁺ signaling, the mechanistic link between Gelsolin and UPR signaling, and the role of Gelsolin in TLR-mediated inflammatory responses. In the revised manuscript, we have clarified the interpretation of our mitochondrial Ca²⁺ data, strengthened the discussion regarding the mechanistic role of Gelsolin based on the additional experiments performed in this revision, and more clearly defined the scope of our conclusions regarding Gelsolin in IMQ-induced inflammation. We believe these revisions substantially strengthen the manuscript while avoiding conclusions that extend beyond the experimental evidence. Detailed responses to each point are provided below.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

The following points outline specific issues that would need to be addressed to substantially strengthen the manuscript. Several of these represent fundamental limitations of the current study design and interpretation.

We thank the reviewer for this overall assessment. We have carefully addressed each of the points raised and have revised the manuscript accordingly. Detailed point-by-point responses are provided below.

(1) Model limitations

- The manuscript relies exclusively on imiquimod (IMQ), which does not model the core immune drivers or treatment responsiveness of human psoriasis.

- Claims regarding relevance to human psoriasis should therefore be substantially tempered, or alternative models more reflective of human disease biology should be incorporated.

We thank the reviewer for this important comment. We agree that the IMQ-induced dermatitis model does not fully recapitulate the immunopathology, chronicity, or therapeutic responsiveness of human plaque psoriasis. Accordingly, we have substantially tempered our interpretation throughout the manuscript. In the revised Introduction and Discussion, we explicitly state that our findings should be interpreted primarily in the context of IMQ-induced skin inflammation rather than human psoriasis, and that further validation in human psoriasis-relevant systems will be required. We have also revised statements throughout the manuscript to avoid overgeneralization regarding human psoriasis. In addition, to improve the disease relevance of our mechanistic findings, we have performed additional keratinocyte experiments using IL-17A and TNF-α stimulation, which better reflect the canonical inflammatory pathways implicated in human psoriasis. Together with the revised interpretation throughout the manuscript, we believe these changes appropriately position our findings within the context of the IMQ-induced dermatitis model while improving their relevance to human psoriasis.

Changes made in the manuscript: See Figure S6

- The Introduction and Discussion were revised to clarify the limitations of the IMQ-induced dermatitis model and to distinguish IMQ-driven inflammation from human plaque psoriasis.

- Statements implying direct relevance to human psoriasis were revised to more appropriately reflect the scope of the study.

- Additional experiments using IL-17A and TNF-α-stimulated keratinocytes were incorporated to strengthen the relevance of the findings to established psoriasis biology.

(2) Immune context

- gdT cells should be removed from the Introduction as contributors to IL-17A production in human psoriasis, as this is a feature of mouse models rather than human disease (PMID: 28945199).

- The roles of Th17 and Tc17 cells should be emphasized, with appropriate acknowledgment that IMQ-driven inflammation differs substantially from human psoriasis immunopathology.

We thank the reviewer for this valuable comment. We agree that gdT cells are major IL-17A-producing cells in the IMQ-induced mouse model but are not considered the principal source of IL-17A in human plaque psoriasis. Accordingly, we have revised the Introduction to remove statements implying that gdT cells are major contributors to IL-17A production in human psoriasis and have instead emphasized the established roles of Th17 and Tc17 cells. In addition, we have revised the Discussion to explicitly acknowledge that the immunopathology of the IMQ-induced dermatitis model differs substantially from that of human psoriasis and that our findings should therefore be interpreted within the context of IMQ-induced skin inflammation.

Changes made in the manuscript:

- Statements describing gdT cells as major IL-17A-producing cells in human psoriasis were removed from the Introduction.

- The roles of Th17 and Tc17 cells in human psoriasis were emphasized.

- Additional text was added to the Discussion clarifying the immunological differences between the IMQ-induced dermatitis model and human plaque psoriasis.

(3) Keratinocyte stimulation

- IMQ stimulation of keratinocytes is not an accepted model of psoriasis-relevant keratinocyte activation.

- To support disease relevance, experiments should incorporate stimulation with IL-17A (100 ng/ml) {plus minus} TNF-a (10 ng/ml) and appropriate time points consistent with established psoriasis biology.

We thank the reviewer for this constructive suggestion. We agree that stimulation of keratinocytes with IL-17A and TNF-α more closely reflects cytokine-mediated keratinocyte activation in human psoriasis than stimulation with IMQ alone.

We would like to clarify that our IMQ stimulation experiments were not intended to serve as a model of psoriasis-associated keratinocyte activation. Rather, these experiments were designed to investigate the molecular mechanisms by which IMQ directly induces UPR signaling in keratinocytes, as IMQ is the primary experimental stimulus used throughout this study.

To address the reviewer's concern regarding disease relevance, we performed additional experiments using primary keratinocytes stimulated with IL-17A and TNF-α. As expected, IL-17A and TNF-α robustly induced canonical psoriasis-associated genes, including S100a8, S100a9, and Defb14, thereby providing complementary evidence supporting the relevance of our findings to psoriasis-associated inflammatory signaling. These new data have been incorporated as Figure S6.

We believe that these additional experiments appropriately complement our mechanistic studies by linking the identified pathways to established psoriasis-associated inflammatory signaling while preserving the original objective of the IMQ stimulation experiments.

Changes made in the manuscript: See Figure S6

- New experiments using IL-17A and TNF-a-stimulated primary keratinocytes were performed.

- A time-course analysis was conducted to evaluate cytokine-induced gene expression.

- The new data have been included as Figure S6.

(4) Inflammasome and IL-1-related claims

- The manuscript should acknowledge that IL-1 and inflammasome targeting have failed to demonstrate clinical efficacy in plaque psoriasis.

- Observations in inflammasome-, MyD88-, or TLR-deficient mice should not be interpreted as evidence of underexplored human psoriasis pathways, but rather as reflecting IMQ-specific biology.

We thank the reviewer for this important comment. We agree that the contribution of IL-1 signaling and inflammasome activation to IMQ-induced skin inflammation should not be directly extrapolated to human plaque psoriasis. Accordingly, we have revised the Discussion to acknowledge that clinical studies targeting IL-1 signaling have not demonstrated consistent therapeutic efficacy in plaque psoriasis. We have also tempered our interpretation of findings obtained from inflammasome-, MyD88-, and TLR-deficient mouse models, emphasizing that these observations likely reflect mechanisms specific to the IMQ-induced dermatitis model rather than underexplored pathways in human psoriasis. Throughout the revised manuscript, statements implying direct relevance to human psoriasis have been modified accordingly.

Changes made in the manuscript:

- The Introduction and Discussion now acknowledge the limited clinical efficacy of IL-1-targeted therapies in plaque psoriasis.

- Statements regarding inflammasome-, MyD88-, and TLR-dependent mechanisms have been revised to clarify that they primarily reflect IMQ-specific biology.

- Interpretations linking these pathways directly to human psoriasis have been moderated throughout the manuscript.

(5) Cathelicidin and defensin biology

- Statements suggesting that LL37 or b-defensins "exacerbate psoriasis" should be revised to reflect their contributory roles in disease pathogenesis rather than disease worsening.

- It should be acknowledged that CRAMP- or defensin-deficient mice do not show improvement in IMQ-induced dermatitis, consistent with IMQ bypassing these pathways.

We thank the reviewer for this valuable comment. We agree that LL37 and b-defensins should not be described as factors that directly exacerbate psoriasis, but rather as multifunctional mediators that contribute to disease pathogenesis in a context-dependent manner. Accordingly, we have revised the relevant statements throughout the manuscript to more accurately reflect their proposed roles.

In addition, we have expanded the Discussion to acknowledge previous studies demonstrating that CRAMP- or b-defensin-deficient mice do not exhibit substantial improvement in IMQ-induced dermatitis. We now explicitly state that IMQ-driven inflammation can proceed independently of these pathways, highlighting the distinction between mechanisms contributing to human psoriasis pathogenesis and those operating in the IMQ-induced dermatitis model.

Changes made in the manuscript:

- Statements describing LL37 or b-defensins as exacerbating psoriasis were revised to indicate that they contribute to disease pathogenesis.

- The Discussion was expanded to acknowledge that CRAMP- or b-defensin deficiency does not substantially attenuate IMQ-induced dermatitis, consistent with the IMQ model bypassing these pathways.

- The limitations of extrapolating these observations to human psoriasis were clarified.

(6) Gelsolin and IMQ-binding experiments

- Experiments focused on proteins that bind IMQ have limited translational relevance.

- If gelsolin is to be emphasized, the rationale should be grounded in human psoriasis data demonstrating altered gelsolin levels rather than IMQ binding (PMIDs: 36902587, 32002760).

We thank the reviewer for this important comment. We agree that the translational relevance of proteins identified solely through their ability to bind IMQ is limited. Accordingly, we have revised the manuscript to clarify that our rationale for focusing on Gelsolin is supported not only by its interaction with IMQ but also by independent evidence demonstrating altered Gelsolin expression in patients with psoriasis and psoriatic arthritis. We have incorporated these human studies into the Introduction and Discussion and have revised the relevant text to emphasize the potential clinical relevance of Gelsolin beyond its interaction with IMQ.

Changes made in the manuscript:

- Statements emphasizing IMQ binding as the primary rationale for studying Gelsolin were revised.

- Additional references reporting altered Gelsolin expression in patients with psoriasis and psoriatic arthritis were incorporated.

- The Discussion now clarifies that the rationale for investigating Gelsolin is supported by both its interaction with IMQ and independent observations from human disease.

(7) Vehicle controls

- Appropriate vehicle controls for IMQ treatment (Aldara alone) should be included and clearly described, particularly given the known inflammasome-activating properties of isostearic acid (PMID: 23463003).

- The use of DMSO or ethanol as vehicle controls is not justified in this context.

We thank the reviewer for this important comment. We agree that inclusion of an appropriate vehicle control for Aldara cream would have strengthened the interpretation of the in vivo experiments. Unfortunately, the vehicle formulation of Aldara was not commercially available to us and therefore could not be included in the present study.

Because the in vivo experiment assessing mtDNA accumulation in ear tissue following topical IMQ cream application could not be appropriately controlled, we have removed these data from the revised manuscript. We believe this is the most appropriate approach to avoid overinterpretation of results that may potentially be influenced by the cream formulation.

Importantly, our in vitro experiments were performed using purified IMQ rather than IMQ cream. Thus, our conclusion that IMQ induces mtDNA release is supported by experiments performed with purified IMQ, independent of the topical cream formulation.

Changes made in the manuscript: See Figure 4

- The in vivo experiment assessing mtDNA accumulation in ear tissue following topical IMQ cream application has been removed from the revised manuscript.

- The Results and corresponding figure have been revised accordingly.

- The Discussion has been updated to acknowledge the limitation associated with the absence of an Aldara vehicle control.

(8) RNA-sequencing and bioinformatics

- The rationale for selecting specific mouse and human RNA-sequencing datasets should be clearly articulated.

- All datasets analyzed should be explicitly identified, with clarification of their relevance and publication status.

- Methods describing normalization, differential expression analysis, false-discovery correction, and cross-species gene mapping should be expanded to ensure transparency and reproducibility.

We thank the reviewer for this constructive comment. We have substantially expanded the description of the RNA-sequencing and bioinformatics analyses to improve transparency and reproducibility.

First, we now explicitly describe the rationale for selecting the public RNA-seq datasets. GSE289485 was selected because it contains transcriptomic profiles from an IMQ-induced mouse model of psoriasis-like dermatitis, whereas GSE117405 contains transcriptomic data from human psoriasis lesions and healthy control skin, enabling comparison between the mouse model and human disease. We also clarify that both datasets were publicly available at the time of analysis.

Second, detailed information regarding all GEO datasets analyzed, including accession numbers, sample descriptions, publication status, and the specific samples included in the present study, has been provided in Supplementary Table 14.

Finally, the bioinformatics workflow has been described in substantially greater detail. The revised Methods now include descriptions of raw data retrieval from the SRA, quality trimming, sequence alignment, rRNA read removal, read counting, normalization, differential expression analysis, multiple-testing correction, and the orthology-based cross-species comparison used to identify conserved transcriptional responses between mouse and human datasets.

Changes made in the manuscript: See Table S14

- The rationale for selecting GSE289485 and GSE117405 was added.

- Detailed information for all analyzed datasets was summarized in Supplementary Table 14.

- The RNA-seq Methods were expanded to describe quality control, alignment, read counting, normalization, differential expression analysis, false-discovery correction, and orthology-based cross-species comparison.

(9) Gene selection and validation

- Validation should include canonical psoriasis signature genes known to correlate with disease activity and therapeutic response (e.g., S100A8/A9, IL-17C, IL-36g, IL-23, TNF; see PMID: 21085185).

- The current emphasis on Ccl20, Nr4a3, and Defb14 does not adequately capture established psoriasis biology and should be better justified.

We thank the reviewer for this valuable suggestion. We agree that validation using canonical psoriasis-associated genes strengthens the disease relevance of our findings. Accordingly, we performed additional experiments using primary keratinocytes stimulated with IL-17A and TNF-α and evaluated the expression of established psoriasis signature genes, including S100a8 and S100a9. As expected, both genes were robustly induced by IL-17A and TNF- a stimulation. In addition, Defb14, which was also induced by IMQ stimulation, was similarly upregulated by IL-17A and TNF-α. These results further support the relevance of our findings to psoriasis-associated inflammatory signaling.

We have also clarified the rationale for selecting Ccl20, Nr4a3, and Defb14 for further validation. These genes were not intended to represent canonical psoriasis biomarkers but were selected because our transcriptomic analyses identified them as representative UPR-responsive genes that were strongly induced by IMQ stimulation. Accordingly, they were used to investigate the mechanistic contribution of UPR signaling rather than to represent the overall psoriasis transcriptional signature. This rationale has now been clarified in the revised Results section.

Changes made in the manuscript: See Figure S6, and S7

- Additional validation experiments were performed using IL-17A/TNF-a-stimulated keratinocytes.

- The rationale for selecting Ccl20, Nr4a3, and Defb14 was clarified in the Results section.

(10) Histology and data presentation

- Ear skin sampling procedures should be standardized and clearly described.

- All relevant control groups should be shown histologically.

- Figures require clearer labeling, consistent terminology (e.g., ear skin vs. ear lobe), appropriate white balancing, and improved quantitative presentation (e.g., dot plots where appropriate).

- qRT-PCR data should be presented using clearly defined raw or normalized values rather than scaled or ambiguous controls.

We thank the reviewer for these helpful suggestions. We have revised the manuscript to improve the description of histological procedures and the presentation of histological and quantitative data.

First, the Methods section has been expanded to clearly describe the ear skin sampling procedure. We now specify that approximately the distal 2 mm of the ear was collected and processed for histological analysis, thereby ensuring consistent sampling among all animals.

Second, we carefully reviewed the histological figures and confirmed that the relevant control groups are included in the revised manuscript.

Third, figure labeling and terminology have been standardized throughout the manuscript. In addition, quantitative histological data are now presented with individual data points overlaid on the graphs where appropriate, thereby improving data visualization and transparency. The representative histological images are intended to illustrate epidermal thickening, whereas the conclusions are based on quantitative measurements rather than qualitative assessment of image appearance.

Finally, the presentation of the RT-qPCR data has been clarified. The Y-axis labels now explicitly indicate the reference condition used for normalization, and the Methods section has been expanded to describe the DDCt method, including the reference genes used for normalization.

Changes made in the manuscript: See Figure 4D, and 5C

- The ear skin sampling procedure was described in greater detail in the Methods.

- Histological figures and figure labels were reviewed and terminology was standardized throughout the manuscript.

- Individual data points were added to quantitative graphs where appropriate.

- The RT-qPCR y-axis labels were revised to clearly indicate the normalization reference, and the DDCt analysis was described in the Methods.

Reviewer #2 (Recommendations for the authors):

(1) The effects of IMQ in Figure 1B are very small. I recommend adding an orthogonal approach to support that mitochondrial Ca is involved.

We sincerely thank the reviewer for this thoughtful and constructive comment. We agree that the increase in the Rhod-2 signal observed following IMQ stimulation is quantitatively modest. However, we respectfully believe that the biological significance of this observation should not be judged solely by the magnitude of the fluorescence change. Rather, the increase in mitochondrial Ca²⁺ should be interpreted in the context of the multiple independent functional assays presented throughout Figure 1, all of which consistently support a role for mitochondrial Ca²⁺ in IMQ-induced inflammatory responses.

First, we demonstrated that IMQ stimulation significantly increased intracellular ROS production, as assessed by CellROX staining (Figure 1C), and that this increase was significantly suppressed by pretreatment with 2-APB, suggesting that Ca²⁺ dysregulation functionally contributes to ROS generation. In addition, 2-APB markedly reduced IL-1b secretion (Figure 1D), further supporting a functional link between Ca²⁺ signaling and inflammasome activation.

Second, IMQ stimulation induced mitochondrial dysfunction, as demonstrated by JC-1 staining (Figure 1G), and significantly increased mitochondrial ROS production, as measured by MitoSOX (Figure 1H). These findings indicate that IMQ triggers a cascade of mitochondrial events extending beyond the modest increase in mitochondrial Ca²⁺, ultimately resulting in oxidative stress and mitochondrial damage.

Furthermore, treatment with the mitochondria-targeted antioxidant MitoQ, as well as the antioxidants GSHEE, NAC, and PDTC, significantly suppressed IMQ-induced IL-1b secretion (Figures 1I and 1K), supporting the conclusion that mitochondrial ROS is a critical downstream mediator of IMQ-induced inflammatory signaling.

Taken together, these complementary findings provide multiple independent lines of evidence supporting a role for mitochondrial Ca²⁺-associated signaling in IMQ-induced inflammation. Although the increase in Rhod-2 fluorescence was relatively modest, it was consistently accompanied by mitochondrial ROS generation, mitochondrial dysfunction, and inflammasome activation. We therefore believe that the biological significance of mitochondrial Ca²⁺ is best evaluated in the context of these convergent functional outcomes rather than by the magnitude of the Rhod-2 signal alone.

We agree that an independent approach for measuring mitochondrial Ca²⁺ would further strengthen this conclusion. However, because several complementary functional assays consistently support the involvement of mitochondrial Ca²⁺-associated mitochondrial dysfunction in IMQ-induced inflammatory responses, we believe that the current data collectively provide strong evidence for the proposed mechanism.

(2) Figure 7E-G would benefit from testing effects of IMQ versus RSQ on observed phenotypes to confirm that they are mediated by Gelsolin-IMQ interaction but not an effect of Gelsolin on TLR7-mediated inflammation.

We sincerely thank the reviewer for this valuable suggestion. We agree that it is important to determine whether the observed phenotypes reflect a specific interaction between Gelsolin and IMQ rather than a general role of Gelsolin in TLR7-mediated signaling.

In response to this comment, we performed additional experiments using resiquimod (RSQ), a TLR7/8 agonist. Gelsolin-deficient MEFs were stimulated with RSQ, and the same parameters analyzed in the IMQ experiments were evaluated.

Unlike the phenotypes observed following IMQ stimulation, RSQ stimulation did not reveal significant differences between wild-type and Gelsolin-deficient MEFs. Specifically, the Xbp1s/Xbp1 ratio was comparable between the two genotypes following RSQ stimulation. Similarly, mitochondrial ROS production, assessed by MitoSOX staining, and MAM formation, evaluated by proximity ligation assay (PLA), were not significantly altered by Gelsolin deficiency under RSQ stimulation.

Although the IMQ and RSQ experiments were performed independently and were not intended as a direct side-by-side quantitative comparison, the absence of genotype-dependent effects in the RSQ experiments indicates that Gelsolin deficiency alone does not generally enhance TLR7-mediated responses. Instead, these findings support the interpretation that the enhanced UPR activation, mitochondrial ROS production, and MAM formation observed in Gelsolin-deficient cells are specific to IMQ stimulation, consistent with the interaction between Gelsolin and IMQ.

Accordingly, the Results section has been revised to include these additional experiments, and the corresponding data have been incorporated into the revised Figure S11.

Changes made in the manuscript: See Figure S12

- Additional experiments using RSQ-stimulated wild-type and Gelsolin-deficient MEFs were performed.

- The Xbp1s/Xbp1 ratio, mitochondrial ROS production, and MAM formation were evaluated following RSQ stimulation.

- No significant genotype-dependent differences were observed under RSQ stimulation, supporting the specificity of the phenotypes observed following IMQ stimulation.

eLife Assessment

This important study addresses a discrepancy between population-level growth laws and single-cell correlations. It shows, for flagellar and synthetic genes in E. coli, that while gene expression of certain genes reduces population-average growth, expression levels positively correlate with growth at the single-cell level. The measurements are convincing, and the proposed mechanism - inheritance of growth factors such as ribosomes during asymmetric division - can explain this observation.

Reviewer #1 (Public review):

Summary:

Garcia-Alcala, Kratz and Cluzel investigate to what extent our understanding of bacterial physiology in bulk experiments can be applied to single-cell observations. They find that intrinsic noise may be powerful enough to even inverse the trends found in the bulk. The authors hypothesize that asymmetric distribution of ribosomes to daughter cells during the cell division plays the dominant role in the intrinsic noise and is able to generate the observed phenomenon. They do not show it directly, but the data and its agreement with the model suffice to support this claim.

Strengths:

The experimental part is convincing: the positive correlation between the elongation rate and promoter activity of unnecessary protein is clear, as well as the negative correlation between the mean values while changing the promoter strength. This was demonstrated in both rich and poor media. The causality between the growth rate and the promoter activity was shown using the negative lag time of the cross-correlation function. A simple, reasonable model accounts well for the data. This paper demonstrates an interesting phenomenon and provides a plausible theory for it, advancing our understanding of bacterial physiology on the single-cell level.

Weaknesses:

(1) Mean-reversion timescales were assumed to be longer than the simulation time and much longer than the cell cycle time. It is not clear whether the results robust in case mean-reversion timescales become of the order of cell cycle or smaller. If not, is there an argument for such practically infinite reversion timescales?

(2) It is not easy to understand the simulation part unless one reads Ref. [14]. Is k(t) assumed to follow Eq. (1) from ref. [14]? Is this crucial that the ribosome noise appears only at the division? The ribosome noise strength \sigma_R=0.06 - is it lower or higher than the naively expected binomial division?<br /> Also, more intuitive explanation of the Simpson paradox would help the reader.

(3) It would be useful for the reader to see the raw data and not only the filtered one to appreciate the measurement noise level.

(4) Negative lag time of the cross-correlation function is visible, but consider adding statistical test for it.

(5) Can you make similar cross-correlation plots using the model? Can you infer using it whether the data agrees better with the assumption that ribosomes noise appear only at division or continuous fluctuations during the cell cycle?

Comments on revised version:

The authors addressed the five comments listed above.

Reviewer #2 (Public review):

Summary:

The manuscript by Garcia-Alcala et al. reports an interesting paradox: the cost of gene expression slows the population-average growth rate, whereas at the single-cell level, expression levels from these genes positively correlate with the growth rate. The effect is observed in the expression of flagellar genes and a gene under a synthetic promoter in E. coli. The findings are explained by the inheritance of growth factors, including ribosomes, during asymmetric division.

Strengths:

(1) The manuscript adds strength to an emerging body of literature showing that the population-level bacterial growth laws do not match correlations based on single-cell data. The evidence presented here is more striking than in previous works (such as Pavlou et al., Nat. Commun. 2025), as the trends in population-level data and single-cell data are reversed.

(2) A relatively simple model correctly explains the trends in the data.

The findings raise an interesting question of whether similar effects occur in other bacterial species and, more broadly, in other organisms.

Comment on latest version:

The additional analysis has strengthened the conclusions.

Author response:

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

Public Reviews:

Reviewer #2 (Public review):

(1) The differing behavior of the MG1655 and MC4100 strains remains a lingering question concerning the generality of the conclusions. It appears unlikely that ribosomes or other growth factors partition significantly differently in the MC4100 strain than in the MG1655 strain. Furthermore, based on Fig. S15, it is still unclear to what extent MC4100 exhibits growth-rate fluctuations, as stated in the text, rather than primarily size fluctuations, as shown in the figure. It is also unclear why such very slow fluctuations would lead to qualitatively different behavior, given that the proposed mechanism appears to be rather fundamental. It would be helpful for the authors to discuss these two points.

We thank the reviewer for revisiting this point. Here, we re-examined the MC4100 data in more detail and found that our original analysis was inaccurate; we now clarify this below along with new supporting analyses.

We agree that there is no a priori reason for ribosome or growth-factor partitioning to differ between MC4100 and MG1655, and our expanded analysis now supports this directly in Fig.S15.

Using the Class-1 promoter of the flagellar cascade in MC4100, which behaves under our conditions as a quasi-constitutive promoter, we find a positive correlation between instantaneous elongation rate and promoter activity that is comparable in magnitude to MG1655 (Fig.15C). We further analyzed publicly available data from two independent studies of strains expressing a constitutive fluorescent protein (new Fig.S18): Tanouchi et al. [44, 48], who tracked MC4100 at 25°C and 37°C, and Wang et al. [33], who tracked MG1655 and B/r strains. In these datasets, we found the same positive coupling between instantaneous elongation rate and expression, consistent with what we observe in MG1655. Together, these results indicate that the short-timescale coupling between growth-factor availability and gene expression that underlies our proposed mechanism is not strain-specific and is present in MC4100 for constitutively expressed and Class-1 activity.

On the nature of MC4100's slow fluctuations: We thank the reviewer for pointing out that Fig. S15 did not distinguish growth-rate from size fluctuations. We have now computed the autocorrelation function of elongation rate for both strains and added it to Fig. S15. This analysis shows that MC4100's characteristic oscillation is present in cell size but is absent from the elongation-rate autocorrelation. We have revised the text accordingly to state that MC4100 displays long-timescale oscillations in cell size, rather than describing this as a growth-rate phenomenon.

On why MC4100 does not show coupling between elongation rate and flagellar Class-2 activity despite this coupling being present at Class-1: In MC4100, the positive correlation between elongation rate and promoter activity, comparable to MG1655 at Class-1, is markedly attenuated at Class-2. Since both promoters are measured from the same cells and time series, this rules out our first assumption, a generic masking effect, and instead localizes the discrepancy to the Class-1-to-Class-2 step of the flagellar cascade, the pulse-generating switch we and others have described previously (Sassi et al., 2020, [24]). We do not have data to determine the molecular basis of this attenuation and present it as an open question.

(2) It is unclear what fraction of the total proteome mVenus represents in different measurements. Adding this information would strengthen the conclusions.

We agree that a direct proteomic quantification (e.g., Coomassie staining or mass spectrometry) would be the most direct way to determine the fraction of the proteome occupied by mVenus. However, we are no longer in a position to carry out such experiments.

As in our original response, our elongation-rate reductions (1.3-9.3% across our promoter series; see Table S3) remain far smaller than the 67% reduction associated with ~27% proteome occupancy reported by Scott et al. [6], making it unlikely that mVenus approaches such an extreme fraction in our system.

Now we used a validated quantitative model relating relative growth-rate reduction to unnecessary-protein fraction, built on the same ribosome-allocation theory as Scott et al. and empirically calibrated specifically for a GFP-family fluorescent protein (Bienick et al., 2014, PLoS ONE [59]). This model predicts μ/μ_max = 1 - b·ɸ_U, with b = 2.33 µg dry cell weight (DCW) per µg protein determined for eGFP across multiple growth media. Applying this relationship to our own elongation-rate data, using the growth rate of our non-expressing WT strain as μ_max, we estimate that mVenus constitutes approximately 0.6-4.0% of dry cell weight across our promoter series, reaching ~4.0% in our strongest-expressing strain, P5.

While this remains a model-based estimate rather than a direct proteomic measurement and involves some extrapolation across growth media and strain background relative to the original Bienick et al. study, both independent approaches converge on the same conclusion: mVenus occupies a modest fraction of the proteome in our experiments, well below the f_U = 14.4% upper value explored in our simulations. This supports our original framing of f_U = 14.4% as a conservative exploratory upper bound rather than an underestimate of experimental burden, and we have added this quantitative estimate (Table S3) to the revised manuscript to strengthen this point, as suggested.

eLife Assessment

This valuable study examines how the rodent prelimbic cortex represents learned and generalized threat over time and identifies distinct stable and dynamic neuronal populations that contribute to these representations. The evidence is convincing, supported by longitudinal calcium imaging, appropriate control groups, and sophisticated analyses showing that the relevant neural signals cannot be explained simply by freezing behavior. The work provides a conceptual framework for understanding how stable threat-related representations supporting memory generalization and discrimination can be maintained despite ongoing changes in neuronal ensemble composition.

Reviewer #1 (Public review):

[Editors' note: this version has been assessed by the Reviewing Editor without further input from the original reviewers. We appreciate the care with which the authors have addressed the remaining concerns. The additional analyses and the revisions to the framing and interpretation have strengthened the manuscript and clarified several of the issues raised during the previous round of review. In particular, the added analyses in Figure 4 and the more precise treatment of repeated retrieval, learned threat value, and the relationship between neural activity and freezing have improved the paper substantially.]

Summary:

The authors combine discriminative auditory fear conditioning with longitudinal in vivo calcium imaging to ask how prelimbic (PL) representations of learned and generalized threat evolve across recent and remote memory time points. Using two different CS+ frequencies and a no-shock control group, they report that PL population activity tracks graded behavioral generalization, that population similarity is highest for tones eliciting strong threat responding, and that distinct subnetworks can be identified that appear to encode tone-specific sensory features versus learned threat-related response structure.

To my knowledge, this may be the first study to comprehensively examine neural encoding of fear generalization in prelimbic cortex (PL). The manuscript is ambitious and technically interesting, and several aspects are potentially important. In particular, the suggestion that neurons showing graded, learning-related response patterns become selectively stabilized over time is intriguing. The inclusion of two CS+ training conditions and a no-shock control also strengthens the case that at least some of the reported effects are related to associative learning rather than simple sensory differences.

Reviewer #3 (Public review):

Summary:

Normandin et al. explore the coding of stimuli predicting an aversive event in the prelimbic cortex. Stimuli could either be explicitly paired, explicitly unpaired, or novel but with an inferred association with the aversive event (generalization). Long-term tracking of GCaMP positive neurons allowed them to examine how coding evolves out to a month following training. In general, they found two types of ensemble codes. One was ensembles coding for each stimulus independently, but with enhanced responding to the one eliciting a freezing response. The other was ensembles that responded to all stimuli in proportion to their similarity to the stimulus paired with the aversive event, either increasing or decreasing their activation with the degree of freezing elicited by a stimulus. Importantly, this second set of ensembles was more stable across days, potentially providing a memory trace.

Strengths:

(1) The authors track ensembles in prelimbic cortex over long time scales, providing valuable information on the consolidation of neural codes.

(2) Neural coding of generalization is examined, which is under examined in the field.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

The authors combine discriminative auditory fear conditioning with longitudinal in vivo calcium imaging to ask how prelimbic (PL) representations of learned and generalized threat evolve across recent and remote memory time points. Using two different CS+ frequencies and a noshock control group, they report that PL population activity tracks graded behavioral generalization, that population similarity is highest for tones eliciting strong threat responding, and that distinct subnetworks can be identified that appear to encode tone-specific sensory features versus learned threat-related response structure.

To my knowledge, this may be the first study to comprehensively examine neural encoding of fear generalization in prelimbic cortex (PL). The manuscript is ambitious and technically interesting, and several aspects are potentially important. In particular, the suggestion that neurons showing graded, learning-related response patterns become selectively stabilized over time is intriguing. The inclusion of two CS+ training conditions and a no-shock control also strengthens the case that at least some of the reported effects are related to associative learning rather than simple sensory differences. However, in its current form, the manuscript does not yet fully support the strength of the conceptual claims. Several issues limit confidence in the interpretation, including the possibility that repeated testing itself contributes to changes across days, uncertainty about the relationship between neural activity and freezing behavior, limited quantitative documentation of longitudinal cell registration, and a number of problems in figure clarity and statistical framing. Overall, the study contains promising observations, but the claims should be narrowed, and several analyses or controls would be needed to fully support the proposed framework.

Comments on revised version.

The authors have addressed my previous concerns well, and the revised manuscript is substantially improved. In particular, the additional analyses strengthen the conclusion that prelimbic cortical activity reflects learned threat value rather than simply freezing behavior, while the revised framing and additional controls clarify the interpretation of the longitudinal neural dynamics. This paper represents an important contribution to our understanding of the neural mechanisms supporting aversive learning, memory, and generalization.

We thank Reviewer 1 for his/her constructive comments, which significantly contributed to strengthen our conclusions.

In response to the reviewer’s recommendations, we added two new analyses to Fig. 4, presented in Fig. 4c–g.

Reviewer #2 (Public review):

The authors have substantially revised the paper in response to the original review, which is greatly appreciated. It is clear that it will eventually make a nice contribution to the literature. This being said, the following points are somewhere between major and minor in term of their implications for interpretation of the study results. If they were to be addressed, the paper would be again improved.

We thank Reviewer 2 for the careful second review, which helped us sharpen our arguments and improve the manuscript. The reviewer’s additional comments prompted us to refine the scope and precision of several interpretations. Accordingly, we have removed or clarified potentially confusing language, reframed the longitudinal findings in terms of repeated retrieval rather than the passage of time, and explicitly acknowledged the limitations of relying exclusively on freezing as a behavioral measure. We now also recognize repeated nonreinforced testing as the most direct explanation for the sharpening of the generalization gradients and the responses of newly recruited neurons, while clarifying below how we view this additional learning as contributing to memory updating. We believe these revisions have substantially improved the manuscript, and we are grateful for the reviewer’s thoughtful and detailed feedback.

There are a few remnants of the past language that are not helpful for the interpretation of the study results: 1) "Specifically, the observed population gradients could emerge either from the pooled activity of frequency-selective neurons that respond to individual tones or from neuronal subpopulations that integrate information across tones to encode their learned threat-value."; and 2) "Together, these findings suggest that the PL integrates sensory similarity with learned threat value to generate stable representations that support adaptive generalization and discrimination." Neither of these statement follows what has been shown in the study, even with inclusion of the results from the GLM analysis (see point 4 below).

We directly address this point in response to the reviewer’s point 4

(1) This paragraph in the Discussion is difficult to follow: "Generalization has traditionally been explained by perceptual similarity (Shepard, 1987), whereby stimuli resembling a conditioned cue recruit overlapping sensory representations and evoke similar behavioral responses (Corches et al., 2019; Grosso et al., 2018). Although perceptual similarity clearly influences the extent of generalization, accumulating evidence indicates that it cannot fully account for generalized responding (Verra et al., 2026). More recent frameworks propose that associative learning assigns learned value to novel stimuli by integrating their sensory similarity with previous experience, allowing behavior to scale according to predicted biological significance (Verra et al., 2026; Zaman et al., 2023). Our findings provide a neural framework consistent with these ideas. Sensory similarity promoted consistent neuronal population responses across tones, whereas associative learning organized these responses into graded representations that tracked learned threat value across the stimulus continuum. Thus, sensory similarity appears to define the neuronal substrate upon which associative learning constructs value-based representations that support graded behavioral generalization."

While the revisions have removed the many unnecessary references to inference and integration, this paragraph seems like it is adhering to the original idea of how the authors wished to present their work. If the authors wished to talk about something more than perceptual similarity in the context of generalization, they should have used a task that lends itself to a more-than-perceptual-similarity explanation. Again, the inclusion of the GLM analysis is suggestive for some of what the authors wish to say, but doesn't justify the statements that: "Sensory similarity promoted consistent neuronal population responses across tones, whereas associative learning organized these responses into graded representations that tracked learned threat value across the stimulus continuum." In short, the analysis does not substitute for the design that could have and should have been used to assess learned threat value independently of sensory similarity.

We thank the reviewer for this comment, which helped us identify ambiguity in our terminology. By “learned threat value,” we did not intend to imply that the PL independently infers or computes the value of each novel tone, separate from perceptual similarity. Rather, we used this term to denote the associative significance acquired by the CS+ and CS− during conditioning. Novel cues may then be evaluated according to their perceptual similarity to these learned associations. We have now defined “learned threat value” when it first appears in the manuscript.

Furthermore, we agree that perceptual similarity can account for the graded generalization of responses from the CS+ to neighboring frequencies. We therefore do not consider learned associations and perceptual similarity to be competing explanations. Instead, conditioning determines which stimulus anchors the gradient and its direction according to their acquired “threat value”, whereas perceptual similarity governs how the response extends across intermediate frequencies. This interpretation is supported by our reversed conditioning design: the same frequency continuum produced opposite neural gradients depending on whether 3 or 15 kHz served as the CS+, and no gradients emerged in control animals exposed to the same tones without conditioning. Thus, the physical relationships among the tones shape the graded response, but mnemonic experience determines its organization along the frequency continuum.

The GLM analysis was not intended to demonstrate threat value independently of sensory similarity. Rather, it showed that the learning-dependent gradient remained after accounting for freezing and therefore could not be explained solely by this behavioral response (we address the point of other potential fear responses below).

“Generalization has traditionally been explained in terms of perceptual similarity (Shepard, 1987): stimuli resembling a conditioned cue recruit overlapping sensory representations and therefore evoke similar behavioral responses (Corches et al., 2019; Grosso et al., 2018). More recent frameworks propose that responses to novel stimuli depend not only on sensory similarity but also on mnemonic representations of learned threat value, allowing behavior to scale with the predicted significance of each stimulus (Verra et al., 2026; Zaman et al., 2023). This mnemonic contribution should be especially important when generalization is assessed long after conditioning because responding to a novel cue requires retrieval of the associations formed during learning. Our design did not manipulate sensory similarity and learned threat value independently. However, the reversed conditioning procedure dissociated them in one respect: depending on whether 3 or 15 kHz served as the CS+, the neural gradients ran in opposite directions along the same frequency continuum, with each anchored to the threat-associated tone. A gradient determined by spectral features alone would have run in the same direction in both groups. Thus, the learned associations and their mnemonic representations must have determined the anchor and direction of the neural gradient. By contrast, the contribution of sensory similarity is inferred rather than directly demonstrated: intermediate tones were represented in an order that followed their spectral distance from the CS+. Because discriminative conditioning tends to narrow generalization gradients (Dunsmoor & LaBar, 2013; Herzog et al., 2021; Jenkins & Harrison, 1960; Lommen et al., 2017), tracking neural representations over 30 days allowed us to examine how PL populations evolved as behavioral discrimination became progressively more precise during repeated retrieval. Whereas stable neuronal populations retained consistent response profiles across retrieval sessions, neurons recruited after conditioning exhibited changes that paralleled the behavioral sharpening. These results suggest that memory, new learning, and sensory similarity interact to shape generalization gradients.”

(2) The next paragraph in the Discussion is also confusing. "Such reorganization has been proposed to provide flexibility by allowing new information to be incorporated into existing cortical representations while preserving stable behavioral performance (Mau et al., 2020; Zaki & Cai, 2024). Several mechanisms could contribute to this turnover, including systems consolidation, retrieval-induced reconsolidation or memory updating, and repeated nonreinforced stimulus exposure (Lacagnina et al., 2019; Mau et al., 2020; Sangha, 2015; Zaki & Cai, 2024). Although our experiments cannot distinguish between the first two possibilities, the behavioral data argue against extinction as the primary explanation. Extinction is generally associated with the formation of new CS+-safety associations (Bouton et al., 2021), whereas discrimination ratios increased across retrieval sessions, indicating that animals progressively improved their discrimination between threat-associated and safe stimuli rather than acquiring generalized safety responses. This pattern is consistent with previous work showing that discrimination learning sharpens stimulus representations and narrows behavioral generalization gradients (Dunsmoor & LaBar, 2013; Herzog et al., 2021; Jenkins & Harrison, 1960; Lommen et al., 2017). Importantly, turnover was not uniform across the population. Graded neurons retained remarkably consistent response profiles across retrieval sessions, and their activity remained more strongly associated with learned threat value than with freezing behavior. These observations indicate that stable components of the population code can coexist with extensive reorganization of surrounding neuronal ensembles."

The issue with repeated testing is not caused by extinction per se. The issue is that nonreinforcement across the repeated testing should differentially affect the CS+ and CS-. Specifically, it should extinguish responding to the CS- stimulus at a rate that matches its distance from the CS+, thereby sharpening the CS+ versus CS- discrimination in precisely the ways that have been observed. Ergo, the repeated testing is a problem for inferences that might be drawn about the way that generalization gradients change with; and is a problem for statements regarding "dynamic reorganization of cortical activity patterns over time." There is nothing in the study that allows one to comment on the reorganization of cortical activity patterns over time. The reorganization can and should be attributed to the repeated testing, which is confounded with time. Nonetheless, the reorganization must be due to the repeated testing and NOT time as the present findings are inconsistent with the well-documented broadening of generalization gradients with time.

We agree with the reviewer that discrimination between the CS− and CS+ sharpened across retrieval sessions and that repeated testing may have contributed to this effect. Our discussion of extinction was included specifically to address a concern previously raised by Reviewer 1 and to clarify that the observed sharpening did not reflect a uniform reduction in conditioned responding. We now only left this explanation in the results section.

We also agree that later retrieval sessions are not passive readouts of the original memory. Repeated presentation can provide new opportunities for learning, update reactivated memory traces, and initiate reconsolidation. The intermediate tones illustrate this point particularly well: they are novel during the first retrieval session but become familiar through subsequent exposure, and their representations may therefore change across sessions. Thus, new learning, memory updating, and reconsolidation are not mutually exclusive explanations but interacting processes engaged by repeated retrieval. We have revised the Discussion to acknowledge these contributions more explicitly.

We also agree that our use of phrases such as “over time” was imprecise. We have replaced this language with “across retrieval sessions” to avoid implying that the passage of time alone produced ensemble turnover.

However, we respectfully disagree that cortical reorganization cannot be evaluated across repeated retrieval sessions or that repeated testing alone necessarily accounts for all the observed changes. Multiple studies have documented turnover within cortical ensembles following learning (Lacagnina et al., 2019; Mau et al., 2020; Sangha, 2015; Zaki & Cai, 2024). Importantly, we observed ensemble turnover by test day 1, before repeated testing could have exerted a cumulative effect, and similar early turnover has been reported by other laboratories (Kitamura et al., 2017; DeNardo et al., 2019). These previous studies have also interpreted changes in ensemble composition between conditioning and subsequent retrieval sessions, including remote retrieval, as evidence of cortical reorganization. Our paradigm differs from these studies because we introduced novel tones to examine how representations of the original CS+/CS− associations interact with representations of perceptually similar cues.

In summary, we agree with the reviewer that repeated testing may generate additional learning that contributes to the sharpening of behavioral generalization gradients and the responses of newly recruited neurons. However, we view this learning as inseparable from memory updating and reconsolidation, because information acquired during retrieval must be incorporated into existing memory representations to persist across sessions.

“The ensemble turnover observed here is consistent with previous studies demonstrating dynamic reorganization of cortical activity patterns across temporally separated retrieval sessions (DeNardo et al., 2019; Gallego et al., 2020; Kitamura et al., 2017; Tome et al., 2024). Such reorganization has been proposed to provide flexibility by allowing new information to be incorporated into existing cortical representations while preserving stable behavioral performance (Mau et al., 2020; Zaki & Cai, 2024). Several processes could contribute to this turnover, including additional learning during repeated nonreinforced testing, memory updating, and reconsolidation (Lacagnina et al., 2019; Mau et al., 2020; Sangha, 2015; Zaki & Cai, 2024). In our experiments, turnover was already evident at the first retrieval session, before repeated testing could have exerted a cumulative effect, indicating that this reorganization emerges early after learning. Nevertheless, repeated testing provides a plausible explanation for changes during subsequent sessions. Each retrieval session reactivated the original CS+/CS− associations while presenting the conditioned and intermediate tones without reinforcement, thereby creating opportunities for additional discrimination learning. These experiences may have progressively sharpened differentiation between the CS+ and CS-, modifying the retrieved memory representations and changing which neurons participated in representing the refined associations. Although our data do not establish a mechanistic link between neuronal turnover and additional learning, they raise the possibility that dynamic ensemble membership provides the flexibility needed to incorporate new information.”

(3) In the next paragraph, the authors state: "At the same time, narrower generalization gradients and improved discrimination across retrieval sessions suggests ongoing memory updating. These observations are consistent with contemporary theories proposing that systems consolidation and retrieval-dependent updating are complementary processes through which memories continue to evolve after learning (Mau et al., 2020; Tome et al., 2024; Zaki & Cai, 2024)."

In general, I'm not sure why one would invoke systems consolidation or retrieval-induced reconsolidation as an explanation for any of the present findings: they are not explanations of much at all. In this specific text, the authors seem to be implying an updating process that occurs independently of what is learned across the repeated sessions of testing. Why? The changes that occur in the behaviour and neuronal representations are perfectly explicable in terms of additional learning that occurs - of the sort that I hope to have made clear in my previous comment. Why invoke more than what is needed to explain the observed pattern of results?

We appreciate the reviewer’s clarification. As discussed in our response to the preceding comment, we agree that repeated nonreinforced testing provided additional learning opportunities and offers the most direct explanation for the progressive sharpening of behavioral discrimination and neuronal responses. We recognize that our original wording could have been interpreted as proposing memory updating as a process occurring independently of learning during the test sessions. This was not our intention. By “memory updating,” we meant that new information acquired during repeated retrieval modified the existing representations of the CS+ and CS−, allowing these stimuli to become more clearly differentiated. Thus, the additional learning that occurs through repeated testing provides the experience through which the original associations are refined.

We agree that systems consolidation and retrieval-induced reconsolidation are not required as direct explanations for the observed sharpening and that our design cannot isolate their contributions. However, ensemble turnover was evident by day 1, before repeated testing could have exerted cumulative effects, indicating that repeated testing cannot fully explain the turnover. We view the additional learning acquired during subsequent retrieval sessions as refining the represented values of the CS+ and CS− and, if these changes persist, as requiring incorporation into existing memory representations through updating and reconsolidation. These processes therefore complement, rather than compete with, additional learning. The revised Discussion distinguishes repeated testing as the most direct explanation for the sharpening of discrimination from the broader memory processes that may accompany this learning and contribute to cortical ensemble reorganization.

“In summary, PL population responses formed generalization gradients that paralleled behavioral generalization and were primarily organized according to tone-learned threat value. The overlap among responses to conditioned and novel tones was consistent with their perceptual similarity, whereas repeated nonreinforced testing was accompanied by progressive sharpening of both behavioral discrimination and the response gradients expressed by neurons recruited after conditioning. Together, these findings provide a potential neural framework through which stored threat associations may guide the evaluation of perceptually similar cues.”

“The coexistence of these stable neurons with dynamic ensembles may allow repeated retrieval to refine a memory while preserving core features of its original representation (Mau et al., 2020; Tome et al., 2024; Zaki & Cai, 2024). Determining whether these stable graded neurons are causally required for memory storage or retrieval—and whether they constitute a persistent cortical memory trace—will require longitudinal imaging combined with selective manipulation of this population.”

(4) Re the GLM analysis - The authors write that: "the fact that the GLM analysis indicates that these neurons reflect learned threat value more than freezing behavior, suggests that they encode an abstract property of the learned stimulus rather than simply mirroring behavioral output."

This is fine if freezing fully indexes the state of conditioned fear and there are no other behaviours in which animals express their fear. If, however, fear is expressed in a range of other behaviours that are likely coordinated by the PL (e.g., startle, vigilance, scanning, orienting to source of danger), this interpretation of the GLM analysis is unwarranted. This is an important point and would be worth noting somewhere in the paragraph where the statement appears.

We agree with the reviewer. Our GLM demonstrates that the graded neuronal responses cannot be explained by freezing behavior alone, but it does not exclude contributions from other unmeasured manifestations of conditioned fear, including vigilance, scanning, orienting, startle, or physiological responses. We have therefore removed the claim that these neurons primarily encode threat value and revised the Discussion to acknowledge this limitation explicitly.

“Freezing, however, does not exhaust the conditioned defensive state, and we cannot rule out contributions from unmeasured behavioral or physiological correlates of fear, including vigilance, scanning, orienting, startle, and changes in autonomic state. Our findings are therefore consistent with PL neurons representing the learned significance of the stimuli, but they do not establish that this representation is independent of all fear-related behavioral and physiological states.”

Reviewer #3 (Public review):

Summary:

Normandin et al. explore the coding of stimuli predicting an aversive event in the prelimbic cortex. Stimuli could either be explicitly paired, explicitly unpaired, or novel but with an inferred association with the aversive event (generalization). Long-term tracking of GCaMP positive neurons allowed them to examine how coding evolves out to a month following training. In general, they found two types of ensemble codes. One was ensembles coding for each stimulus independently, but with enhanced responding to the one eliciting a freezing response. The other was ensembles that responded to all stimuli in proportion to their similarity to the stimulus paired with the aversive event, either increasing or decreasing their activation with the degree of freezing elicited by a stimulus. Importantly, this second set of ensembles was more stable across days, potentially providing a memory trace.

Strengths:

(1) The authors track ensembles in prelimbic cortex over long time scales, providing valuable information on the consolidation of neural codes.

(2) Neural coding of generalization is examined, which is under examined in the field.

Comments on revised version.

The authors have convincingly and thoroughly addressed my concerns. I have no further issues regarding this study.

We thank reviewer 3 for his thoughtful and constructive comments and the suggestion to use the GLM which greatly improved the interpretation of our data.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

One small point is that the authors could report the beta coefficients for the tone and freezing predictors from the GLM analysis shown in Figure 4. Providing these values would make it easier to directly compare the relative contributions of tone-related and freezing-related activity to the model.

We now include this analysis in Figure 4c and 4g

eLife Assessment

This study presents a valuable human organoid platform for investigating neuron-immune interactions in Alzheimer's disease and modeling the interplay between innate and adaptive immunity in the context of amyloid pathology. The system has the potential to advance the field by enabling the study of human-specific neuroimmune interactions that is difficult to recapitulate in rodent models. The evidence on the microglia-T cell crosstalk are convincing. The study will interest researchers in neuroimmunology and Alzheimer's disease.

Reviewer #2 (Public review):

Summary:

In this study, the authors developed a human forebrain organoid model that incorporates both iPSC-derived microglia and CD8⁺ T cells, allowing them to recreate and investigate multicellular aspects of AD pathology in a human-relevant system.

Their findings show that microglia help clear amyloid-β deposits, but they also promote inflammatory responses. Activated microglia recruit CD8⁺ T cells by releasing the chemokines CCL4, CCL5, and CXCL10, which signal through the receptors CCR1/CCR5 and CXCR3. Pharmacological inhibition of CCR5 or CXCR3 prevents T-cell recruitment and alters autophagy pathways in a microglia-dependent manner.

Strengths:

The manuscript has several strengths, including its innovative multicellular organoid model, the combination of complementary experimental approaches, and the identification of potentially relevant immune signaling pathways.

Comment on the revised version.

Overall, the revised manuscript is considerably improved, and the major conceptual concerns raised in the initial review have been adequately addressed.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

A growing body of evidence indicates that Alzheimer's disease is not simply a disease of neurons accumulating toxic protein aggregates, but one in which the immune system, both its resident brain component and its circulating peripheral arm, plays an active and sustained role. Understanding how these two immune compartments interact with one another and with diseased neural tissue has been hampered by the fact that the mouse immune system differs fundamentally from the human one in ways likely to matter for disease progression. The authors set out to address this gap by building a modular laboratory model that brings together three human cell types in a three-dimensional setting: brain organoids derived from human stem cells to provide a neural substrate, stem cell-derived brain immune cells (microglia) to represent the resident immune compartment, and circulating immune cells (CD8-positive T cells) harvested from human blood to represent the peripheral adaptive immune response. By exposing this tri-cellular system to a toxic form of amyloid protein, the hallmark aggregating molecule of Alzheimer's disease, the authors aimed to dissect, step by step, how microglia respond to amyloid stress, what inflammatory signals they release as a consequence, and whether those signals are sufficient to attract T cells into the neural environment. They further aimed to test whether blocking the molecular receptors that guide T cell movement could interrupt this process, with the broader goal of positioning the platform as a tool for human-relevant drug screening.

Strengths

The conceptual architecture of the platform is one of its clearest strengths. The decision to add immune components in a stepwise, modular fashion, first characterising the neural response to amyloid, then adding microglia, then adding T cells, makes it possible to attribute observed changes to specific cellular contributions in a way that a more complex all-at-once model would not allow. This staged design is well thought-through, and its logic is clearly communicated. The combination of single-cell transcriptional profiling, calcium imaging for real-time functional readouts, transwell migration assays, and protein secretion measurements gives the study a genuinely multi-modal character that goes beyond what purely transcriptomic or purely imaging-based approaches can offer. The observation that T cells failed to migrate toward amyloid-treated organoids in the absence of microglia is a clean and conceptually important result, clearly supporting the idea that the resident immune response acts as an intermediary between amyloid pathology and the recruitment of peripheral immune cells. The identification of specific chemokine receptor pathways mediating T cell movement and the demonstration that pharmacological blockade of those receptors reduces migration and provide a degree of mechanistic resolution useful for thinking about future therapeutic strategies.

Weaknesses

Despite these strengths, several aspects of the work as presented substantially limit the confidence one can place in its conclusions.

The most consequential issue concerns the origin of the cells used in the model. The three cellular components: the brain organoids, the microglia, and the T cells are derived from genetically unrelated individuals. The T cells, in particular, come from healthy blood donors unrelated to the stem cell lines used to generate the neural tissue. This means the immune cells and the tissue they are interacting with carry different molecular identity markers (the proteins that the immune system uses to distinguish self from non-self). In this setting, any T cell activation or directed movement could reflect a generic rejection-like response to foreign tissue rather than a disease-relevant, chemokine-directed recruitment process. This is not a subtle concern: it represents a fundamental ambiguity at the heart of the model's central finding, and it is not acknowledged anywhere in the manuscript. For the transwell migration data to be interpretable as a model of Alzheimer's disease rather than of immune incompatibility, the authors would need to demonstrate that migration is driven by the specific chemokine environment and not by the genetic mismatch between cells, for example, using cells from the same donor or from matched donors, or by showing that blocking identity-marker recognition does not alter migration.

A related concern is that the T cells used are from healthy individuals, whereas T cells from people with Alzheimer's disease are known to differ in their activation state, surface receptor expression, and functional behaviour. The platform cannot yet claim to model the specific T cell biology of Alzheimer's disease until disease-relevant T cells are incorporated.

Beyond this foundational issue, the study frequently describes findings in causal terms that the experimental design does not support. The resident immune cells are said to "drive" T cell recruitment and "establish" a feedback loop. These are strong mechanistic claims. The evidence presented indicates that when microglia are present, more T cells migrate, and that blocking T cells receptors reduces migration. What is missing is direct evidence that the specific molecules measured, particularly the chemokines CCL4 and CCL5, are the agents responsible, as opposed to other signals also present in the conditioned environment. No experiment directly neutralises these chemokines to test whether their removal is sufficient to abolish T cell recruitment. Without such an experiment, the receptor-blocking data show only that the receptors matter, not that the measured ligands are the ones activating those receptors.

The abstract describes one particular molecule, CXCL10, as a contributor to T cell recruitment, but the data in the paper itself show no significant change in CXCL10 levels between conditions. This discrepancy between the abstract and the results is misleading to readers who may not read the figures in detail.

The single-cell sequencing data, which form the basis for claims about changes in cell populations following amyloid treatment or microglia addition, are presented without validation of the cell type labels against established reference datasets from human brain tissue. The proportional shifts in cell populations between conditions (Figures 1H and 3E) are described as significant findings but are shown without any statistical test appropriate for this type of compositional data. Comparisons of cell-type proportions derived from single-cell sequencing require specialised statistical approaches that account for the interdependence of proportions and the variability between samples; standard tests are not appropriate here, and none are applied.

There is also an unresolved inconsistency in the age at which the organoids were analysed by single-cell sequencing: the text states day 90, while the figure legend states day 60, and the methods section contains a passage describing experimental conditions (including a cholesterol treatment and a drug called semaglutide) that are entirely unrelated to this study and appear to have been copied from a different manuscript. These issues raise concerns about the rigour of the manuscript preparation and should be corrected.

Finally, the sample sizes underpinning several key conclusions are small (typically three to four organoids per group), particularly for the protein-secretion measurements used to identify the inflammatory signals responsible for T cell recruitment. While organoid studies are inherently limited in scale, the strength of the mechanistic claims made here would benefit from larger sample size or independent experimental replication.

Conclusion:

The authors have built a platform that is conceptually well-conceived and generates data consistent with a role for microglia in bridging amyloid pathology and T cell recruitment. In that sense, they have made meaningful progress toward their stated aims. However, the platform, as described, cannot yet deliver the human-specific mechanistic insight it claims to provide, primarily because the non-autologous configuration of the model introduces an uncontrolled variable that confounds the interpretation of the immune interaction data. The claim to have provided "the first human-specific mechanistic demonstration" of microglial activation as a bridge between amyloid pathology and adaptive immune recruitment is not supported by the evidence presented. The data are consistent with this interpretation but do not establish it.

The general approach, building increasingly complex human neural-immune models by adding components in a controlled, stepwise manner, is a valuable direction for the field and one that other groups working on neuroinflammation will find useful to consider. The combination of live calcium imaging and transcriptional profiling in the same experimental system is a practical contribution that demonstrates the kind of multi-modal readout this class of model can support. If the autologous confound is resolved in future iterations and if the mechanistic claims are grounded in more direct experimental evidence, this type of platform could become a genuinely useful tool for investigating human neuroimmune biology and for screening candidate therapeutic compounds in a human-relevant context. As currently presented, however, readers and researchers considering adopting this approach should be aware that the immune interaction data may reflect genetic mismatches between cell sources rather than disease-specific biology, and that the causal conclusions drawn from the chemokine and migration data go beyond what the experiments can support.

Reviewer #2 (Public review):

Summary:

In this study, the authors developed a human forebrain organoid model incorporating both iPSC-derived microglia and CD8⁺ T cells, enabling them to recreate and investigate multicellular aspects of AD pathology in a human-relevant system.

Their findings show that microglia help clear amyloid-β deposits, but they also promote inflammatory responses. Activated microglia recruit CD8⁺ T cells by releasing the chemokines CCL4, CCL5, and CXCL10, which signal through the receptors CCR1/CCR5 and CXCR3. Pharmacological inhibition of CCR5 or CXCR3 prevents T-cell recruitment and alters autophagy pathways in a microglia-dependent manner.

Strengths:

The study presents a versatile human organoid platform for investigating neuron-immune interactions in Alzheimer's disease. It highlights the critical role of microglia-driven recruitment of CD8⁺ T cells in sustaining neuroinflammation and identifies CCR5 and CXCR3 signaling pathways as promising therapeutic targets for neuroinflammatory conditions.

This study is interesting and presents novel findings supported by state-of-the-art approaches, including single-cell RNA sequencing, a three-dimensional cerebral organoid model, and co-culture systems involving two distinct immune cell populations.

Weaknesses:

Several aspects of the study require clarification and further improvement. For example:

(1) Figure 1H is missing statistical analyses.

(2) The scRNA-seq analysis shows a reduction in the proportion of cells occupying transcriptional states associated with later pseudotime values, which the authors interpret as evidence that Aβ treatment inhibits neuronal maturation. However, the data presented do not appear sufficient to support this conclusion. An alternative explanation is that Aβ preferentially affects the survival of more mature neuronal populations, leading to their depletion, consequently, an apparent enrichment of cells at earlier pseudotime states. Therefore, the observed pseudotime shift does not necessarily demonstrate impaired maturation per se. The authors should revise the interpretation of these results in the first paragraph and either provide additional evidence supporting a maturation defect or discuss alternative explanations such as selective loss of mature neurons.

(3) A similar concern applies to the scRNA-seq data presented in Figure 3. The authors interpret the shift toward later pseudotime states in the presence of microglia as evidence of enhanced neuronal maturation. However, the data do not exclude alternative explanations. For instance, microglia may preferentially promote the survival of more mature neuronal populations or protect them from cell death, thereby increasing their relative abundance in the dataset. Consequently, the observed pseudotime distribution cannot be taken as direct evidence of enhanced maturation. The authors should revise their interpretation accordingly and discuss the possibility that the observed effect reflects differential survival rather than accelerated neuronal maturation.

(4) In Figures 4A-E, the authors should report the levels of the secreted proteins in pg/mL instead of relative values, as this would better reflect the actual amounts produced. In Figure 4H, the inhibitor-treated control T-cell samples should be included. Furthermore, it should be explicitly stated that the inhibitor-treated data points currently shown refer to T cells cultured in the presence of myeloid Aβ.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) Addressing the allogeneic confound

To determine whether observed T cell migration reflects chemokine-driven recruitment rather than allogeneic recognition, the authors should perform one or more of the following: (a) repeat transwell migration assays using HLA-matched donors for T cells and iPSC lines; (b) include a blocking condition using anti-HLA class I antibody to suppress allogeneic recognition and test whether migration is reduced; (c) compare migration toward conditioned media alone (without cells) versus co-culture conditions to establish whether secreted factors are sufficient to drive migration independently of direct cell contact. If HLA-matched material is not currently available, the authors could, at a minimum, use conditioned media transfer experiments to dissociate chemokine-mediated from contact-mediated effects.

We agree this is an important limitation. We have not performed HLA-matched migration assays, anti-HLA class I blockade, or conditioned-media-only migration experiments. We note that in our transwell assay design (Fig. 4G–H), T cells are seeded in the upper chamber and organoids in the lower chamber, separated by a porous membrane; while this precludes direct T cell–organoid cell contact, live organoid/microglial cells are present throughout the assay rather than their conditioned medium alone, so we have not directly tested part (c) as the reviewer describes it.

We would also note that the CD8⁺ T cells used in this assay were derived from a single healthy donor, while the organoids and iMGLs were derived from a separate iPSC line (DYR0100); the same T cell donor and the same organoid/microglial line were used across all conditions (CTR, Aβ42, Aβ42+iMGL). The T cell–organoid pairing is therefore allogeneic, but identical in every condition. Any contribution of allogeneic recognition to baseline migration should, in principle, be present equally across conditions and would not by itself account for the increased migration specifically toward the Aβ42 and Aβ42+iMGL conditions relative to CTR.

(2) Direct validation of CCL5 as the responsible ligand

To substantiate the claim that microglia-derived CCL5 is responsible for T cell recruitment, a CCL5-neutralising antibody should be added to the transwell assay. Similarly, a CCL4-neutralising antibody should be tested independently. This would allow the authors to attribute the migration effect to specific molecules rather than to the overall conditioned environment and would substantially strengthen the mechanistic interpretation.

We appreciate this comment and agree that ligand-neutralization experiments would substantially strengthen the mechanistic interpretation. We have not performed these experiments in the current study but will consider including CCL5- and CCL4-neutralizing antibody conditions in future follow-up work. We have revised the Results/Discussion to make clear that our receptor-blockade data (Fig. 4H) establish that CCR5/CXCR3/CCR1 signaling on T cells is necessary for recruitment, but do not by themselves attribute this effect to CCL4 or CCL5 specifically, as opposed to other chemokines present in the conditioned environment.

(3) Cell-type annotation validation for single-cell data

The authors should add a supplementary figure showing a dot plot or heatmap of canonical marker gene expression across all annotated clusters, cross-referenced to at least one published human brain atlas or human organoid single-cell reference dataset. Module score analysis using published cell-type gene signatures (e.g., Velmeshev et al. 2019, for neuronal subtypes or established microglial signature sets) would further validate the annotations. The specific software tool and reference dataset used for annotation should be explicitly named in the Methods section.

We thank the reviewer for this suggestion. Canonical marker gene expression supporting our cluster annotations is provided in Supplementary Figure S1 (violin plots of marker genes across annotated clusters.

(4) Statistical testing for cell-type proportion comparisons

Figures 1H and 3E should be reanalysed using a compositional statistical framework. The authors are encouraged to use the propeller method (Phipson et al., Bioinformatics, 2022) or scCODA (Büttner et al., Nature Communications, 2021), both of which are designed for this type of comparison in single-cell data. Individual organoid-level proportion values should be shown as overlaid data points to make biological variability is visible.

We agree and have reanalysed both comparisons with scCODA (Büttner et al., 2021), using cell-type counts aggregated per library (n = 2 per condition). Because scCODA estimates are conditional on a reference population, we specified migrating neurons as reference — the only population with a near-unity fold change (1.19×) and no credible change under any alternative reference. The results are shown in Supplementary Table 1.

We note that scCODA reports posterior inclusion probabilities rather than P values, and have removed P-value notation from all proportion comparisons. Figures 1H and 3E now display composition for each individual library as separate stacked bars, so that between-replicate variability is directly visible.

(5) Functional validation of microglial-promoted neuronal maturation

To support the claim that microglia promote neuronal maturation, at least one functional or morphological measurement attributable specifically to the microglia co-culture condition should be provided. Suggested approaches include: quantification of neurite length or branching complexity by automated image analysis comparing organoid slices with and without microglia; or synaptic puncta density measurements (already used elsewhere in the manuscript) comparing Aβ42 and Aβ42+iMGL conditions.

Thanks a lot for pointing this out. We agree that trajectory inference alone cannot support a claim that microglia promote neuronal maturation, and we regret that we are unable to provide the requested measurement: synaptic puncta quantification in this study was performed only for the CTR and Aβ42 conditions, and the material required to extend it to Aβ42+iMGL is no longer available. We have therefore revised the interpretation rather than defend the original claim.

We now describe the effect as a shift in organoid cell-type composition and transcriptional state toward more differentiated populations, rather than as microglia-driven neuronal maturation. The Results text has been changed from "…indicating that microglia promote neuronal maturation and partially reverse the Aβ42-induced immature state" to:

" Pseudotime analysis showed that microglial co-culture shifted cells toward higher pseudotime values compared with Aβ42 alone (Fig. 3F–G), consistent with a shift in organoid cell-type composition toward more differentiated populations (Fig. 3E) and a partial reversal of the Aβ42-associated skew toward progenitor states.”

(6) Chemokine secretion follow-up after T cell addition

To begin closing the proposed feedback loop, the authors should measure CCL4 and CCL5 levels (and ideally a broader cytokine panel) in conditioned media from the Aβ42+iMGL+T condition and compare them with those from Aβ42+iMGL. If T cells amplify microglial activation (as shown by calcium imaging), one would predict increased chemokine output. Including this measurement would substantially strengthen the feedback loop claim.

We would first clarify the scope of our claim. The feedback loop described in the manuscript operates at the level of cellular activation state: microglia-derived chemokines recruit CD8⁺ T cells (Fig. 4A–E, 4G–H), and recruited CD8⁺ T cells in turn amplify microglial activation (Fig. 4L). Each step is supported by direct measurement, and we do not claim that T cells increase microglial chemokine output or drive a further round of recruitment.

We agree that measuring chemokine secretion after T cell addition would test an important extension of this model — whether T cell-driven amplification of microglial activity translates into increased chemokine output and thus a self-sustaining recruitment cycle. We are unable to perform this experiment within the revision period, as the tri-culture conditioned media were not retained.

We would also note that this measurement is not straightforward in bulk conditioned media. CD8⁺ T cells are themselves major producers of CCL4 and CCL5, releasing preformed CCL5 from cytotoxic granules within hours of activation, so an increase in the Aβ42+iMGL+T condition could not be attributed to microglia. A rigorous test would require cell-type-resolved output — intracellular cytokine staining, single-cell profiling of the tri-culture, or physical separation of the two populations — and we now identify this explicitly as the next step.

(7) Time-course data for the protective-to-pathological transition

The dual functionality narrative requires temporal data to be credible. The authors should consider measuring Aβ clearance, pseudotime distribution, and chemokine secretion at multiple time points after microglial addition (e.g., 6, 24, and 48 hours) to determine whether the protective and inflammatory outputs are sequential or whether they co-occur from the outset.

We agree that a single 48-hour timepoint cannot determine whether protective and inflammatory microglial outputs are sequential or concurrent, and we are unable to add a time course within the revision period.

We have therefore moderated our interpretation. The Discussion previously stated that "microglial activation is not a binary state but a spectrum, where sustained Aβ stress drives the transition from a protective to a pathological, T-cell-recruiting state." This has been revised to: "This duality indicates that microglial activation is not a binary state: within the Aβ42 environment, clearance and neuroprotective functions are detectable alongside inflammatory, T-cell-recruiting outputs at the same timepoint." The temporal claim implied by "transition" has been removed, as our data establish co-occurrence at 48 hours rather than a sequence.

Recommendations for writing and presentation

(8) Abstract correction

CXCL10 must be removed from the mechanistic description of T cell recruitment in the abstract, as Figure 4E shows no significant change in CXCL10. The abstract should also moderate the language around "establishing a feedback loop" to reflect that the loop was observed and partially characterised rather than mechanistically closed.

CXCL10 has been removed from the mechanistic description in the Abstract, as Fig. 4E shows no significant change in its secretion. CXCR3 has been retained, as pharmacological blockade reduced T cell migration (Fig. 4H), but is now presented as a receptor-level finding without an identified ligand. We have also moderated the concluding clause, which now describes a neuroimmune circuit in which recruited T cells amplify microglial activation, rather than stating that a feedback loop is established. The Abstract sentence now reads: Using this platform, we demonstrate that microglia mediate amyloid-β clearance and shift organoid cell composition toward more differentiated states, but also become inflammatory and recruit CD8⁺ T cells through CCL4/CCL5 signaling via CCR1, CCR5, and CXCR3, forming a neuroimmune circuit in which recruited T cells further amplify microglial activation.

(9) Resolve the day 90 / day 60 inconsistency

The discrepancy between "day 90" in the Results text (line 88) and "day 60" in the Figure 1G legend must be corrected throughout the manuscript.

"Day 90" in the Results text (line 88) has been corrected with “day 60”.

(10) Rewrite the scRNA-seq library preparation methods

The methods section (lines 357-360) must be rewritten to describe the actual experimental conditions used in this study. The passage referring to cholesterol-treated and semaglutide-treated organoids on day 30 must be removed entirely.

The methods section has been now revised as: For isolation of iPSC-derived forebrain cells, cells were collected from CTR and Aβ42-treated organoids at day 60, and from Aβ42-treated organoids with and without a 48-hour iMGL co-culture (Aβ42 and Aβ42+iMGL). Two biological replicates were included in each group. Three organoids were pooled within each replicate and washed three times with pre-chilled PBS. Single-cell suspensions were prepared by incubating with 0.5 mg/mL papain for 30 min at 37 °C in a water bath. Suspensions were filtered through a 70 µm cell strainer (BD Falcon, 352350). After centrifugation at 500 g for 5 min, the cell pellet was resuspended in PBS + 0.01% BSA.

(11) Report the number of organoids per scRNA-seq replicate

The Methods section should explicitly state how many organoids were pooled per biological replicate for each single-cell sequencing experiment and how many replicates were included per condition.

The Methods section has been revised to state explicitly the number of organoids pooled per biological replicate and the number of replicates per condition for each single-cell experiment, as described in our response to comment (10). Two biological replicates were included per condition, each prepared from 3 pooled organoids.

(12) Attribute iPSC lines to specific experiments

A table or supplementary note should specify which cell line (H9, DYR0100, or DXR0109B) was used for each experiment and figure. If different lines were used interchangeably within the same figure, this should be stated and any resulting variability discussed.

All organoid data presented in this manuscript were generated from a single line, DYR0100; the H9 and DXR0109B lines were not used for any experiment reported here. We have removed them from the Methods to avoid ambiguity, and the Methods now state that DYR0100 was used for all organoid experiments. No experiment or figure combines material from different lines.

(13) Moderate the use of "human-specific"

Throughout the manuscript, claims of human specificity should be restricted to contexts where a direct comparison with rodent data has been performed or cited. When the platform uses only human cells, the appropriate phrasing is "human-derived" or "in a human cellular context" rather than "human-specific mechanisms."

We have replaced "human-specific" throughout with "human-derived" or "in a human cellular context," at four locations: the Abstract, the final paragraph of the Introduction, the second paragraph of the Discussion, and the legend of Fig. 4O.

(14) Revise the "first demonstration" claim

The claim to provide the "first human-specific mechanistic demonstration" (line 218) is not substantiated and should be removed or substantially qualified.

This claim has been revised.

(15) Immunofluorescence panel legibility

Protein label text in Figures 1B-E and 3B should be rendered in a contrasting colour (e.g., white with a black outline, or placed on a coloured background tab) so that they are readable against the fluorescence image background. Scale bars should be present and consistent across all panels within a figure.

Protein label text in Figures 1B–E and 3B has been re-rendered in a contrasting colour so that it is legible against the fluorescence background. Scale bars are present in all panels, and their dimensions are stated in the corresponding figure legends.

(16) Remove or justify the Animals section in Methods

If no mouse data are presented in the paper, the Animals section should be removed. If mouse experiments were performed and the data are available, a corresponding figure or supplementary figure should be included.

Animals section description has been removed from Methods.

Corrections & Clarifications

(17) The following must be corrected before resubmission:

(a) Replace "(ref)" placeholders on lines 46 and 63 with full citations.

(b) Replace "(cell reports 2023)" on line 48 with a properly formatted citation. This appears to refer to Feng et al., Cell Reports 42, 113313 (2023), which is already reference 9 in the list - it should simply be cited as such.

(c) Reference 14 (Feng et al., STAR Protoc, glioma organoid protocol) does not support the CCL5-CCR5 claim for which it is cited and should be replaced with an appropriate reference.

(d) Reference 20, cited in the text (line 56), does not exist in the reference list. The intended citation must be identified and added.

(e) Reference 3 (Michell-Robinson et al.) is listed but not cited in the text. It should either be cited where appropriate or removed from the list.

We have carefully reviewed the manuscript and corrected the incomplete and incorrect references.

(18) GEO accession numbers

The manuscript states that bulk RNA-seq data have been deposited at GEO but does not provide an accession number. The accession number must be included in the Data Availability section.

Accession numbers have been added to the Data Availability section: bulk RNA-seq data are deposited under GSE339404 and single-cell RNA-seq data under GSE339602. Both datasets are publicly accessible.

(19) Single-cell RNA-seq data availability

The single-cell RNA-seq data are not mentioned in the Data Availability statement. These data should also be deposited in a public repository (GEO or a single-cell-specific repository such as the Human Cell Atlas data portal), and the accession number should be provided.

Mentioned in comment (18).

(20) Zenodo DOI

The Code Availability section states that code has been deposited at Zenodo, but no DOI is provided. The Zenodo DOI must be included.

Zenodo DOI has been added in the Methods: Single-cell RNA-seq data have been deposited at GEO under accession GSE339602 and bulk RNA-seq data under accession GSE339404; both are publicly accessible as of the date of publication. Microscopy data are available at Zenodo (DOI: 10.5281/zenodo.21686712). All other raw data, including cytokine array images, and all original code are available at https://github.com/FengYilinElaine/2-3D-AD-oranoids.

(21) Ethical approval for human blood collection

The manuscript states that blood was collected from healthy donors at Zhangzhou People's Hospital but does not mention institutional ethical approval for this collection or informed consent procedures. A statement confirming ethical approval (with approval number) and donor-informed consent must be added to the Methods section in accordance with eLife's policies on human subjects research.

Ethical approval for this study was granted by the First Affiliated Hospital of Zhengzhou University (2021-KY-0875-003) and Tsinghua Shenzhen International Graduate School (2024-F125). It has been added to the Methods.

(22) Microscopy data availability

The manuscript states that microscopy data will be shared upon request. eLife's data policy requires that primary data supporting the figures be made publicly available at the time of publication. The authors should deposit representative raw imaging data (or processed calcium imaging traces) in an appropriate repository such as Figshare, Zenodo, or the Image Data Resource and provide the link in the Data Availability section.

Mentioned in comment (20)

Reviewer #2 (Recommendations for the authors):

This study is interesting and presents novel findings supported by state-of-the-art approaches, including single-cell RNA sequencing, a three-dimensional cerebral organoid model, and co-culture systems involving two distinct immune cell populations.

These innovative methodologies provide valuable insights into the mechanisms under investigation. Nevertheless, several aspects of the study require clarification and further improvement.

The authors should address the points in the public review and the following additional points:

(1) Throughout the manuscript, the figure legends contain conclusions and interpretations of the data. These statements should be removed from the figure legends and incorporated into the Results section, while the legends should be restricted to describing the experimental conditions and the data displayed.

Revised manuscript and legends fixed the problem.

(2) The reference list and in-text citations appear to be incomplete. In several instances, the manuscript contains placeholder citations (e.g., "Ref") instead of full references. The authors should carefully review and complete all citations.

We have carefully reviewed the manuscript and corrected the incomplete and incorrect references. All placeholder citations have been replaced with the appropriate references, and the reference list and in-text citations have been checked for completeness.

eLife Assessment

This study presents an important examination of the role of cis-acting versus trans-acting genetic variation on DNA methylation divergence between humans and chimpanzees, including its consequences for gene expression. By differentiating fused interspecies tetraploid cell lines into multiple cell types, the study provides compelling evidence for the importance of cis-acting changes and solid evidence for the relevance of these changes to adaptive evolution in humans. This work will be of interest to biologists and evolutionary anthropologists studying the evolution and genetics of gene regulation, particularly in primates.

Reviewer #1 (Public review):

Ma et al. use human-chimpanzee tetraploid cells, across different cell types, to identify the genetic causes and then transcriptomic consequences of divergence in DNA methylation. They conclude that the evolution of DNA methylation is driven primarily by cis-regulatory changes, and that the evolution of CpG sites contributes to cis-regulation while transcription factor expression underlies some trans changes. They then argue that divergence in DNA methylation is associated with changes in gene expression and may contribute to human phenotypes.

The tetraploid model is able to provide compelling evidence that most regulatory evolution occurs due to cis-regulatory changes, and that sites that have diverged in DNA methylation level cluster together into DMRs which share similar divergence patterns and genetic architecture. This stands in intriguing contrast to trans-mechanisms which explain most variation within modern human populations. The authors proceed to show that trans-effects can be explained, in part, by nearby TF binding motifs and many cis-regulatory changes are explained by CpG-disrupting variants. While these mechanisms clearly contribution to divergence in DNA methylation, the degree to which they explain cis- and trans-regulatory divergence would be valuable.

Next, the authors seek to show that differences in DNA methylation are functionally relevant. Consistent with previous results, they show that differences in DNA methylation are (weakly) associated with changes in gene expression. They hypothesize that genes with concordant regulatory should exhibit great methylation-expression coupling than other genes and show that cis-expression/cis-methylation pairs are more strongly correlated than trans/trans pairs. I think that looking at cis/trans or trans/cis changes would also be useful. Another limitation is that this analysis is limited to promoter regions. It is not clear how many divergent DMRs that includes and how many of those genes have differences in expression. The key question is whether differences in DNA methylation are functionally important, and the answer provided by these analyses is "sometimes".

Finally, the authors make a case for lineage-specific selection on DNA methylation that is connected to human traits. Using a sign-test, they identify sets of genes which have likely experienced selection in humans and may underlie human phenotypes.

In conclusion, I think this study provides a valuable resource for differences in DNA methylation between humans and chimpanzees across tissues and provides important insight into the relative abundance of cis and trans regulatory divergence. Additional research is necessary to investigate the underlying regulatory mechanisms and more care needs to be taken in exploring the functional consequences.

Reviewer #3 (Public review):

Summary:

Ma et al. use human-chimpanzee tetraploid cells to examine species differences in DNA methylation. They identify differentially methylated regions under cis or trans regulation. Cis-DMRs are enriched near SNVs that disrupt or create CpGs, providing a plausible mechanism for cis changes in methylation. They also seek to identify transcription factors that might affect methylation in trans, as well as gene sets with evidence for consistent changes in methylation and expression between humans and chimpanzees, suggesting that they may underlie lineage-specific traits.

Strengths:

The authors have generated a new dataset across multiple different cell types examining differences in DNA methylation between humans and chimpanzees using human diploid cells, chimpanzee diploid cells, and human-chimpanzee tetraploid cells. Using this dataset, they identify that cis-DMRs are enriched near SNVs that disrupt or create CpGs compared to trans-DMRs and identify transcription factors as candidate trans-acting factors. Both identified SNVs and transcription factors are good candidates for future experimentation. The authors also find that cis-DMRs are more highly correlated with cis-expressed genes than trans-DMRs with trans-expressed genes, providing evidence that methylation and expression are linked genome-wide. Further, they apply a clever sign test approach to identify gene pathways with evidence for lineage-specific selection.

Comments on revised version.

They authors have addressed my concerns from their initial manuscript. In particular, the authors have noted the limitations of their study as appropriate, including the use of permissive FDR cut-offs.

Author response:

Summary of changes:

(1) Framing of the sign test results. Throughout the manuscript we have clarified that the sign test provides direct evidence that the implicated gene sets are under lineage-specific selection, while the connection of this selective signal to any specific human phenotype is inferential and would require experimental validation. We also now emphasize that some sign test results are expected to be false positives, as indicated by the FDR.

(2) FDR and cis:trans quantification. We have added explicit statements that (i) the cis dominance is consistent across a range of FDR thresholds (FDR < 0.25, 0.20, 0.10, 0.05, 0.01), (ii) the mean proportion of divergent sites explained by cis-regulation is 91%, and (iii) using the changepoint detection method, we identified 9159 cis-DMRs and 2046 trans-DMRs in total for downstream TF motif and SNV analysis. A power analysis comparing sensitivity to detect cis vs. trans effects is provided as author response image 1.

(3) Clarification of regulation groups, including pure cis, pure trans, conserved, cis × trans and cis + trans. We have added explicit definitions of these categories in the Results.

(4) Cis-gene direction-of-effect definition. We have clarified in the text that cis-regulated genes are defined as those where the direction of allelic difference is consistent between hybrid and parental samples. We note that the scatter plots in Figure 2B as well as Figure 2 supplemental figures plots the per-sample average percent difference in methylation. Cis genes appearing to have opposite direction-of-effect along the y=x diagonal on the scatter plot were due to a difference between this average, used only for visualization, and the values used for analysis in our statistical model. For values close to zero, average log2FC or per cent difference can flip sign even when the model correctly identifies the site as cis-regulated. The regulation classification is based on a statistical model and not the direction of average difference, so there will naturally be some small deviation around the axes when visualizing the results as a scatter plot.

(5) New limitations. We have added four new limitations to the Discussion: (i) absence of an outgroup species; (ii) TFBS-disrupting mutations as an alternative cis mechanism; (iii) the need for experimental validation of SNV-methylation and TF-methylation links; and (iv) the scope of cell types examined.

(6) Quantitative reporting. We have replaced "substantial" with specific numbers throughout.

(7) Additional supplemental resource. A list of cis–cis regulated promoters and their associated genes has been added as Supplemental File 8.

(8) Minor corrections. Missing citation for Hallgrímsdóttir et al. (2024) added; "Preprint at" removed from published paper citations; sequencing coverage reported in Methods.

eLife Assessment:

This study presents an important examination of the role of cis-acting versus trans-acting genetic variation on DNA methylation divergence between humans and chimpanzees, including its consequences for gene expression. By differentiating fused interspecies tetraploid cell lines into multiple cell types, the study provides compelling evidence for the importance of cis-acting changes, but incomplete evidence that these changes are of importance for adaptive trait evolution in humans. This work will be of interest to biologists and evolutionary anthropologists studying the evolution and genetics of gene regulation, particularly in primates.

We appreciate the assessment and agree that the evidence for adaptive trait evolution is indirect. We would like to clarify what the sign test does and doesn’t establish. By rejecting a rigorous neutral null model, the sign test provides strong evidence for lineage-specific selection on DNA methylation divergence. Since the coordinated directional divergence we observe is not expected under neutral evolution, we are confident that the data are evidence of selection. However, the sign test does not identify the specific traits that selection acted upon; the connection between the signal of selection and any phenotype is speculative. Accordingly, we have now revised the manuscript to describe the sign test results as evidence of selection while keeping the interpretation of specific traits explicitly speculative. We also added discussion of the limitations on the trait-level inference (such as the absence of an outgroup, reliance on clinical HPO ontologies, etc.).

Reviewer #1 (Public review):

Ma et al. use human-chimpanzee tetraploid cells across different cell types to identify the genetic causes and then transcriptomic consequences of divergence in DNA methylation. They conclude that the evolution of DNA methylation is driven primarily by cis-regulatory changes, and that the evolution of CpG sites contributes to cis-regulation, while transcription factor expression underlies some trans changes. They then argue that divergence in DNA methylation is associated with changes in gene expression and may contribute to human phenotypes.

We thank Reviewer 1 for a detailed summary of our work.

The tetraploid model is able to provide compelling evidence that most regulatory evolution occurs due to cis-regulatory changes. My only concern is that the extent of trans-changes may be overstated, as almost all are eliminated by changing from a nominal p-value criterion to even a 25% false discovery rate.

We agree that trans-effects are more sensitive to FDR thresholds than cis-effects, and we have addressed this directly. This is a well-recognised limitation of existing cis/trans classification frameworks, and we acknowledge this limitation in the discussion and have added suggestions in experimental set-up to mitigate it. To address the reviewer's concern directly, we have added a formal power analysis quantifying the relative power to detect cis and trans effects as a function of read depth as well as biological noise (dispersion). We now explicitly state in the Results that the cis dominance over trans is consistent across a range of FDR cutoffs (FDR < 0.25, 0.20, 0.10, 0.05, 0.01; Figure 2—figure supplement 1–2), and we note that the greater FDR-sensitivity of trans-DMRs likely reflects systematically smaller effect sizes rather than false positives. We have added a power analysis in Author response image 1 that formally compares our sensitivity to detect cis vs. trans effects. We also note that DMR-level analyses recover both cis and trans effects at meaningful FDRs, consistent with the idea that trans effects are real but requires more replicates as well as a higher sequencing depth to make significant calls at the same level as cis changes at the individual CpG level.

Author response image 1.

Power analysis of cis and trans effects detected by the beta-binomial GLM framework. For each combination of effect size, per-unit read depth, and overdispersion (φ), we simulated a genome of 10,000 units — either individual CpG sites or regions/DMRs — comprising 2,000 true-effect units and 8,000 null units. The simulation is unit-agnostic: a "unit" represents a single CpG when modeling the per-CpG analysis and an aggregated region when modeling the regional (DMR-level) analysis, with read depth interpreted as the per-CpG coverage or the region-level (aggregate) coverage, respectively, and effect size as the corresponding per-CpG or region-level H–C methylation difference.

Effects were classified using the same two-model scheme as the main analysis. A unit was called cis if the hybrid allelic (H–C) test was significant and the allele-by-generation interaction was not significant, and trans if the interaction was significant and the hybrid allelic test was not significant; all tests were Benjamini–Hochberg–corrected across the genome at the stated FDR threshold. Each unit was simulated with the full six-measurement design (two parental samples and four hybrid alleles from two hybrids), both models were fit, each set of p-values was BH-corrected across the genome, and "power" is the fraction of true units that land in the correct class.

Cis-effect units were simulated with an equal H–C difference in both parents and hybrid (zero true interaction); trans-effect units with a parental H–C difference and no hybrid allelic difference (full-magnitude interaction); null units with no difference in either parents or hybrid. Sequencing depth was treated as a fixed design parameter: every sample at every simulated unit was assigned the same total read depth (the value on the y-axis of the heatmaps), corresponding to per-CpG coverage for the site-level analysis or aggregate per-region coverage for the regional analysis.

We estimated the beta-binomial overdispersion (φ) directly from the data for each cell type used in this study: DA = 0.024, CNCC = 0.016, IPSC = 0.013, SKM = 0.014, and HEP = 0.011 (median = 0.014). To span this empirical range and to assess robustness to higher-than-observed dispersion, we evaluated power at φ = 0.015 (approximating the empirically observed median), 0.05, and 0.10; the latter two represent substantially more conservative (higher-noise) scenarios than any cell type in our data. Because power declines monotonically with φ, the φ = 0.015 row reflects the sensitivity expected under realistic conditions, while the higher rows bound the worst case. For each unit, a methylation probability was drawn from a beta distribution whose mean equals the unit's true methylation level and whose dispersion is set by the overdispersion parameter φ, and the number of methylated reads was then drawn from a binomial with that probability and the specified total depth. Consequently, the reported power describes the sensitivity expected at a given uniform per-unit (per-CpG or per-region) depth, spanning 10× to 200×, and is interpreted as the proportion of true-effect units assigned to the correct class.

The follow-up analyses are incomplete with major gaps. The authors focus on single potential mechanisms for cis- and trans-changes, but it is not clear to what degree these mechanisms explain the extent of cis and trans changes. There are also other mechanisms which are not investigated, such as the importance of TF binding sites for cis-regulatory evolution.

We agree that CpG-disrupting SNVs and TF binding motifs are just two out of many possible mechanisms, and we have added explicit acknowledgements of this in the text. Our goal was not to investigate all possible mechanisms, but rather to focus on two that showed promising results. For cis-regulation, we now state that TFBS mutations and other sequence variants could also contribute. We agree that further mechanistic investigation is an important direction for future work, and we have noted this explicitly in the Discussion.

Next, the authors seek to show that differences in DNA methylation are functionally relevant... I worry that this result could be confounded by larger effect sizes for cis-changes than trans effects.

We agree that larger cis-regulatory effect sizes could contribute to this result, and have now mentioned this in the Discussion: “This finding suggests that the repressive effects of species-specific methylation are strongest when both layers of regulation are driven in cis, perhaps because cis-regulated methylation changes tend to have larger effect sizes than trans-regulated changes.”

Finally, the authors make a case for lineage-specific selection on DNA methylation that is connected to human traits. This evidence was not convincing. In fact, it is even said that these tests cannot be interpreted as evidence of lineage-specific selection (lines 399-401), so I am confused why these results are framed as testing for selection.

We appreciate this comment but want to clarify. Lines 399–401 in the original manuscript state that the dental pulp stem cell (DPSC) sign test results specifically should not be interpreted as evidence of lineage-specific selection, because DPSCs use parental rather than hybrid cell lines. This caveat applies only to DPSCs. For all other cell types (iPSC, DA, CNCC, SKM, HEP), which use hybrid cell lines that control for trans-acting confounders, the sign test does indeed provide evidence of non-random directional bias inconsistent with neutral evolution, thereby constituting evidence of lineage-specific selection. We have added a clarifying sentence to make this distinction explicit: "For all other cell types (iPSC, DA, SKM, HEP, CNCC), which use hybrid cell lines, the sign test results provide direct evidence of lineage-specific selection on the implicated gene sets, as the hybrid system controls for trans-acting confounders."

To be clear about the scope of the claim: the sign test directly demonstrates that the implicated gene sets are under lineage-specific selection. What remains inferential is the connection between this selective signal and any specific human phenotype, which would require experiments or further validation to establish; we have revised the framing throughout to keep this distinction explicit.

Reviewer #1 (Recommendations for the authors):

(1) Line 96: How many iPSC lines were used for each species? When a replicate is mentioned (e.g., Figure 1B), are those technical or biological replicates?

We have added the iPSC line counts to both the Results and Methods sections: two human and two chimpanzee iPSC lines were used. Replicates shown in Figure 1B are biological replicates (independent differentiation experiments from the same iPSC lines).

(2) Line 98: How many donors for the DPSCs?

We have added DPSC donor counts to the Methods: two human and two chimpanzee donors.

(3) Line 103: PCA and other analyses combined data from WGBS and RRBS cell types. Some clarification about how this was done (e.g. restricting to RRBS sites?) would be useful in the main text as well as an acknowledgement of potential biases. And

(4) Line 103: Related, what is the number of CpG sites considered?

We have added a clarifying sentence to the Results: cross-cell-type analyses including Figure 1B heatmap and Figure 1C PCA analysis were restricted to CpG sites covered in all samples (i.e., the intersection of all covered sites, after phasing the hybrid samples), totaling 561,762 shared CpG sites. Within-cell-type PCA analysis in Figure 1—supplemental figure 1 was restricted to CpG sites shared across samples of the same cell type, which contains 31,802,196 sites for CNCC samples, 26,163,237 sites for DA, 29,787,850 sites for DPSC, and 1,006,674, 935,636 and 952,835 sites for IPSC, SKM and HEP, respectively. We acknowledge that this restriction to the intersected CpG sites result in PCA performed on sites covered by both WGBS and RRBS, which are most frequent in CpG-dense regions.

(5) Line 103: For Figure 1B, it would be useful to first mention how human/chimp reads were parsed and for how many CpG sites this was possible.

We have added a brief description of the allele-parsing approach (SNPsplit using species-specific SNV positions). For hybrid WGBS samples (DA and CNCC), on average, 48.2% ± 0.2% of all aligned reads are unassignable using SNPs between human and chimpanzee genome, 25.9% ± 0.2% of the reads are specific to human, and 25.1% ± 0.2% of reads are specific to chimpanzee. For hybrid RRBS samples (IPSC, SKM and HEP), on average, 88.4% ± 0.3% of all aligned reads are unassignable using SNPs between human and chimpanzee genome, 5.3%±0.1% of the reads are specific to human; 5.3%±0.1% of reads are specific to chimpanzee. We have added information above to the main text. Per sample splitting reports containing the exact number of reads assignable to each of human and chimpanzee are provided as a comprehensive table at Supplemental File 1. The lower assignment rate in RRBS is expected, and we have performed two additional analyses to demonstrate why. First, the reduced representation strategy concentrates coverage in CpG-dense promoters that are highly conserved between human and chimpanzee and therefore SNV-poor, while the short MspI fragments that dominate these libraries frequently fail to reach an informative SNV even when one is nearby. Quantifying this directly: among the 16,845,376 CpG positions covered by the union of all unphased hybrid RRBS libraries, 65.1% contain a human–chimpanzee SNV within ±50 bp (the reach of a typical RRBS read), compared with 90.8% within ±150 bp (the reach of a typical WGBS read pair) — a 1.40-fold difference in SNV accessibility at the very same CpGs. Second, we compared the aligned-length distributions of allele-resolved and unassigned reads across all ten hybrid libraries (Author response image 2). In the four WGBS libraries the two distributions are indistinguishable, confirming that read length is not driving mappability. In contrast, for all six RRBS libraries, allele-resolved reads are consistently longer than unassigned reads, with the effect reproducible across every cell type and replicate.

Author response image 2.

Aligned read length determines allele-assignment success in RRBS but not in WGBS. Aligned read lengths were extracted from the Bismark-aligned BAM files produced by phasing all ten hybrid bisulfite libraries: four WGBS libraries (CNCC and DA, two replicates each; left) and six RRBS libraries (HEP, iPSC and SKM, two replicates each; right). For each library, reads assigned to either the human (genome1) or chimpanzee (genome2) alleles were pooled into a single phased set (blue) and compared with the reads that could not be phased (grey); distributions were computed from subsampled reads and are shown as boxplots (box, interquartile range; line, median; whiskers, 5th–95th percentiles). In the WGBS libraries, phased and unassigned reads have effectively identical length distributions (median 150 bp for both; means 147.4–147.8 vs 142.1–143.1 bp), indicating that read length does not drive mappability in WGBS. In the RRBS libraries, which are dominated by short MspI fragments, phased reads are consistently longer than unassigned reads across every cell type and replicate (medians 70–75 vs 49–50 bp; means 80.5–85.7 vs 58.6–60.6 bp, ~1.4-fold). Because a read can be assigned to a parental allele only if it spans an informative human–chimpanzee SNV, these results show that the short fragment length characteristic of RRBS — together with its enrichment for SNV-poor, evolutionarily conserved CpG-dense promoters — accounts for its lower allele-resolution rate relative to WGBS.

(6) Line 103: Hybrid/parental line isn't noted in the PCA. Is this just the parental samples?

We clarify that Figure 1C shows both parental and hybrid samples, and we have updated the figure caption for Figure 1C to note that both hybrid and parental samples are plotted in the PCA. The parent/hybrid stratifications are shown in Figure 1—figure supplement 1 and referred to in the main text.

(7) Line 149: No citation # is given for the Hallgrimsdottir paper.

Corrected. Citation number 50 (Hallgrímsdóttir et al., 2024) has been added.

(8) Line 167-169: Some explicit test here would be useful. Is this more than we'd expect just because the majority of CpG sites have conserved methylation levels? How much more do divergent CpG sites cluster than expected by chance?

We agree that an explicit test of clustering would be informative, and we want to be clear about what our analysis does and does not establish. The changepoint algorithm is not a test of non-random clustering: it detects shifts in the local composition of regulatory classifications along the genome and segments each chromosome into locally homogeneous stretches. Its purpose here is enrichment rather than inference, because it selects regions in which neighboring CpG sites share both a regulatory classification and a consistent direction of species bias, so that the downstream motif-enrichment and CpG-SNV proximity analyses operate on interpretable units rather than on mixtures of mechanisms. Because the segmentation is not compared against a null model, it cannot by itself establish that divergent sites co-localize more than expected given that 83–93% of all sites are conserved. We have therefore revised the text so that Figure 2D reads as a descriptive summary of the neighbourhood composition of each regulation group, and removed any implication that the co-localization has been tested against a chance expectation. Asking whether divergent sites cluster more than expected is a genuinely different question from the one our DMR-calling addresses and answering it well would require a dedicated null model. We think this is a worthwhile analysis and a natural extension of this framework, but it is separate from the claims we make here, and we have not attempted it in this revision.

(9) Line 186-187: It should be made clear that you looked to cis, trans, and cis + trans DMRs independently.

We have revised this sentence to make explicit that cis-DMRs, trans-DMRs, and cis+trans DMRs were identified independently using the changepoint detection method applied separately to each regulatory class.

(10) Line 190-192: Some quantification of the degree to which cis effects exceed trans effects would be useful. What proportion of total divergence (e.g. mean and s.d.) is explained by cis factors?

We have added this quantification: “At FDR < 0.05, cis-regulation accounted for a mean of 91% of divergent sites and trans-regulation a mean of 4.5% across cell types, and cis remained the dominant category at every FDR cutoff tested (FDR < 0.25–0.01; Figure 2C, Figure 2—figure supplement 1–2, Supplemental Files 1–2).”

(11) Line 194-196: It should be made clear that motif enrichment was done in the human genome, right? Are the results consistent if motif enrichment was done in the chimpanzee genome?

We have clarified in the Methods that HOMER motif enrichment was performed using the human genome (hg38) as background. Repeating the analysis using the chimpanzee genome as background is a valuable future direction; we acknowledge this has not been formally tested.

(12) Line 208: For TFs other than FOXM1 and FOXA2, is TF expression generally associated (positively or negatively) with trans DMRs favoring the chimpanzee or human lineage? An idea of the distribution would be useful.

We plotted the distribution of differential TF expression for those with predicted binding sites enriched in Hu>Ch trans-DMRs versus Hu<Ch trans-DMRs in DA and CNCC. In neither cell type do the two distributions show a clear separation of directional shift. TF expression differences are broadly overlapping regardless of whether the associated trans-DMR favors the human or chimpanzee lineage. We speculate the lack of separation reflects multiple trans-acting inputs shaping methylation divergence such that single TF expression does not predict it. Aggregating across TFs with potentially opposing effects could further contribute to this observation as well (Figure 3—figure supplement 1). FOXM1 and FOXA2 are individual cases where a suggestive relationship was visible rather than evidence of genome-wide pattern.

Author response image 3.

Distribution of differential expression of TFs with predicted binding sites enriched in trans-DMRs. Density distribution of TF expression difference in human versus chimpanzee parental samples. There is a lack of separation between expression of TFs with predicted binding sites enriched in Hu>Ch trans-DMRs versus Hu<Ch trans-DMRs, in both DA and CNCC.

(13) Line 211-212: Stats are needed.

This statement is intended as a qualitative description rather than a quantitative statement. With only 4 cell types per comparison (Figure 3B), we do not have enough statistical power to establish a significant correlation, therefore we present this result as an exploratory observation rather than a statistically significant finding. We have therefore removed "consistent with this expectation," reframed the FOXM1 and FOXA2 results as descriptive observations from individual factors, and added an explicit statement that they are exploratory and hypothesis-generating rather than evidence of a genome-wide pattern.

(14) Figure 3C: Direction is not given. It should be made clear that this is a gain/loss in humans.

We have updated the Figure 3C caption to explicitly label the three SNV categories as: CpG gains in humans (human allele creates a CpG), CpG losses in humans (human allele disrupts a CpG), and no CpG change.

(15) Figure 3C: Most cell types have a bias towards increased DNA methylation when there are no nearby CpG sites (gray bars). Why? Is this a consequence of a reference bias?

We thank the reviewer for raising this. The grey bars correspond to methylation levels of conserved CpG sites near SNVs with no CpG-altering substitution and serve as the genome-wide background/control category, against which the substitution-containing categories are compared. Their modest skew toward higher methylation reflects a global offset shared by all categories rather than a substitution-specific effect. We suggest two non-exclusive explanations for this baseline offset: a genuine genome-wide difference in the distribution of human- versus chimpanzee-biased methylation, and/or a possible contribution of reference genome mapping bias arising from alignment to the human genome. Importantly, this does not affect the conclusions drawn from Figure 3C. Because the genome-wide offset is shared across all categories, the substitution-attributable signal is reflected in the difference between the CpG-gain/loss categories and the no-change (grey) baseline, and any genome-wide baseline shift — biological or technical — cancels in that comparison. We therefore interpret the grey-category asymmetry as a background property and explicitly do not attribute it to the substitutions themselves. Future work such as analyzing with reads mapped to the chimpanzee or a masked consensus genome or restricting to mappability- and coverage-matched regions could directly quantify any reference-bias contribution, and we note these as promising directions.

(16) Line 258-269: Figure 3D is not referenced in the text.

We have added a reference to Figure 3D in the relevant paragraph of the Results: “To test this, we compared the genomic distance between each DMR and its nearest CpG SNV. Consistent with our model, we found consistently shorter distances for cis-DMRs than trans-DMRs across all cell types examined: Median distances to the nearest CpG SNV were 24 ± 6 bp for trans-DMRs vs. 11 ± 2 bp for cis-DMRs (Figure 3D; Mann-Whitney p < 0.001 for all comparisons) [65].”

(17) It is unclear why Figure 4A-C focus exclusively on cis-regulated promoters. Is this for biological or technical reasons?

Both. Biologically, cis-regulated promoters are the most interpretable for assessing cell type-specificity, because cis effects are allele-intrinsic and not confounded by differences in trans-acting environments across cell types. Technically, trans-regulated promoters show methylation differences that depend on the trans-environment, making cross-cell-type comparisons less straightforward.

(18) Line 371: How many DMRs are being considered?

We have added the total number of DMRs (promoters) considered in the sign test analysis: 6,283.

(19) Line 371-372: What is the ASM/ASE concordance test? I thought you were restricting the analysis to genes with a negative association between ASM and ASE (lines 366-367), so this needs to be clarified.

We have clarified this in the text. The two-step procedure works as follows: (1) a binomial sign test is applied to all genes with promoter ASM to identify gene sets with directional bias in methylation; (2) separately, a binomial sign test is applied to the subset of genes where ASM and ASE show a negative (repressive) relationship. Gene sets that pass both steps are reported as candidates. The "ASM/ASE concordance test" refers to step 2. We have revised the text to make this two-step logic clearer.

(20) Line 379: It may be worth mentioning that these are the DMRs which are most likely to be functionally relevant in shaping expression levels.

We have added this sentence: " This subset represents cases where methylation changes are most likely to have a simple and direct repressive effect on transcription, filtering out more complex regulatory scenarios where methylation and expression changes may be uncoupled or subject to competing regulatory influences."

(21) Line 387: The test here needs to be clearer. Does a significant result mean an enrichment of differences in that gene set, or a bias in the ratio of Hu/Ch differences?

We have clarified: a significant result from the binomial sign test indicates a statistically significant bias in the ratio of human-biased to chimpanzee-biased changes within a gene set, relative to the genome-wide background ratio. It does not test for enrichment of the number of differences, only for non-random directionality.

(22) Line 403: Why the focus on expression, when the rest of the paper is focused on the methylation patterns?

Gene expression is the most direct functional readout of promoter methylation changes. The two-step sign test uses expression data in the second step precisely because it allows us to identify cases where methylation divergence has a demonstrable downstream consequence on transcription, which is the canonical mechanism by which promoter methylation affects phenotype. We have added a brief justification of this rationale to the text.

(23) Line 456: Not clear where there is actually evidence of lineage-specific selection.

We have added an explicit sentence in the Discussion describing what the evidence consists of: "Specifically, the evidence rejecting a neutral null model of cis-regulatory evolution consists of statistically significant directional bias in both promoter methylation and gene expression within functionally coherent gene sets, assessed using a two-step binomial sign test with permutation-based FDR correction." This constitutes direct evidence that the implicated gene sets are under lineage-specific selection; the separate question of which specific human phenotypes that selection shaped remains inferential and is framed as such throughout.

(24) Line 457-459: I think this line needs to be further explained: "Our use of hybrid cell lines was critical to this discovery, as it allowed us to isolate cis-acting regulatory changes from confounding trans-acting and environmental effects." Specifically, it's not apparent why cis-regulation is important for demonstrating evidence of selection.

We have added an explanation: "Isolating cis-acting changes is critical because the sign test requires that each promoter represents an independent observation; in hybrid cells, each allele's methylation is determined by its own cis-regulatory sequence, making observations across promoters genuinely independent and thus satisfying the assumptions of the binomial test."

(25) Line 460-465: The concluding claims throughout this paragraph appear to be overstated.

We have revised the concluding paragraph of the Results and the Discussion conclusion to soften the language.

(26) Line 487: Provide the actual numbers instead of saying "substantial".

We have replaced "substantial numbers of allele-specifically methylated promoters" with the actual count: 6,283 allele-specifically methylated promoters across all cell types.

(27) Line 502: I question this interpretation. While it could be that there is a shared mechanistic basis, it could also be that the cis effects tend to be larger than the trans effects, providing additional power to identify strong correlations.

We agree and have added this alternative explanation explicitly to the Discussion (see response to public review comment above).

(28) Line 510: But the results section states that it's not possible to interpret these as lineage-specific selection.

The caveat at lines 399–401 applies specifically to DPSCs, not to hybrid cell types. We have revised the text to make this distinction unambiguous.

(29) Line 601: What coverage was the methylation data?

We have added sequencing coverage and the number of CpG sites assayed below “Bisulfite-seq library preparation, sequencing and mapping” section in Methods. WGBS libraries achieved a mean coverage of 9.68× per CpG site, covering 43.6M unique CpG positions in CNCC (hybrid) and 43.4M in CNCC (parental), 41.9M in DA (hybrid) and 38.8M in DA (parental). RRBS libraries achieved a mean coverage of 5.02× per CpG site, covering 5.0M, 4.8M, and 4.5M unique CpG positions in the hybrid HEP, IPSC, and SKM libraries respectively, and 3.3M, 3.4M, and 3.2M in the corresponding parental libraries. The total number of CpG sites (union) of all WGBS samples is 48,994,320 sites, and the union of all CpG sites of RRBS samples is 7,289,251. The union of all samples (including WGBS and RRBS) is 49,049,052. We have also included coverage information per sample as a table in Supplemental File 1.

(30) Line 820: citation shouldn't include "preprint at".

Corrected. "Preprint at" has been removed from all published paper citations in the reference list.

Reviewer #2 (Public review):

This manuscript investigates the causes and consequences of human-specific DNA methylation divergence relative to chimpanzees... This study provides a valuable dataset and a compelling framework for understanding how local sequence variation contributes to epigenetic and transcriptional divergence, with likely broad impact in comparative and evolutionary genomics.

We thank Reviewer 2 for this positive assessment and for the constructive suggestions.

Although the authors identify transcription factors associated with differential methylation, it is unclear what proportion of differentially methylated CpGs or DMRs can be attributed to these factors. Providing a quantitative estimate would help assess the relative contribution of trans-acting regulation.

We agree that a quantitative estimate of the proportion of differentially methylated CpGs or DMRs attributable to these transcription factors would be informative in principle. In practice, however, such an estimate is challenging to produce reliably: predicted binding sites are not all occupied or functional, individual DMRs are typically influenced by multiple trans-factors, and we lack the per-site functional data needed to assign methylation differences to specific TFs with confidence. More importantly, even if we could generate such a number, an association-based estimate would not establish that these factors causally drive the observed methylation differences. We have added a note to the main text clarifying that our analysis identifies candidate trans-acting factors associated with differential methylation rather than quantifying their causal contribution.

The analysis of CpG-disrupting mutations is interesting but raises two concerns. First, other classes of variants—such as transcription factor binding site-disrupting mutations—could also influence local methylation patterns and are not considered here. Second, the causal direction remains ambiguous: CpG-disrupting mutations may result from methylation-associated mutational processes (e.g., C->T transitions at methylated CpGs) rather than being the primary drivers of methylation divergence.

We have addressed both concerns in the revised manuscript. On the first point, our goal was not to suggest that CpG-disrupting variants are the only causes of local methylation divergence. We now explicitly acknowledge in the Results that TFBS mutations and other variant classes could also contribute to cis-methylation divergence and represent an important avenue for future investigation. On the second point: while CpG-disrupting mutations are indeed expected to be enriched in highly methylated regions, they would be expected to associate with methylation level rather than methylation divergence, and thus cannot explain the patterns we observe.

Regarding the discussion comparing the distance between CpG-disrupting SNVs and trans-DMRs, without information on the absolute or relative distance distributions, it was difficult to assess the magnitude of the observed differences. Moreover, trans-DMRs, by definition, are not driven by local (cis) variation, and the lack of proximity to CpG-disrupting SNVs is expected. Clarifying what additional insight this analysis provides beyond this expectation may improve this section.

We agree that the lack of proximity of trans-DMRs to CpG-disrupting SNVs is expected. We have revised the text to clarify that this analysis serves as an affirming result: it is consistent with the fact that cis-DMR are under local sequence-driven regulation, and that the CpG-disrupting SNV mechanism is more closely associated to cis-DMRs than trans-DMRs. The quantifications for distance distributions are shown in Figure 3D, and we have added a sentence noting the median distances for trans-DMRs vs. cis-DMRs: 24 ± 6 bp vs. 11 ± 2 bp.

One potential extension would be to examine whether the same cis-acting SNVs are consistently associated with methylation differences across multiple cell types.

We thank the reviewer for this suggestion and have performed this analysis below. For each of the three regulatory region classes (promoters, enhancers, CTCF binding sites), we intersected CpG SNVs (±100 bp window) with cis-classified DMRs (pure_cis or cis_plus_trans at BH-corrected FDR < 0.05) across the five cell types (CNCC, DA, HEP, IPSC, SKM), and counted the number of cell types in which each SNV overlapped a cis-DMR. To assess significance, we compared this distribution to a permutation null in which, for each cell type, we randomly sampled the same number of regions from that cell type's pool of tested-but-conserved regions of the same class (1,000 permutations); SNVs were restricted to those falling within the tested universe across cell types.

Local methylation effects of CpG SNVs were shared across cell types substantially more than expected by chance in all three region classes. The observed mean number of cell types sharing per SNV-in-cis-DMR was 1.244 vs. 1.077 ± 0.006 in the null for promoters, 1.133 vs. 1.042 ± 0.001 for enhancers, and 1.171 vs. 1.061 ± 0.002 for CTCF binding sites (all p < 0.001). Fold-enrichment scaled sharply with the degree of sharing: at the highest sharing level (cis-DMR in all five cell types), observed counts exceeded the permutation null by ~3,500-fold for promoters, ~800-fold for CTCF, and ~700-fold for enhancers. The slightly stronger consistency signal at promoters relative to enhancers is consistent with the more constitutive activity of promoter elements across cell types. These results indicate that the same cis-acting variants tend to drive methylation divergence across multiple cell types, supporting a shared mechanistic basis for cis-methylation divergence. We have added the figure in the main text as Figure 3—figure supplement 2.

Regarding their two-step sign test analysis, because enrichment-based approaches can sometimes overemphasize statistical significance without reflecting effect size, I wonder if incorporating the magnitude of methylation change would provide additional information.

We agree. The magnitude of methylation change (effect size) for each gene and gene set is now provided in Supplemental File 7 alongside the directional bias statistics. We have added a sentence to the Results pointing readers to this resource.

Strength:

I recommend that the authors provide a list of cis-cis-regulated promoters and their associated genes, which would be a valuable resource for the field.

We have added this list as Supplemental File 8.

Reviewer #3 (Public review):

Ma et al. use human-chimpanzee tetraploid cells to examine species differences in DNA methylation... Both identified SNVs and transcription factors are good candidates for future experimentation. Further, they find that cis-DMRs are more highly correlated with cis-expressed genes than trans-DMRs with trans-expressed genes, providing evidence that methylation and expression are linked genome-wide.

We thank Reviewer 3 for this summary and for the detailed recommendations.

Weakness

(1) Strengthening their cis/trans analysis, including: (a) only showing or analyzing genomic regions that pass FDR correction; (b) clarifying how cis genes are defined (Figure 2B shows some genes labeled as cis where the direction-of-effect differs between hybrid and parent cells); (c) assessing how well powered they are to perform each analysis.

(a) Figure 2B has been updated to show regulatory classifications of promoter regions in cranial neural crest cells (CNCCs) at FDR < 0.05. Scatter plots and bar plots for all cell types at the level of individual CpG sites have been moved to Figure 2—figure supplement 1, and the corresponding promoter-level plots for all cell types other than CNCCs to Figure 2—figure supplement 2. We have clarified in the Figure 2—figure supplement 1 caption that nominal p-values are used to preserve the full dynamic range of the data, whereas FDR-corrected thresholds are applied for visualization of promoter scatter plots as well as all formal inference and for reporting significant candidate loci. FDR-corrected results are presented in Figure 2—figure supplements 1–2, and we have added explicit statements in the Results confirming that the cis: trans ratio is stable across FDR thresholds.

(b) We have clarified the definition of cis-regulated genes in the text: cis-regulated genes are defined as those where the direction of allelic difference is consistent between hybrid and parental samples for both methylation and expression. We have verified that this definition is applied consistently throughout the manuscript and downstream analyses.

(c) We have clarified the FDR correction approach for the sign test in the Methods: FDRs are estimated by permutation (10,000 permutations), and we report results at FDR < 0.25 for the two-step test with supporting evidence from the methylation-only sign test (nominal p < 0.05). We acknowledge that this is a relatively liberal threshold. The sign test itself provides direct evidence that the implicated gene sets are under lineage-specific selection; what we have toned down is the downstream interpretation, framing the link between these gene sets and specific human phenotypes as inferential and requiring experimental validation rather than as confirmed.

(d) We agree that experimental validation would strengthen the mechanistic claims. We have added this explicitly to the Limitations section: "definitive demonstration of causality requires targeted experimental perturbations such as base editing (for CpG-disrupting SNVs) or TF knockdown/overexpression experiments (for trans-acting TFs)."

(2) Softening claims about human evolution or human specificity for several reasons: (a) Their comparison lacks tetraploid controls (e.g. human-human tetraploids and chimp-chimp tetraploids) or experimental follow-up in diploid cells, making it hard to be certain that observed effects are not due to ploidy. (b) There are no outgroup species included in the analysis. (c) The use of no or very loose FDR corrections with the sign test makes it difficult to draw conclusions. (d) Experimental data to link SNVs to changes in cis methylation or identified transcription factors to changes in trans methylation would be needed to validate the authors' predictions.

(a) The concern about ploidy effects is noted. We note, however, that the primary evidence for cis-regulation comes from allele-specific methylation within the same tetraploid nucleus, where both alleles experience identical ploidy and trans-environments. Ploidy effects would be expected to affect both alleles equally and would therefore not produce the allele-specific differences we observe. We acknowledge that single-species tetraploid controls would provide additional confidence and represent a valuable future experiment.

(b) We have added the absence of an outgroup species as an explicit limitation in the Discussion.

(c) We have clarified the FDR correction approach for the sign test in the Methods: FDRs are estimated by permutation (10,000 permutations), and we report results at FDR < 0.25 for the two-step test with supporting evidence from the methylation-only sign test (nominal p < 0.05). We acknowledge that this is a relatively liberal threshold and have emphasized this by adding a new sentence: “However, as indicated by the FDR, we do expect some fraction of these candidate gene sets to be false positives.”

(d) We agree that experimental validation would strengthen the mechanistic claims. We have added this explicitly to the Limitations section: "definitive demonstration of causality requires targeted experimental perturbations such as base editing (for CpG-disrupting SNVs) or TF knockdown/overexpression experiments (for trans-acting TFs)."

Reviewer #3 (Recommendations for the authors):

(1) Why are dental pulp stem cells so different from the other cell types transcriptionally (e.g. Figure 1C)? Is this due to being primary cells vs. stem-cell-derived cells?

The transcriptional distinctiveness of DPSCs is most likely attributable to their status as primary cells rather than iPSC-derived cells. Primary cells retain the epigenetic and transcriptional signatures of their tissue of origin and have not undergone reprogramming, whereas iPSC-derived cell types share a common pluripotent origin that may reduce inter-cell-type transcriptional distance. Additionally, DPSCs are mesenchymal stem cells with a distinct developmental lineage and were obtained from adult donors rather than differentiated in vitro, which may further contribute to their distinct profile. We have added a brief note to the Results acknowledging this.

(2) I am concerned about how cis genes are defined. In Figure 2B, there are genes labeled as cis, where the direction-of-effect differs between hybrid and parent cells. I believe cis should only include genes with the same direction-of-effect between hybrid and parent cells, as illustrated in Figure 2A. This fix should propagate through the ensuing figures and results.

We have clarified the definition of cis-regulated genes in the text (see response to Weakness 1b above). The classification framework assigns a site to "cis" when the allele effect test is significant in hybrids and the System × Allele interaction term is not significant, meaning there is no detectable change in the allelic difference between the hybrid and parental systems. Sites where the allelic difference genuinely differs between systems — that is, where the interaction term is significant — are classified as cis × trans (interactive) or cis + trans (additive) rather than pure cis, depending on whether the two systems disagree in direction or only in magnitude.

We note that Figure 2B plots parental and hybrid methylation differences as the per-sample average difference in fractional methylation, which is used for visualization only. Points labeled cis that fall on the opposite side of the y = x diagonal are an artifact of this averaging: where the underlying difference is close to zero, the coverage-weighted per-sample average can flip sign even though the beta-binomial model, which fits the read counts directly and accounts for coverage and overdispersion, finds no significant interaction. The regulatory classification is based on the model, not on the sign of the averaged difference, so a small amount of scatter around the diagonal is expected. We have verified that this definition is applied consistently throughout the manuscript and downstream analyses and have clarified the caption of Figure 2B to make this explicit.

(3) Are you equally powered to detect cis and trans effects?

At the single-CpG level, the two hypotheses do differ in statistical power, but at the regional level this difference is mitigated by the higher effective read depth, and we now state this explicitly in the revised manuscript.

The first hypothesis in our classification framework tests allele-specific methylation directly, whereas the second hypothesis includes an interaction term that evaluates whether allelic differences shift between the parental and hybrid systems. Because the interaction test is inherently less powerful, it requires greater sequencing depth and, ideally, additional replicates to yield comparably confident estimates and to assign sites to certain classification categories with significance. As a consequence, at the single-CpG level, trans effects are more sensitive to FDR thresholds than cis effects of equivalent nominal significance, which reduces our power to detect them. At the regional level, however, as well as in CpG-level analyses with high-coverage samples, this disparity in power between cis and trans largely disappears.

This is the technical component of the issue. From a biological standpoint, cis effects are also intrinsically easier to detect than trans effects: estimates of trans effects necessarily incorporate not only trans-acting molecular mechanisms but also environmental and technical noise, so cis estimates will always be cleaner. This is a well-recognized limitation of existing cis/trans classification frameworks, and we acknowledge this limitation in the discussion and have added suggestions in experimental set-up to mitigate it. To address the reviewer's concern directly, we have performed a formal power analysis quantifying the relative power to detect cis and trans effects as a function of read depth (See Author response image 1).

(4) Are the results shown for SNVs in CpGs in Figure 3C only for cis-DMRs or for all DMRs? If the latter, please show cis-DMRs and trans-DMRs separately and explain why trans-DMRs show the same pattern as cis-DMRs. In addition, I would expect that the CpG that contains an SNV leading to CpG loss or gain would be the most affected in terms of methylation status, rather than CpGs within 25bp vs. 50bp vs. 100bp. It would be helpful to see that plot as well.

We thank the reviewer for the opportunity to clarify. Figure 3C is not an analysis stratified by cis-DMRs or trans-DMRs. Rather, it examines local methylation changes at conserved CpG sites located within 25 bp, 50 bp, and 100 bp of a CpG-disrupting SNV. The purpose of this analysis is to test a specific mechanistic hypothesis: that a CpG-disrupting mutation may influence the methylation status of nearby, intact CpG sites in cis. The analysis is therefore agnostic to cis/trans-DMR classification, as it asks a different question, namely whether sequence disruption at one CpG propagates locally to neighboring CpGs.

We note that Figure 3D addresses a related but distinct question, showing that cis-acting sequence changes more broadly (not restricted to CpG-disrupting mutations) are more strongly associated with cis-DMRs than with trans-DMRs. Together, Figures 3C and 3D support complementary aspects of the cis mechanism: the local propagation of methylation changes around disrupted CpGs (3C) and the broader association of sequence variation with cis-DMRs (3D).

Regarding the reviewer's second point: we agree that the CpG site directly disrupted by the SNV would itself be the most affected, by definition, since the CpG dinucleotide is destroyed (in the case of CpG loss) or newly created (in the case of CpG gain). Because methylation cannot be measured at a CpG that no longer exists (or has only just been created on one allele), this site cannot be included in a comparative methylation analysis across alleles or species. The 25/50/100 bp windows were therefore chosen specifically to test the local effect on conserved, measurable CpGs surrounding the disruption. We have clarified this rationale in the revised text/figure legend.

(5) The finding that cis-DMRs and cis-expressed genes are more correlated than trans-DMRs with trans-expressed genes is nice to see. What is a potential explanation for why the patterns across the genomic interval surrounding the TSS are so different across cell types, and even positively correlated near the TSS in dopaminergic neurons? Why do you not see a difference between cis and trans in CNCCs? In addition, it would be nice to see the correlation between cis-DMRs and trans-expressed genes, and vice versa, as a control for these plots.

We have added the suggested control analysis. For the cis-DMR/trans-expressed-gene and trans-DMR/cis-expressed-gene sets in both DA neurons and CNCCs, the correlations around the TSS are less consistently negative than for the cis-DMR/cis-expressed-gene set. In both cell types, cis-methylation and cis-expressed genes show the strongest opposing (negative) relationship to one another, which supports the specificity of the cis–cis coupling reported in Figure 4G. Regarding why the correlation profiles across the TSS-flanking interval differ so markedly across cell types—including the positive correlation near the TSS in dopaminergic neurons—and why the cis–trans distinction is less pronounced in CNCCs, we are not able to offer a confident explanation. The variation may reflect cell-type-specific regulatory architecture, but a great deal remains unknown about how methylation and transcription are coupled in a cell-type-specific manner, and our four cell types do not allow us to distinguish among the possible explanations. We think this is an open and interesting question, and that analyzing additional cell types with matched WGBS and gene expression data would be the most informative way to establish how general these patterns are and what drives the between-cell-type variation. We have noted this explicitly in the main text.

Author response image 4.

Spearman correlation of expression and methylation for CNCC and DA for subsets of genes with cis-regulated methylation and trans-regulated expression (orange), as well as genes with trans-regulated methylation and cis-regulated expression (blue). Two kb surrounding each transcription start site (TSS) is shown, split into 10 bins of 200 bp where individual CpG sites are pooled and averaged as fractional methylation values and correlated with expression values of the neighboring genes (in TPM).

(6) The use of the sign test to identify pathways with the same direction of effect is a great approach. However, I am concerned with the use of no or very loose FDR corrections (e.g. FDR < 0.25 in line 372 and no FDR correction in line 374). Combined with Figure 6, where many of the signals appear to be weak or driven by a few genes (e.g. highly arched eyebrow and poor speech), it makes it difficult to draw robust conclusions. It is notable that the strongest signal is seen in DPSCs, which the authors note contains experimental confounds. We also think that the authors should tone down their biological interpretations, particularly for stem cells. For instance, COLEC11 is involved in neural crest cell migration but is identified from the iPSC analysis and not the CNCC analysis. Why not?

We have added a sentence to emphasize the possibility of some false positive sign test results (“However, as indicated by the FDR, we do expect some fraction of these candidate gene sets to be false positives”), and we have toned down the biological interpretations accordingly.

We want to clarify that the sign test directly demonstrates that these gene sets are under lineage-specific selection. We have clarified that the test does not establish a definitive link between these gene sets and specific human phenotypes; that link is inferential and would require experiments or further validation, and we have toned down the biological interpretations accordingly.

Regarding COLEC11: in response to this comment, we directly examined COLEC11 expression and methylation in CNCCs and found that it is in fact significant in this cell type. In CNCC hybrid cells, COLEC11 shows significant chimpanzee-biased allele-specific expression (log2 fold change [human/chimpanzee allele] = –2.45; DESeq adjusted p = 0.005), together with significant human-biased methylation (fractional methylation [human – chimpanzee] = 14%; adjusted p < 0.001). The direction of this divergence is therefore consistent with IPSC. The reason COLEC11 did not surface at the pathway level in CNCCs is that other genes in the same pathway contribute to the directional signal for that cell type; we would not expect every individual gene to emerge in the cell type where its pathway is most relevant. We have added a note making this point and cautioning against over-interpreting any single gene example.

(7) We appreciate that the authors provide a careful list of limitations of their study. In addition to the limitations listed, the authors should also include that experiments would be needed to validate that SNVs disrupting or creating CpGs affect methylation.

We have added this to the Limitations section: “definitive demonstration of causality requires targeted experimental perturbations such as base editing (for CpG-disrupting SNVs) or TF knockdown/overexpression experiments (for trans-acting TFs).”

(8) We also caution the authors in describing their findings as "human-specific" because there is no outgroup in this study.

We agree and have added the absence of an outgroup as an explicit limitation in the Discussion.

We thank all three reviewers again for their thorough and constructive engagement with our work. We believe the revised manuscript is improved as suggested.

eLife Assessment

This computational study constitutes an extension to prior work on biophysical calcium-based synaptic plasticity rules, investigating how the regulation thresholds for strengthening and weakening connection help solve learning tasks. This important work presents a significantly simpler solution to the studied problem with potentially broad applicability, the evidence to support the core conclusions is solid.

Reviewer #1 (Public review):

Summary

This computational modelling study investigates the functional role of metaplasticity in a calcium-dependent synaptic plasticity rule, using a biophysically detailed model of a striatal projection neuron. The learning rule is deliberately simple: local calcium signals derived from different sources regulate LTP and LTD through separate plasticity thresholds, while dopamine provides a reward-related signal that determines the direction of synaptic updates. The author uses linear and nonlinear feature-binding problems (FBP and NFBP) as learning tasks to illustrate the mechanics of competing LTP and LTD processes in this rule. The central aim is thus to use these classification tasks to understand what metaplasticity in the two calcium thresholds contributes to learning.

The study identifies complementary roles for metaplasticity in the LTP and LTD thresholds, enabling synapses exposed to competing plasticity processes to converge toward a stable outcome. In reversal-learning tasks, relaxing the conditions for metaplasticity allows previously stabilized synaptic states to become flexible again and permits relearning. Finally, the manuscript investigates whether two separate calcium thresholds are themselves necessary. While a modified rule with a single adaptive calcium threshold can solve the same tasks comparably well, two thresholds allow separate control over synaptic strengthening and weakening.

Strengths

A major strength of the study is the simplicity of the learning rule, which makes it possible to dissect the roles of individual components while retaining a connection to experimentally motivated mechanisms of cortico-striatal plasticity. The use of shared features in the FBP and NFBP is useful for exposing the interaction between competing LTP and LTD processes and for showing how adaptation of one plasticity threshold can indirectly permit expression of the opposite form of plasticity.

The manuscript also provides a much more systematic analysis of the rule than the original version. In particular, the expanded parameter analyses explore both successful and failing regimes for the learning and metaplasticity rates, while the scan over the maximum synaptic weight provides a clear mechanistic motivation for the additional upper LTP threshold.

Importantly, the single-threshold simulations directly address whether two calcium thresholds are computationally necessary. These additional simulations clarify that the principal advantage of two thresholds is not that they uniquely enable nonlinear learning, but that they permit independent regulation of strengthening and weakening. This considerably strengthens the conceptual conclusions of the study.

Weaknesses

The main limitations concern the scope and biological generalizability of the results. The simulations in this paper are based on a particular detailed SPN model and depend on several specific biological and modelling assumptions. Most notably, solving the nonlinear task requires appropriately clustered excitatory inputs, but the learning rule itself does not provide a mechanism for generating these clusters. The manuscript now discusses this limitation explicitly and appropriately identifies structural plasticity as an important direction for future work.

A second important assumption is the upper calcium threshold that prevents LTP once sufficiently strong supralinear responses are reached. This mechanism plays an important functional role in the model but has not been experimentally established for cortico-striatal synapses. The manuscript appropriately identifies this as a major assumption and discusses potential molecular mechanisms that could implement such an effect.

Overall assessment

The revised manuscript is substantially stronger. The conclusions are carefully matched to what is demonstrated by the simulations, and several important alternative explanations and model configurations are tested directly. In particular, the revised framing provides a more specific mechanistic account of what metaplasticity in two separate thresholds contributes within the proposed rule. The work therefore provides a valuable contribution to computational studies of synaptic plasticity and metaplasticity, with convincing evidence supporting its principal conclusions.

Reviewer #2 (Public review):

Summary:

The manuscript proposes interesting synaptic plasticity rules grounded in experimental data. Its main features are: (1) plasticity depends on local calcium concentration driven by presynaptic activity and is independent of somatic action potentials, (2) the rules incorporate metaplasticity, and (3) they demonstrate how a single neuron could address the feature-binding problem at the dendritic level.<br /> The work extends a previous study (https://doi.org/10.7554/eLife.97274.2), to which the author also contributed.

The author models two calcium thresholds (LTP/LTD) from two different calcium sources (NMDA/VGCC) and these thresholds are flexible (metaplasticity rule, similar to BCM) which is claimed to be necessary for successful learning of both FBP and NFBP (linear and nonlinear feature binding problem with 1 or 2 patterns). The role of each threshold seems to be is opposite and complementary. One extra condition has been added : an upper threshold for LTP. This threshold serves to stop synaptic strengthening once synapses are strong enough to evoke a plateau. With that, synapses are not strengthened to the maximal value, avoiding strong supralinear integration for irrelevant patterns.

Strengths:

The current model implements not only local synaptic plasticity but also metaplasticity and solves the FBP at the dendrite level. Another strong aspect of the model is that metaplasticity in the LTD threshold protects strengthened synapses from weakening. In this way, as the author mentioned, metaplasticity is able to protect learned patterns from being forgotten or weakened and prevent irrelevant patterns from being stored. This is a nice modelling example of metaplasticity being helpful in preventing the catastrophic interference or forgetting (as has been explicitly discussed in a recent article https://doi.org/10.1016/j.tins.2022.06.002). The author might want to briefly mention or emphasize this aspect of the model, which might be interesting also for the AI community.

Comments on revised version:

The author improved the paper significantly. He conducted new simulations on relearning. He addressed the problems and limitations, added new simulation results and reasoned better in the discussion and the introduction. Also, the figures are improved.

Author response:

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

The goal of the study was to demonstrate the role of the two thresholds in learning, i.e. the role of metaplasticity with a learning rule that is both as simple as possible, but also biologically-based (hence the use of the detailed SPN model, as well). The goal was not to solve the FBP and NFBP with a different rule. However, the text likely gives that impression. Therefore, in addition to addressing the reviewers’ comments, the text has been substantially revised to reflect the following:

Main results

(1) Metaplasticity enables synapses that undergo both LTP and LTD to ultimately express just one plasticity outcome (either LTP or LTD).

(2) Metaplasticity in the LTP threshold allows LTD to be expressed, and vice versa. (That is, the threshold regulating one plasticity process allows the expression of the opposite plasticity process.)

Reason for using the FBP and NFBP

The reason why the FBP and NFBP are particularly useful to demonstrate the thresholds’ roles is that the patterns in the tasks share features. (For example, in the FBP, the feature ‘strawberry’ is shared between both ‘red strawberry’ and ‘yellow strawberry’.) The synapses for these shared features experience precisely such competing LTP and LTD processes where the role of metaplasticity becomes evident. Specifically, the role of the LTD threshold is visible in shared synapses that need to be strengthened during learning (such as the shared ‘strawberry’ synapses in the FBP), while the LTP threshold’s role is visible in shared synapses that need to be weakened (there are no such synapses in the FBP, but there are in the NFBP, which is why it is needed in this article). In addition, feature binding is relevant for the striatum (now described in the introduction).

In the first version of the article there are sentences that are likely confusing and misleading regarding the goal of the study, and these have been removed (lines 98-100 in the tracked changes file).

The revised article now contains 4 new main figures and 15 new figure supplements prompted by the reviewers’ comments, thus expanding the scope of the study and hopefully clarifying its content, the mechanisms, and the conclusions.

Finally, the question whether this rule can solve the NFBP with excitatory synapses alone is being addressed in a new, ongoing study, as written at the end of the Discussion section in the first version of this article. The new study tests 100+ SPN models (71 dSPN and 34 iSPN models differing in ion channel composition, with two different morphologies), different locations of the synaptic clusters along the dendrites (from proximal to distal), and two different learning regimes (suprathreshold – where the neuron initially spikes for all patterns, and subthreshold – where the neuron is initially silent for all patterns, as in this study) containing both clustered and distributed synapses in the same setup. Where necessary, preliminary results from this study are attached in the responses.

Public Reviews:

Reviewer #1 (Public review):

Summary:

This computational modelling study addresses the important question of how neurons can learn non-linear functions using biologically realistic plasticity mechanisms. The study extends the previous related work on metaplasticity by Khodadadi et al. (2025), using the same detailed biophysical model and basic study design, while significantly simplifying the synaptic plasticity rule by removing non-linearities, reducing the number of free parameters, and limiting plasticity to only excitatory synapses. The rule itself is supervised by the presence or absence of a binary dopamine reward signal, and gated by separate calcium-sensitive thresholds for potentiation and depression. The author shows that, when paired with a strong form of dendritic non-linearity called a "plateau potential" and appropriate pre-existing dendritic clustering of features, this simpler learning mechanism can solve a non-linear classification task similar to the classic XOR logic operator, with equal or better performance than the previous publication. The primary claims of this publication are that metaplasticity is required for learning non-linear feature classification, and that simultaneous dynamics in two separate thresholds (for potentiation and depression) are critical in this process. By systematically studying the properties of a biophysically plausible supervised learning rule, this paper adds interesting insights into the mechanics of learning complex computations in single neurons.

As mentioned in the introductory response above, the goal of the article was not to solve the NFBP, but to study the role of metaplasticity. The text has now been substantially revised to reflect that. One of the primary claims that “metaplasticity is required for learning non-linear feature classification, and that simultaneous dynamics in two separate thresholds (for potentiation and depression) are critical in this process” is now removed from the abstract. Instead, the abstract now focuses on the main results regarding the role of metaplasticity, as well as the results which arose from addressing the reviewers’ comments. However, I guess I should note that to be able to study the role of metaplasticity using the FBP and the NFBP, it was first necessary to have a rule that solves these tasks – that allows to later observe the effects of systematically fixing or modifying parameters in the rule. Another aspect which may have added to the confusion about the study’s goal may be due to the NFBP being a complex task requiring supralinear dendritic integration. Because of this, plateaus have received significant attention in the article, possibly diverting from the main focus. This is also now clarified in the article.

Strengths:

The simplified form of the learning rule makes it easier to understand and study than previous metaplasticity rules, and makes the conclusions more generalizable, while preserving biological realism. Since similar biophysical mechanisms and dynamics exist in many different cell types across the whole brain, the proposed rule could easily be integrated into a wide range of computational models specializing in brain regions beyond the striatum (which is the focus of this study), making it of broad interest to computational neuroscientists. The general approach of systematically fixing or modifying each variable while observing the effects and interactions with other variables is sound and brings great clarity to understanding the dynamic properties and mechanics of the proposed learning rule.

It would indeed be great if this rule facilitates similar studies in other neuron types. The rule requires at least qualitatively accurate calcium dynamics, which at the moment are not widely available for other neuron types (but will likely appear in the future).

Weaknesses:

General notes

(1) The credibility of the main claims is mainly limited by the very narrow range of model parameters that was explored, including several seemingly arbitrary choices that were not adequately justified or explored.

The parameter range has now been expanded to address all comments below.

(2) The choice to use a morphologically detailed biophysical model, rather than a simpler multicompartment model, adds a great deal of complexity that further increases uncertainty as to whether the conclusions can generalize beyond the specific choices of model and morphology studied in this paper.

Regarding the plasticity rule and the role of metaplasticity, the conclusions should hold if the calcium dynamics of other (simpler or detailed) neuron models is qualitatively similar (i.e. shows the same monotonicity of “stronger synaptic input – stronger calcium”, and not something like Figs. 12A, B for which the rule was not tested).

As to whether the NFBP can be solved, that is being addressed in the new study with 100+ neuron models (71 dSPN models and 34 iSPN models, and two morphologies: one for the dSPNs and another for the iSPNs). So far, the results show that the important ingredient is the threshold nonlinearity provided by the plateau potential (both dSPNs and iSPNs exhibit this nonlinearity, irrespectively of where the synaptic cluster is located, see Author response image 1).

Also, plateaus can be evoked in passive SPN dendrites (as stated in the methods in lines 916-919, by “turning off” ion channels in the computational model as in Fig. S7 of Du et al. (2017) (see list of references provided)). Although plateaus are somewhat modified by active conductances, the main behavior important for the NFBP is given by NMDARs. The most striking contributions of the other ion channels in SPNs are the low resting potential around -85 mV, delayed first spike under current injection and strong inward rectification. Basically, SPNs require more input to be stimulated compared to other neurons that lack these properties. So, other neurons with NMDAR-dependent nonlinearities should in principle be able to solve the same task, but perhaps needing less inputs (provided dendritic integration is sufficiently supralinear – see response to comment (2) under Reviewer #2 (Recommendations for the authors)).

(3) The requirement for pre-existing synaptic clustering, while not implausible, greatly limits the flexibility of this rule to solve non-linear problems more generally.

In my view, the limitation of this rule is that there is no mechanism for structural plasticity with which clusters could be “grown”. For example, Hedrick et al. 2022 demonstrate that during learning in the motor cortex, existing functional clusters are “enlarged” by growing new spines. Devising a biologically realistic rule for structural plasticity is a separate research project, which would be very interesting to do.

In any case, to solve the NFBP with excitatory synapses alone, supralinear voltage elevations are necesssary (Tran-van-Minh et al. 2015). When it comes to NMDAR-dependent supralinear integration, clustering is basically necessary, within a smaller, e.g. 20 micron dendritic stretch, or more loosely, within a single dendritic branch (Losonczy and Magee, 2006; Branco et al. 2010). Also, synaptic clustering is quite present across different brain regions (such as the sensory and motor cortices, pallium, striatum, hippocampus, brainstem, the developing cortex, and across species, e. g. see the introduction of Kirchner and Gjorgjieva, 2021), so I suppose it is not that implausible. Inputs from motor cortex to striatum are also clustered (Hwang et al. 2022).

(4) In order to claim that two thresholds are truly necessary, the author would have to show that other well-known rules with a single threshold (e.g., BCM) cannot solve this problem. No such direct head-to-head comparisons are made, raising the question of whether the same task could be achieved without having two separate plasticity thresholds.

Although the goal of the study was not to solve the NFBP, this is a very interesting question related to the question “what is the use of having two separate thresholds for plasticity”? I have added simulations in which the rule is modified to use a single calcium threshold instead, showing that the FBP, NFBP, and reversal learning are solved just as well (Fig. 12 and Figure 12 – figure supplements 1 – 4). The results show that two calcium thresholds allow for separate control over the LTP and LTD processes (lines 687-706).

Specific notes

(1) Regarding the limited hyperparameter search:

(a) On page 5, the author introduces the upper LTP threshold Theta_LTP. It is not clear why this upper threshold is necessary when the weights are already bounded by w_max. Since w_max is just another hyperparameter, why not set it to a lower value if the goal is to avoid excessively strong synapses? The values of w_max and Theta_LTP appear to have been chosen arbitrarily, but this question could be resolved by doing a proper hyperparameter search over w_max in the absence of an upper Theta_LTP.

Thank you for raising this question – it is closely related to the very important question of when to stop updating the weights. Before providing the response, I should clear up any confusion made due to an error in notation. In this study, , and , meaning that during learning the weights can increase up to twice (up to 100% of) the initial value, and can decrease down to 1% of the initial value. Currently, it says w_max = 2, and w_min = 0.01, which is a mistake, and possibly a reason why the chosen values seem arbitrary.

The reason for introducing the upper threshold θ_LTP is most easily seen in the parameter scan for w_max done in the absence of θ_LTP (Figure 4 – figure supplement 4) – it is very difficult to choose a value for w_max with which all three tasks will be solved (FBP with linear integration, i.e. distributed synapses, the FBP with supralinear integration, i.e. clustered synapses, and the NFBP). Put differently, if there is a range of w_max values which solves all three tasks, it is very narrow. So, θ_LTP is introduced to solve all three cases without specially tuning w_max.

The following is a description of the results in Figure 4 – figure supplement 4, which is also present in the article in lines 383-396. The reason why a single preset value for w_max does not work is that distributed synapses sum only linearly at the soma, while clustered synapses sum supralinearly. This means that to trigger somatic spiking, the distributed synapses need to be strengthened more compared to clustered synapses. Concretely, this means that a is needed to solve the FBP with linear integration (distributed synapses), but it is already too strong to solve the NFBP (Figure 4 – figure supplement 4, column four: top panel shows that FBP with linear integration is solved, while the bottom panel shows the average performance for the NFBP is right at the border – pink line aligns with the dashed line). On the other hand, is enough in the FBP with clustered synapses and the NFBP to trigger glutamate spillover and a plateau potential, which drives somatic spiking (Figure 4 – figure supplement 4, column two). However, it is not enough to solve the FBP with linear integration. Larger values for w_max increase the performance on the FBP with linear integration, but lower the performance on the NFBP due to spiking for the irrelevant patterns (especially visible once ). As said, in this parameter scan, only the value solves all three tasks, with borderline performance on the NFBP (it is arguable whether the borderline performance means the NFBP is solved). This suggests that if a range of values for w_max exists which solves all three tasks, it is very narrow.

With the settings used in the study, the w _max threshold for triggering glutamate spillover is a number between 1.2 and 1.3 with many decimals – 1.230769231. A possibility could be to program spillover to always occur at , but this is also not a general solution. For example, other dSPN models from the model library in Lindroos et al. (2021) have different excitability, and that would mean a different, specific value of w_max would be needed for each neuron model.

θ_LTP is thus a solution that prevents “over-excitation” in a dendrite. The logic is that synapses in a cluster do not need to be as strong as distributed synapses to be effective in exciting the neuron. θ_LTP ensures that once plateaus appear, synapses are not strengthened further. This allows using the same value across all scenarios, i.e. avoiding tuning of w_max or tuning the number of synapses representing the features. (Also, preliminary results show this works well in the new study which tests all dSPN and iSPN models in the model library.) As for the value of θ_LTP, it can be set anywhere in the “blank” region in Fig. 2C₃ where the supralinear jump in [Ca]_NMDA occurs. What is important is that [Ca]_NMDA evoked by a plateau should be above θ_LTP – then no more strengthening will occur once plateaus can be evoked.

(b) The author does not explore the effect of having separate learning rates for theta_LTP and theta_LTD, which could also improve learning performance in the NFBP. A more comprehensive exploration of these parameters would make the inclusion of theta_max (and the specific value chosen) a lot less arbitrary.

I am not sure I have understood this comment properly, but hopefully this response addresses it adequately. In fact, the computer code does use separate variables for the learning rates for θ_LTP and θ_LTP, but for simplicity, they are set to the same value. In this response I have included some simulations in which they are set to different values (Author response image 2), but to understand their effect it is better to read the response to the comment under c) first. The metaplasticity rates determine how fast the synaptic weights are stabilized, i.e. how long the time window is where the synapses are “flexible”. When the thresholds reach the calcium amplitudes, the weights are “locked”.

If the metaplasticity rates are too low, the weights take a longer time to stabilize and solving the tasks takes a long time (Figure 4 – figure supplement 10 from the response to c). If they are too high, weights are quickly stabilized and, in the case of weakened synapses, prematurely so, leading to worse performance on the NFBP due to spiking for the irrelevant patterns. (Figure 4 – figure supplement 11).

One can use different values for the metaplasticity rates, as in the examples in Fig. 2 , and this affects the speed of learning. A large η_θLTD = 20 quickly prevents the LTD process (Figs. 2D₁, D₂), causing faster synaptic strengthening, but also quickly limiting weakening (Figs. 2B₁, B₂) – as a result, after learning, the neuron spiked for an irrelevant pattern (Fig. 2A₁). Conversely, a large η_θLTD = 20 quickly prevents the LTP process (Figs. 2C₃, C₄), prolonging synaptic strengthening and allowing faster weakening (Figs. 2B₃, B₄) – as a result, the NFBP is solved, but takes a longer time. However, this does not remove the need for using an upper threshold θ_LTP. If I have not understood the comment properly, please let me know so I can address it further.

(c) Figure 4 Supplements 3-4: The author shows results for a hyperparameter search of the learning rule parameters, which is important to see. However, the parameter search is very limited: only 3 parameter values were tried, and there is no explanation or rationale for choosing these specific parameters. In particular, the metaplasticity learning rates do not even span one order of magnitude. If the author wants to claim that the learning rule is insensitive to this parameter, it should be explored over a much broader range of values (e.g., something like the range [0.1-10]).

Thank you for bringing this up! I have expanded the parameter scan for both the learning rate η (Figure 4 – figure supplements 7 and 8) and the metaplasticity rate η_θ (Figure 4 – figure supplements 10 and 11) to cover three orders of magnitude (when taken together with the results already present in the article in Figure 4 – figure supplements 6 and 9).

Figure 4 – figure supplements 7 and 8: The learning rate η was was tested with the values 0.1 and 20. This shows a known result in other plasticity rules, which is that if the learning rate is too fast or too slow, learning is not successful or is too slow. For η = 0.1, learning takes very long (around 2000 patterns for FBP with linear integration), and for the NFBP is at the borderline score (Figure 4 – figure supplement 7E). As the LTD thresholds rise, they will prevent the slowly decreasing synaptic weights from decreasing sufficiently. For η = 20, the weight updates are too large and no pattern is stored because calcium quickly falls below the thresholds as a result of such large weight updates (Figure 4 – figure supplement 8E). This leaves some intermediate range of learning rates that “works”. (The three values {0.4, 0.85, 1.7} that were tested in Figure 4 – figure supplement 6 are roughly a factor of 2 apart.) Results are described in more detail in lines 409-414 of the revised article.

Figure 4 – figure supplements 10 and 11: The metaplasticity rate η_θ was tested with the values 0.2 and 20. This further demonstrates the role of metaplasticity as a “lock” on the learning process. η_θ determines how fast the weights stabilize (i.e. how long they remain flexible for learning). With the value η_θ = 0.2 the weights take a longer time to stabilize, because it takes a long time for the thresholds to reach the calcium amplitudes (Figure 4 – figure supplement 10). This affects the learning time on the NFBP only. In contrast, with the value η_θ = 20, the thresholds quickly reach the calcium amplitudes, and quickly stabilize the weights. While the neuron does learn to evoke plateaus, the weakened synapses are stabilized too early, resulting in spikes for the irrelevant patterns and lowering the performance on the NFBP. (Figure 4 – figure supplement 11). Results are described in more detail in lines 415-429 of the revised article.

(2) Regarding the similarity to BCM, the author would ideally directly implement the BCM learning rule in their model, but at the least the author could have shown whether a slight variant of their rule presented here can be effective: for example having a single (plastic, not fixed) Cadependent threshold that applies to both LTP and LTD, with a single learning rate parameter.

- As mentioned above, this is also a very interesting question, related to the important question of “what is the use of having two separate calcium thresholds?”. I have added simulations according to your second suggestion – using a single calcium threshold that applies to both LTP and LTD. A single threshold can solve the FBP, NFBP, and reversal learning equally well (Fig. 12 and Figure 12

- Figure Supplements 1, 2). This indeed raises the question what are two separate thresholds useful for? Figure 12 – figure supplement 3 shows that when keeping the single calcium threshold fixed, none of the shared synapses stabilize. Comparing this to Figs. 5 and 6, where the LTP and LTD threshold are kept fixed one at a time, it shows that having two separate thresholds allows separate control over the LTP and LTD processes.

I also tried an implementation of the BCM rule using a nonlinear (quadratic) function in the metaplasticity rule for updating the threshold:

where c_norm is a normalization constant set to 80 μM for [Ca]_NMDA and 20 μM for [Ca]_L-type (close to the maximal concentrations achieved throughout the article). In the BCM rule, a nonlinear function is necessary to prevent runaway growth (or collapse) of the weights. So, in principle, w_max and θ_LTP should be unnecessary with this quadratic metaplasticity rule. However, even though the weights seem to stabilize (around a high value), they are too strong and plateaus are triggered for all patterns (see Author response image 3). It is possible that only a narrow range of parameters in the quadratic function will allow weights to stabilize at appropriate values, similarly to the narrow range in w_max in the absence of θ_LTP (as described for comment 1a) above).

Below are some questions about how to “correctly translate” the BCM rule from its formulation for rate-coded inputs to a formulation for sparsely-coded inputs which are used in this article. I did not address these questions in detail. The following is meant for readers who might be interested in pursuing these questions.

Questions when translating the BCM rule for rate-coded inputs to a rule for sparsely-coded inputs:

The similarity of this study’s rule to BCM is only qualitative – a sliding threshold was added that follows an indicator of synaptic activity (in this study it is the amplitude of the calcium concentration). The original BCM rule is defined for rate-based synapses, and its threshold θ is a nonlinear function of the average (synaptic) activity:

where p and c₀ are positive constants, and c) is the average activity. The threshold θ is updated as the average activity c) changes (the averaging being done over a time interval) [1]. Changes in the rate-coded inputs drive changes in c) continuously, thus changing θ over time.

(1) What should be chosen as the average activity c̅ ?

In the BCM model, the average activity, and consequently the threshold θ, are global for the whole neuron (which is represented just by its firing rate), meaning that θ is the same for all synapses. In a morphologically realistic neuron model, what should be the average activity? Especially in the case of supralinear integration occuring in a dendrite, one could also consider average activities in dendrites. In the dSPN model, the calcium concentration decays by the time the next pattern arrives, so one probably needs another, low-pass filtered variable of the calcium concentration (or voltage), with a much longer time constant than that of the calcium decay. (I have chosen to slide the thresholds towards the amplitude of the calcium evoked by a pattern, which could be viewed as an approximation of such a long-lived variable. This is one possible “translation” of this aspect of the BCM rule.)

(2) How to update the chosen indicator of activity c̅?

Assuming an adequate indicator is chosen (different from the calcium amplitude that I have chosen), how should it be updated when using sparsely-coded inputs? Should it evolve continuously, or only when the sparsely-coded inputs are active? If updated continuously, it should not decay very fast when synapses are inactive (not activated by a pattern), while still change fast enough to detect changes in synaptic weight occuring due to learning. (I have chosen to slide the thresholds towards the evoked calcium amplitude only when synapses have been activated, so this is also one way of “translating” this second aspect.)

(1) which in the BCM article is replaced with the average over the input’s probability distribution

(3) What nonlinear function to use to update the threshold?

The BCM rule allows any function with p > 1, but how fast the synapses stabilize will likely depend on c₀, the normalization constant in the nonlinear function, and the power p. The role of the nonlinear function is to ensure stability of the synaptic weights (prevent runaway growth), meaning no θ_LTP nor w_max should be needed. However, achieving high performance on all three tasks might still require a specific tuning of these parameters, as w_max does if no θ_LTP is used. That is, these parameters will need to be chosen such that the threshold quickly goes up once a plateau appears, so weights are not allowed to strengthen further. Having in mind that there is a very narrow range in w_max where all three tasks are solved, there might similarly be only a narrow range in c₀ and p.

Since the goal of the article was to study the role of the two thresholds (not to optimize the rule’s parameters on the three tasks), I have only tried a quadratic function for the metaplasticity rule, and did not search for a region of parameters that could work.

(3) This paper is extremely similar (and essentially an extension) to the work of Khodadadi et al. (2025). Yet this paper is not mentioned at all in the introduction, and the relation between these papers is not made clear until the discussion, leaving me initially puzzled as to what problems this paper addresses that have not already been extensively solved. The introduction could be reworked to make this connection clearer while pointing out the main differences in approach (e.g., the important distinction between "boosting" nonlinearities and plateau potentials).

The last paragraph in the introduction now makes this comparison, highlighting the differences in approach, and mainly emphasizing that the goal of the two studies is different. The open question that this study addresses is to pinpoint the roles of the two calcium thresholds (present in dSPNs) in learning. Also see the response to the similar comment (1) from Reviewer #2 (Public review): Weaknesses.

(4) The introduction is missing some citations of other recent work that has addressed single-neuron non-linear computation and learning, such as Gidon et al (2020); Jones & Kording (2021).

Thank you for mentioning this. Since the first version of the article caused confusion regarding the goal of the study (which is to study metaplasticity), I avoided focusing on nonlinear computation in the introduction, and instead added these references to the Discussion (in line 850 the section regarding nonlinear computation).

(5) Figure 1: The figure prominently features mGluR next to the CaV channel, but there is no mention of mGluR in the introduction. The introduction should be updated to include this.

Thank you for noticing this. It is now included in the introduction in lines 50-53.

(6) Could the author explain why there is a non-monotonic increase/decrease in the [Ca]_L in Figure 2B_4? Perhaps my confusion comes from not understanding what a single line represents. Does each line represent the [Ca] in a single spine (and if so, which spine), or is each line an average of all the spines in a given stim condition?

Thank you for noticing this, that information was missing from the figure caption. The line is from a single spine which is placed at a random location on a randomly chosen dendrite. Because each line comes from a different trial with a different number of synapses, the spine it corresponds to is in a different location, resulting in different voltage and different calcium signals when using distributed synapses. (Clustered synapses are placed at approximately the same somatic distance, despite being on a randomly chosen dendrite, so this effect does not appear in Figs. 2C₃, C₄). The figure caption has been updated accordingly.

(7) Row 124 (page 4): L-type Ca microdomains (in which ions don't diffuse and therefore don't interact with Ca_NMDA) is a critical assumption of this model. The references for this appear only in the discussion, so when reading this paper, I found myself a bit confused about why the same ion is treated as two completely independent variables with separate dynamics. Highlighting the assumption (with citations) a bit more clearly in the results section when describing the rule would help with understanding.

Thank you for pointing this out! This assumption is now clearly stated with citations in lines 174176 when characterizing the plateaus in SPNs, and lines 205-207 when describing the rule (in addition to the existing description in the Methods).

(8) Row 149 (page 5): The current formulation of the update rule is not actually multiplicative. The fact that the update is weight-dependent alone does not make it a multiplicative rule, and judging by equation (1) it appears to simply be an additive rule with a weight regularization term that guarantees weight bounds. For example, a similar weight-dependent update is also a core component of BTSP (Milstein et al. 2021; Galloni et al. 2025), which is another well-known *additive* rule. An actual multiplicative rule implies that the update itself is applied via a multiplication, i.e. w_new = w_old * delta_w

For an example of a genuinely multiplicative rule, see: Cornford et al. 2024, "Brain-like learning with exponentiated gradients"). Multiplicative rules have very different properties to additive rules, since larger weights tend to grow quickly while small weights shrink towards 0.

Thank you for explaining the difference between “additive” and “multiplicative”. I have removed the word “multiplicative” from the description of the rule, as it is not necessary. (In the first version of the manuscript I followed the nomenclature by Gütig et al. (2003), which refers to the weight-dependent update as a multiplicative rule, while an additive rule has no weight dependence in the equation for Δw, which is Eq. 2 in Gütig et al. (2003).)

(9) Equation 1 (page 5): Shouldn't the depression term be written as: (w_min - w)? This term would be negative if w is larger than w_min, leading to LTD. As it is written now, a large w and small w_min would just cause further potentiation instead of depression.

Yes, a minus sign is missing in front of the depression term. Thank you for noticing this! It is now corrected.

(10) In the introduction, the teaching signal is described in binary terms (DA peak, or DA pause), but in Equation 1, it actually appears to take on 3 different values. Could the author clarify what the difference is between a "DA pause" and the "no DA" condition? The way I read it, pause = absence of DA = no DA

Yes, the “no DA” condition should say “baseline DA”. The DA signal does indeed take three different values. In the striatum, there is a baseline tone of dopamine. The DA peaks are transient increases from this tone, and the DA pauses are transient decreases. The basal dopamine level is now introduced in line 113 of the introduction, so that Eq. 1 should be clearer. In the computer code, DA is in effect a ternary signal, with three values, +1 for DA peak, -1 for DA pause, and 0 for baseline DA.

(11) Figure 3: In these experimental simulations, DA feedback comes in 400ms after the stimulus. The author could motivate this choice a bit better and explain the significance of this delay. Clearly, the equations have a delta_t term, but as far as the learning algorithm is concerned, it seems like learning would be more effective at delta_t=0. Is the choice of 400ms mainly motivated by experimental observations? On a related note, is it meaningful that the 200ms delta_t before the next stimulus is shorter than the 400ms pause from the first stimulus? Wouldn't the DA that arrives shortly before a stimulus also have an effect on the learning rule?

These time windows were chosen purely to keep the simulations as short as possible (since a computing cluster was used to run many trials). In reality, two patterns would probably arrive after a longer time window, as an animal should reach for the pattern (and in the case of these fruit patterns, eat it) which would last on the order of seconds. However, the calcium signals that trigger plasticity in these simulations are shorter than that (Figs. 2B_3,4, 2C_3,4), and only the amplitude of the signal is used to trigger plasticity. This gives an opportinity to not have to wait for several seconds between two patterns arrive (as might occur in reality), but shorten that interval and so shorten the simulation time. (This is now stated in lines 245-247 in the Results section where the rule is described, pointing to the Methods for more detials.)

Hence, the dopamine feedback is given at 400 ms after a pattern appears because the calcium amplitudes would have surely occurred by then (even if a plateau were evoked, see Figs. 2B_3,4, 2C_3,4). Similarly, the next pattern is given at 600 ms because the calcium signals would have decreased to baseline by then. (This is already explained in the Methods section in lines 1101-1117). The key implicit assumption here is that the calcium amplitude is somehow remembered by the synaptic circuitry. In experiments, dopamine feedback up to 2 seconds after synaptic stimulation can cause LTP, so it is OK to assume this (Yagishita et al., 2014). However, dopamine signaling before synaptic stimulation has no effect (Yagishita et al., 2014). (This assumption is now clearly stated in the Methods in lines 902-906.)

Lastly, in this rule, if the dopamine feedback coincides with the pattern, then whatever calcium levels were reached at that time would be used to check whether the thresholds are crossed, and these will most likely not be the maximal calcium levels (these are reached some time later, as seen in Figs. 2B_3,4, 2C_3,4).

One last note is that from your comment I got the impression that you may have understood Δt to be the time until dopamine feedback is provided. It is not, it is simply the time step in the simulation (already stated in line 211; now an additional explanation is added in lines 211-214, just in case).

(12) Figure 4C: How is it possible that the theta_LTP value goes higher than the upper threshold (dashed line)? Equation 3 implies that it should always be lower.

This is also just a choice of implementation: θ_LTP evolves independently of θ_LTP, reflecting an implicit assumption that different molecular machinery implements θ_LTP and θ_LTP. This assumption is similar to the findings in Figs. 4, 5 in Ngezahayo et al. 2000, where in weakened synapses the voltage threshold for LTD can increase (to -20 mV) above the voltage threshold for LTP (at -30 mV). (This assumption is now explicitly written out in lines 316-322.)

(13) Row 429 (page 11): The statement that "without metaplasticity the NFBP cannot be solved" is overly general and not supported by the evidence presented. There exist many papers in which people solve similar non-linear feature learning problems with Hebbian or other bio-plausible rules that don't have metaplasticity. A more accurate statement that can be made here is that the specific rule presented in this paper requires metaplasticity.

Yes, that is what is meant with that statement – that this specific rule requires metaplasticity. The text has been corrected. Thank you for noticing this.

(14) The methods section does not make any mention of publicly available code or a GitHub repository. The author should add a link to the code and put some effort into improving the documentation so that others can more easily assess the code and reproduce the simulations.

The link to the code is given in the Data availability statement. However, this statement might not appear in the manuscript files that you are receiving (it is available online and in the article PDF downloadable from eLife), so I am providing the link here, as well. The Readme.md file now describes the code, and how to reproduce figures in the article.

https://github.com/danieltrpevski/Plasticity/tree/metaplasticity

Reviewer #2 (Public review):

Summary:

The manuscript proposes interesting synaptic plasticity rules grounded in experimental data. Its main features are:

(1) plasticity depends on local calcium concentration driven by presynaptic activity and is independent of somatic action potentials,

(2) the rules incorporate metaplasticity, and

(3) they demonstrate how a single neuron could address the feature-binding problem at the dendritic level.

The work extends a previous study (https://doi.org/10.7554/), to which the author also contributed.

The author models two calcium thresholds (LTP/LTD) from two different calcium sources (NMDA/VGCC), and these thresholds are flexible (metaplasticity rule, similar to BCM), which is claimed to be necessary for successful learning of both FBP and NFBP (linear and nonlinear feature binding problem with 1 or 2 patterns). The role of each threshold seems to be opposite and complementary. One extra condition has been added: an upper threshold for LTP. This threshold serves to stop synaptic strengthening once synapses are strong enough to evoke a plateau. With that, synapses are not strengthened to the maximal value, avoiding strong supralinear integration for irrelevant patterns.

This is summarizes the learning rule well. What I should probably add is that, as mentioned in the introductory response, the article’s first version may cause some confusion about the study’s goal. The goal was to study the role of metaplasticity in the two thresholds, not to solve feature binding in particular. Nevertheless, feature binding is a very useful task to demonstrate the roles of each threshold because the patterns share features: the synapses for the shared features experience both LTP and LTD, and metaplasticity is necessary to express (or to converge to) just one plasticity state (either LTP or LTD). More specifically, the threshold for one plasticity process (e.g. LTD) is necessary to express the opposite process (e.g. LTP). However, to be able to study metaplasticity using feature binding, a prerequisite is to have a rule that can solve it. (So, in that sense, it was first necessary to show that the rule solves the tasks before exploring the roles of metaplasticity. The article has been revised to clearly state this.)

Strengths:

The current model implements not only local synaptic plasticity but also metaplasticity and solves the FBP at the dendrite level. Another strong aspect of the model is that metaplasticity in the LTD threshold protects strengthened synapses from weakening. In this way, as the author mentioned, metaplasticity is able to protect learned patterns from being forgotten or weakened and prevent irrelevant patterns from being stored. This is a nice modelling example of metaplasticity being helpful in preventing the catastrophic interference or forgetting (as has been explicitly discussed in a recent article https://doi.org/10.1016/j.). The author might want to briefly mention or emphasize this aspect of the model, which might be interesting also for the AI community.

This is a great suggestion, thank you! I have instead emphasized a related aspect of the model: that it can solve the plasticity-stability dilemma (when taking away the closed-loop implementation of metaplasticity). I did not focus on catastrophic forgetting, because in machine learning it has a slightly more specific meaning: forgetting that occurs in sequential learning of different tasks. Instead, I exemplified the plasticity-stability dilemma using reversal learning (the reward policy is switched in the middle of the simulation), which can be viewed as a special case of sequential learning of opposite tasks. So, strictly speaking, there is no demonstration that metaplasticity prevents catastrophic forgetting (in the more general sense), but there is a demonstration that it retains (stabilizes) what has been learned (within the same task). The latter does suggest that metaplasticity could help prevent catastrophic forgetting, as well.

Weaknesses:

(1) What is novel in the current paper as compared to Khodadadi et al. eLife 2025? That is not completely clear and should be made clearer. Is it only a minor difference related to the fact that the new learning rule has metaplasticity in both calcium thresholds and is simpler? This seems to be just an incremental increase in knowledge/methods. Can the author defend his paper against this point from the „devil's advocate"? How is the conclusion of the author in the abstract that „metaplasticity in both thresholds is necessary" reconcilable with his previous publication (Khodadadi et al. eLife 2025), in which only metaplasticity in one threshold was successful in solving the nonlinear feature binding problem?

Thank you for raising this question, since the answer was not clear in the first version. The study may be an incremental increase in methods, but is (in my view) a solid increase in knowledge, giving concrete new insights into metaplasticity (an area that is still comparatively little understood). The two main conclusions are:

(1) In synapses that are exposed to both the LTP and the LTD process, metaplasticity is necessary to ultimately express just one of them (converge to either LTP or LTD).

(2) Metaplasticity in the threshold regulating one plasticity process is necessary for expressing the opposite process (metaplasticity in the LTD threshold is necessary for expressing LTP, and vice versa).

The article has been substantially revised to clearly state these main conclusions (as well as the study’s goal), while a full list of all conclusions is given in points 1-7 the Discussion.

The conclusion in the abstract that „metaplasticity in both thresholds is necessary" is stated too generally, and it was meant to refer to this rule only. I have now removed it from the abstract, since the study’s goal was not to solve feature binding. Instead, the focus is on the two conclusions above as well as other conclusions obtained from expanding the study with reversal learning and using a single threshold (prompted by the comments from yourself and reviewer #1).

Lastly, the differences compared to Khodadadi et al. 2025 (eLife) are:

(1) Yes, the rule is simpler and has metaplasticity in both calcium thresholds, instead of just one in Khodadadi et al. 2025 that operates according to a different mechanism (where the threshold, along with the entire LTP plasticity kernel, moves in a direction opposite of the calcium signal).

(2) Plateau potentials are used here, versus the “boosting” nonlinearities in Khodadadi et al. 2025.

(3) The most detailed calcium diffusion model to date for SPNs is implemented in this study (by Dorman et al. (2018)). This was a necessary addition to avoid non-monotonous increases in calcium (shown in Fig. 13A, B). No calcium diffusion between neuronal compartments is implemented in Khodadadi et al., 2025. This is indeed a small methodological difference, but not trivial to implement.

The relation to Khodadadi et al., 2025 is now stated both in the introduction in lines 137-144, and at greater length in the discussion in lines 856-870.

Perhaps I should note that the two learning rules (this one and that in Khodadadi et al. 2025) developed in parallel, this one being based on formulations similar to Gütig et al. 2003 by adding metaplasticity, while the rule in Khodadadi et al. 2025 was inspired from the ideas in Schiess et al. (2016) and Urbanczik and Senn (2014) (see list of references provided). The two studies have different goals (and in that sense one was not meant to be an extension of the other):

- Khodadadi et al. (2025) studies whether the NFBP can be solved by SPNs,

- this article studies the role of metaplasticity in the two calcium thresholds that exist in dSPNs; it uses feature binding as a task because the role of metaplasticity is exposed precisely by the shared features in the task (they cause shared synapses to undergo competing LTP and LTD, and metaplasticity is necessary to direct synapses into just one outcome); importantly, feature binding is also relevant for the striatum (now described in the introduction in lines 126-136)

Finally, to obtain the conclusions in this study about the roles of the two thresholds, it was necessary to devise a suitable rule. They cannot be obtained neither with the rule in Khodadadi et al. 2025, nor with any other rule, because none have a formulation with two separate thresholds for LTP and LTD. Phrased more generally, one needs a new/different rule (new/different assumptions) to obtain new/different conclusions, even if the new rule may be related to existing ones. That said, a rule with a single threshold would have reached conclusion 1. above, as is now shown in the article in Fig. 12 and Figure 12 – figure supplements 1 – 4, but SPNs have two thresholds, prompting the use of a rule with two thresholds. Also, although not demonstrated with the cascade model (by Fusi et al. (2005) and its extensions), conclusion 1. should be obtainable with it, and is implied by the dynamics of the cascade model (which uses one threshold to control transitions between strong and weak synapses). More on the cascade model is given below and in the revised article.

Hopefully that provided a clearer answer. If you have more questions, please let me know so I can try to clarify further.

(2) As far as I can judge without testing the model, metaplasticity causes thresholds to monotonically increase during systematic pattern presentation, which stabilizes weights and allows pattern separation. Due to the closed-loop nature of the current implementation, where metaplasticity only happens if plasticity happens, this also effectively locks patterns in place. However, flexible learning is an essential mechanism for survival. Imagine a mutation event takes place and bananas suddenly become red and/or strawberries turn yellow. It seems that the current model would be unable to adapt to these new patterns even if rewards were to be shifted. While out of the scope of the study, due to its importance, I feel that pattern shifting/relearning should at least be briefly discussed. How could the model be improved to allow relearning?

This is a very important question, and I think it is in fact within the scope of the study, so it is now addressed using reversal learning as a task (the reward policy is switched in the middle of the simulation, after the FBP and NFBP are learned). As you pointed out, the closed-loop formulation of metaplasticity effectively locks the patterns in the dendrites, and reversal learning cannot be solved (Fig. 9). On the other hand, if the conditions for metaplasticity are relaxed by allowing any calcium levels to trigger metaplasticity (i.e. no longer have a closed-loop formulation requiring that [Ca]_NMDA or [Ca]_L-type be above their thresholds), reversal learning in both the FBP and NFBP is solved (Fig. 10 and Figure 10 – figure supplements 1 – 3). (Note that [Ca]_NMDA or [Ca]_L-type still need to be above their thresholds for plasticity to occur.)

Recommendations for the authors:

Reviewing Editor Comments:

While the reviewers were very positive, they highlighted limitations on the strength of evidence. Addressing these points could help revise this assessment.

Reviewer #1 (Recommendations for the authors):

(1) Framing the problem as "feature binding" is easy to understand, but it's a slightly narrow view of learning in general. Some mention of how NFBP relates to the XOR problem in the introduction would help you relate your solution to the much broader class of computational problems, since XOR is a more fundamental computational primitive. Non-linear feature learning is very general and relates to all machine learning problems and to computations that occur across every brain region.

Since the goal of the study was not to solve the NFBP or feature binding (but to study metaplasticity), the relation of the NFBP to the XOR is put in the Discussion instead (to avoid further confusion about the study’s goal). Nevertheless, this connection is clearly made in the introduction of the new study that uses 100+ SPN models.

(2) Since the requirement for clustered synapses is one of the main limitations of this learning rule, it would help if there were some discussion of how clustering might occur (e.g., whether there are any other related learning rules or mechanisms that might promote clustering, or if you are assuming that this has to occur entirely through developmental wiring).

This is now discussed in lines 817-827 and related to developing a learning rule that would incorporate structural plasticity.

(3) Page 5, row 157: Another potentially relevant citation here is Bittner et al. 2017, showing that a dendritic plateau potential in silent CA1 neurons drives place field formation without any prior spiking activity.

Thank you, that is indeed a very relevant citation here! It is now added in line 222.

(4) Figure 4C: It would be helpful to add a sentence in the figure legend explaining what the dashed lines represent (even though you also mention it in the main text).

Added, thank you!

(5) Across all figures, the author should consider using color combinations that are more colorblindfriendly (e.g., cyan/red). As a R/G colorblind person, I find it slightly difficult to see which line is which in the panels that compare scores in the NFBP.

The panels showing the NFBP scores have been changed throughout the article, and all other figures have been checked. If there are any more difficult color combinations, please let me know.

(6) The conventional, widely used abbreviation for dopamine is "DA", not "Da".

Now changed.

(7) A few typos I spotted in the paper:

(a) Row 117 (page 3): missing parenthesis around citation

(b) Row 173 (page 5): "uner" --> under

(c) Row 248 (page 7): repeated sentence "...are first seen above..."

(d) Row 255 (page 7): "NBFP" --> NFBP

These are now fixed, thank you for reporting them!

Reviewer #2 (Recommendations for the authors):

(1) How are synapses distributed in the nonlinear integration case? Are pattern combinations branch-specific, or are features distributed randomly across the whole dendritic tree? Does this matter in any way? In any case, it should be clarified.

Yes, they are branch-specific. In the NFBP, the feature combinations from Figure 3 – figure supplement 1 (and later from Figure 10 – figure supplement 1) are placed on two dendrites, chosen at random from 8 dendrites, in a 20-micrometre dendritic stretch starting around 120 micrometers away from the soma. 12 different trials are run for each feature combination, meaning that 12 randomly chosen pairs of dendrites were tested for each feature combination. In the FBP, the clusters are placed in one dendrite chosen at random from 8 dendrites, at the same distance from the soma as in the NFBP. This information is now added in the caption of Fig. 3.

The idea behind placing clusters on the same dendrite is that, after learning, two strong clusters will produce a plateau (e.g. ‘red’ and ‘strawberry’), while one strong and one weak cluster will not (e.g. ‘yellow’ and ‘strawberry’), as in Figs. 3C₂, 3C₃ (with the weights shown in Figs. 4B₂, 4B₃). For this the clusters need to be in the same branch, so that two features are “bound” together “into” a larger, plateau-evoking cluster. Also, a strong and a weak cluster should evoke a sufficiently lower somatic amplitude so that any additional noise will not cause somatic spiking. This is assured by the large voltage jump in the plateau (the all-or-none quality of the plateaus, Fig. 2D₁).

If the clusters are distributed randomly on different dendrites, it might or it might not work. Fig. 10 of Oikonomou et al. (2012) shows that dendritic spikes (that individually do not evoke somatic spiking) summate sublinearly at the soma in pyramidal neurons: weak + weak cluster = no spiking (Fig. 10A); strong + strong = no spiking (Fig. 10B); but also strong + strong = spiking (Fig. 10C). To reliably solve the NFBP, a large enough supralinearity is necessary instead, so one should test how the soma integrates dendritic spikes/plateaus in SPNs. As the goal of this study was not to solve the NFBP, this is left for the future (perhaps within the new ongoing study focusing on the NFBP).

(2) To produce dendritic plateau potentials, the model (as in the previously published model - Trpevski et al. 2023) implements glutamate spillover activating extrasynaptic NMDARs. This is an interesting mechanism, but is there empirical evidence supporting this way of generating plateau potentials? Are synaptic NMDARs not sufficient? If not, which experiments support the role of nonsynaptic ones?

This is still an ongoing area of research, indicating that glutamate spillover is regulated by reuptake from glial cells, which could even reverse function and excrete glutamate (Rusakov and Stewart, 2021; Malarkey and Parpura, 2014).

Except for the experiments from Szapiro and Barbour, 2007 showing that climbing fibers in the cerebellum signal to molecular-layer interneurons exclusively through glutamate spillover, there are no other “in-vivo-like” experimental conditions which show that spillover activates extrasynaptic NMDARs (eNMDARs). The strongest other in vitro data come from the following experiments:

(1) Chalifoux and Carter (2011), where glutamate reuptake by transporters was blocked with TBOA, which promoted NMDA spikes evoked by synaptic stimulation, suggesting that glutamate spillover activates eNMDARs. A similar experiment was done in Suzuki et al. (2008), where, in addition, synaptic NMDARs were blocked, leaving only eNMDARs available to trigger plateaus.

(2) Glutamate iontophoresis, which ejects glutamate directly into the extrasynaptic space, activates plateaus once the iontophoretic current is strong enough (Oikonomou et al., 2012), with or without blocking glutamate reuptake (Suzuki et al. 2008).

(3) Repetitive synaptic stimulation is thought to produce glutamate spillover (Suzuki et al. 2008; Oikonomou et al., 2012). For example, two synaptic shocks trigger NMDA spikes, while 5 synaptic shocks trigger plateaus in pyramidal neurons (Oikonomou et al., 2012).

On the other hand, studies that employ glutamate uncaging at spines, which should activate eNMDARs much less, evoke NMDA spikes instead (Losonczy and Magee, 2006; Branco et al. 2010). Compared to plateaus, these have much smaller amplitudes, and the size of the supralinearity (the voltage jump) is much smaller than in the plateaus obtained with glutamate iontophoresis (compare Fig. 3 in Losonczy and Magee, (2006), Fig. 3B in Branco et al. (2010) to Fig. 4C in Oikonomou et al. (2012), Fig. 6 in Oikonomou et al. (2014)).

The reason why glutamate spillover was implemented is precisely this robust all-or-none quality of the plateaus, i.e. the large jump in somatic voltage (Fig. 2D₁) after a threshold level of stimulation (when the stimulus intensity increases in equal amounts). Without spillover, plateaus are graded in amplitude (and duration, Fig. 2B₁ in Trpevski et al. (2023)), and the NFBP cannot be solved (Fig. 6 in Trpevski et al. (2023)).

(3) The check for dependence on initial conditions of theta_LTP/LTD is missing. Especially for the conditions of the thresholds being fixed. How do you decide what fixed value to use? How about having a corresponding limit for weights and not for thresholds? Why is there still an increase in threshold going on even when weights reach the maximum?

The initial conditions for θ_LTP and θ_LTD are also an important question. The idea behind starting with low values of the thresholds (or fixing them to low values) is to make the synapses flexible for learning. One can view metaplasticity’s role as a “lock” on the weights, locking them once learning is done, and unlocking them (making them flexible) when something needs to be learned. Which signals determine when to lock or unlock the weights is what the metaplasticity rule implements, and is insufficiently understood experimentally. In any case, it makes sense to start with flexible synapses (low thresholds) at the beginning of learning; otherwise, no/little learning will take place (Figure 9 – figure supplement 2, the panels for “thresholded” metaplasticity). Throughout the article I choose the initial values of the thresholds to be lower than the calcium evoked by weakened synapses, ensuring that any calcium signal will trigger plasticity (but higher values also work).

Instead of doing a scan over the initial conditions of θ_LTP and θ_LTD, I chose to show the following:

(1) An example with initial threshold values higher than the calcium amplitudes: these “lock” the weights (Figure 9 – figure supplement 2, panels for “thresholded” metaplasticity) from the start and no learning can occur.

(2) An example initialized with high values for the thresholds, but where metaplasticity can be triggered by any calcium amplitudes (no closed-loop in the metaplasticity rule, Figure 9 – figure supplement 2, panels for “relaxed” metaplasticity): here the thresholds adapt and learning can take place afterwards.

This is supposed to illustrate a mechanism that can “unlock” weights. A scan over the initial conditions of θ_LTP and θ_LTD will give the lowest calcium level that the thresholds can be initialized to so that “thresholded” metaplasticity will work. But it is not important to know these precise values to obtain the conclusions in the article, which is why I did not do such a scan. (The above is treated in the article in the section on reversal learning, lines 569-577 and 628-633.)

Also, when the rule is used for learning, it is not meant to have fixed thresholds, as synapses cannot stabilize and nothing will be stored (Figs. 5, 6, and 8). Fixing the thresholds to a low value was meant to show what happens without any metaplasticity (or if metaplasticity were “dysfunctional”). If in reality a mechanism exists to fix the thresholds to a low value or a high value, fixing would be temporary (until necessary to keep the weights flexible or locked, respectively). 

I am probably not understanding this part of the comment: “How about having a corresponding limit for weights and not for thresholds?” There are two limits, the maximal and minimal weights in the rule w_max and w_min, and are initialized to random values within the interval [0.3, 0.35], but this is probably not what you mean.

When the weights reach their maximum, the thresholds still increase because they have not reached the calcium amplitudes evoked by the maximal weights. (This is most visible with supralinear integration, where strengthened weights evoke plateaus Fig. 4C₂-C₄.) The thresholds move towards the calcium amplitudes with a rate η_θ, which if made very high (as in Figure 4 – figure supplement 11), will make the thresholds rise as fast as the weights. But this is not good, as it will “lock” the learning processes in the synapses too soon (i.e. shorten the window where they are flexible). Neither is a too low η_θ good, as then the synapses are flexible for a very long time and learning of the NFBP is prolonged (Figure 4 – figure supplements 10B₃, 10B₄, 10E₃, learning simulations last longer than in Fig. 4).

(4) Calcium modelling: The author writes that the largest voltage plateaus do not correspond to the largest calcium amplitude because of the plateau's voltage approaching the NMDAR reversal potentials, which might be a problem for the plasticity rule. To solve this, the author tried to implement a monotonic increase of calcium with increasing plateau by implementing axial calcium diffusion and buffering. My question is, is the monotonic increase realistic? Is not the NMDAR reversal effect, described above, a realistic scenario in dendrites?

It seems to be realistic. The closest experiment that I know of is in Fig. 2C₂, D₂ in Oikonomou et al. (2012), where 2 synaptic shocks produce an NMDA spike, and 5 shocks produce a plateau. The calcium dye shows a higher response from the plateau, suggesting a higher calcium amplitude (with a monotonic increase). Moreover, in the detailed calcium model for SPNs by Dorman et al. (2018), larger synaptic clusters produce monotonically higher calcium amplitudes. These two pieces of evidence suggest the calcium amplitudes are not affected by the membrane voltage approaching to the reversal potential. Most likely, this happens because of strong intracellular calcium buffering.

Similarly, the experiments in Figs. 5 and 8 in Losonczy and Magee (2006) with glutamate uncaging at spine heads show a monotonic increase in calcium dye flourescence as the cluster size is increased. However, these experiments evoke NMDA spikes, which might not have approached the NMDAR reversal potential as closely as plateaus do (so, it is theoretically possible that monotonicity does not hold if a plateau were evoked, although it seems unlikely). This is now added to the Methods in lines 957-961.

(5) Function: What is the actual function of the SPN, and how does it relate to FBP/NFBP learning? SPNs are involved in motor control/decision making and generally in sensorimotor tasks. Rather, use an example for that than a visual stimulus, though I understand it is more easily illustrated. Is feature binding what SPNs do and have to solve?

It is not known yet what SPNs do precisely. The initial action selection role of the basal ganglia is currently being challenged or replaced by a role in movement initiation and/or invigoration (with action selection being done by the cortex, see e.g. Thura and Cisek (2017)). In any case, SPNs receive convergent input from sensory, motor, limbic and associative areas, as well as thalamic and neuromodulatory inputs (with topographical projections indicating functional specialization). In that sense, feature binding is particularly relevant for the striatum, as diverse features from different areas would arrive there. The basal ganglia participate in non-motor loops as well, so the striatum may have a role in initiation and termination of cognitive processes such as planning and attention, and in regulating emotional and motivated behavior (Purves et al. 2018).

The role of the striatum and the relevance of feature binding is now stated in the introduction in lines 126-136, and a task with features more suited for the striatum is given in Figure 1 – figure supplement 1 (inspired from similar tasks in Bernklau et al. (2024)). I have kept the example from the visual system in the main text simply because it is widely used throughout the literature and easily recognizable, while clearly stating that other features would be involved in the striatum and pointing to the example in Figure 1 – figure supplement 1. Hopefully this will make a good compromise between ease of reading and relevance to the striatum.

(6) The population of striatal projection neurons can express dopamine D2 receptors and not only D1 receptors. SPNs with different receptors thus undergo synaptic plasticity according to different rules. Would that lead to similar results? A combination of both populations?

This is also being tested in the new study, and preliminary results indicate the answer is “yes” (see Author response image 4). Contrary to the dSPNs, the indirect-pathway SPNs (iSPNs), which predominantly express D₂ receptors, are thought to be involved in suppressing competing or related movements. The learning rule is almost the opposite to dSPNs: to trigger LTP, a dopamine pause is needed, and to trigger LTD a dopamine peak is needed (Fig. 4B and Shen et al. (2008)). So, with such a rule, iSPNs will store the irrelevant patterns and spike to them, and be silent to the relevant patterns (which indeed happens after learning in Author response image 4F₂, F₃). This aligns well with their role to suppress movements – reaching for the irrelevant patterns will be suppressed, while reaching for the relevant patterns will be disinhibited (the indirect pathway inhibits movement initiation). 

(7) Other synaptic plasticity & metaplasticity models (possible comparison or discussion): https://pubmed.ncbi.nlm.nih./ https://linkinghub.elsevier.(https://link.springer.com/ For example, in the last model, there is only one modification LTP/LTD threshold, but it is different from the voltage threshold (which would be comparable to calcium thresholds in the current paper - see the voltage threshold different from the modification threshold here: https://doi.org/10.1371/). The modification threshold favors LTP or LTD - depending on the previous spiking activity of the cell and effectively works as an anti-Hebbian firing rate „homeostasis" mechanism. How is the firing rate homeostasis maintained in the current paper/model? Can you explain how this model is related to the previous models of Benuskova and Abraham, and also Clopath (there was also a metaplasticity version of the Clopath model), in terms of firing rate stability? The current model implements not only local synaptic plasticity but also metaplasticity, which is a nice feature, and seems to not only solve the FBP but also maintain firing stability. Is the stability of firing a consequence of the hard bounds for synaptic weights, or is it also a consequence of plasticity and metaplasticity? I like that each synaptic weight is changed independently based on local calcium concentration, with its own LTP and LTD thresholds.

I will first describe what happens to the firing rate in this model, and then compare with the references you mentioned. In the FBP with linear integration, yes, the firing rate stability is only maintained because of the hard bounds for synaptic weights (Figure 4 – figure supplement 5A₁, the neuron goes into depolarization block without w_max). Without w_max, the weights would grow until [Ca]_NMDA saturates in the spine (which does not happen for most spines within the simulation time in Figure 4 – figure supplement 5B₁).

In the FBP with supralinear integration and the NFBP, the weights are prevented from increasing by the upper threshold for LTP, θ_LTP. If θ_LTP and w_max are gone, synapses also grow without bound (Figure 4 – figure supplement 5B₂). Regardless of how high the synaptic weight becomes, firing rate stability is ensured by the plateau potential, as the maximally achievable voltage is limited by the NMDAR reversal potential (Figure 4 – figure supplement 5A₂, a somatic depolarization block does not happen as in Figure 4 – figure supplement 5A₁). This is part of the plateaus’ function to provide dynamic range compression, as shown experimentally in Figs. 3E, 4D and 12 in Oikonomou et al. (2012). (Of course, such high weights are unrealistic, but they happen in the model without w_max and without θ_LTP). This is now described in the text in lines 397-407.

Regarding the other studies, the second link did not work, so I will refer to Jedlicka et al. (2015), Clopath et al. (2010) and Zenke et al. (2013). (The rule in Jedlicka et al. (2015) is the same as in Benuskova and Abraham, (2007) but with a more detailed neuron model.) In these studies, there is a threshold representing a (weighted) average of the postsynaptic activity (postsynaptic voltage or spiking). In Clopath et al. (2010) and Zenke et al. (2013) it modulates only the amount of LTD, while in Jedlicka et al. (2015) it modulates the amounts of both LTP and LTD that occur due to plasticity. The threshold is global for a neuron (i.e. all synapses use the same threshold), and allows for heterosynaptic effects that compensate increased excitation from synaptic strengthening with stronger weakening in depressed synapses (thus maintaining stable firing rates). (However, the rule in Jedlicka et al. (2015) and Benuskova and Abraham, (2007) has only one threshold, there is no separate voltage threshold. Indeed, the threshold is a low-pass filtered variable of the input spike train, so is similar to calcium concentration.)

There are no such effects in the current learning rule. Some compensatory effects are visible when comparing supralinear integration with and without an upper threshold θ_LTP, as e.g. in Fig. 4B₂ and Figure 4—figure supplement 3B₁. With θ_LTP, synapses do not increase to w_max, and without it, they do. As a consequence, the weakened synaptic cluster is weakened less when using θ_LTP (‘yellow’ synapses in Fig. 4B₂), and more without θ_LTP (‘yellow’ synapses in Figure 4—figure supplement 2B₁). The increased weakening in the latter case is because the strengthened ‘strawberry’ synapses have reached w_max, and contribute to spiking for the irrelevant pattern (‘yellow strawberry’). As a result, the weakened ‘yellow’ synapses have to decrease more so no spiking for the irrelevant pattern occurs. In effect, the increased strengthening in the ‘strawberry’ synapses drives increased weakening in the ‘yellow’ synapses. However, this is a result of the task structure, i. e. that the patterns share features, and not from the learning rule.

The above is briefly explained in the Discussion in lines 778-786.

(8) The last sentence in the discussion is a bold claim: SPN can completely solve NFBP alone. Is that statement too strong, or is it a sign of multiple different mechanisms implementing the same function (i.e., degeneracy)?

The sentence was not meant to be a bold claim. It currently says:

“This indicates that ... SPNs might completely solve the task ... Whether this is true will be explored in another study …”

I have now toned this claim down, as the purpose was only to point to the new study that explores this question (using with 100+ SPN models, in two learning regimes and varying cluster location). Nevertheless, the preliminary results in the new study suggest that SPNs can indeed solve the NFBP (if the plateaus are all-or-none), so I agree that it is a sign of multiple mechanisms implementing the same function.

Figures/Table:

(1) Figure 2: The layout of the figure is confusing. B shows distributed input as in upper A, and C shows clustered input as in lower A. This should be illustrated better (e.g., as in Figure 3 or 4). The term cluster size is confusing as well because it also refers to the distributed inputs; better use the number of synapses here. The color choice is difficult, as similar colors are chosen for cluster size and for differentiating linear and nonlinear integration in D.

Thank you for the detailed comments! The figure has been reworked accordingly.

(2) Figure 4: C What are dashed lines?

They indicate the upper threshold for LTP, θ_LTP.Thank you for noticing this, it is now added in the figure caption, and in other figures where it was missing.

(3) Figure 5 and Figure 6: B is missing.

These figures have been reworked to match the revision of the text describing the role of metaplasticity in the shared synapses. Now, the FBP is described first, followed by the NFBP, so the figures have been merged with their figure supplements (where the FBP results used to be in the first version).

(4) Figure 4 Supplement 1: What do the colors and regions mean in B3? Why show here and not for others?

The main text in lines 311-312, 331-333, and 358-359 refers to these regions when explaining the dynamics of the calcium, the thresholds and the weights (e.g. the pink region shows that [Ca]_L-type in the ‘strawberry’ synapses evoked by ‘yellow strawberry’ is much lower than the calcium threshold for ‘strawberry’, protecting these synapses from weakening). They are simply highlighted with different colors, so readers know precisely where to look when reading the main text. The figure caption has been updated to state this.

Also, the figure caption says that the same regions exist in all panels, although they have not been highlighted. I could have chosen any panel to mark these regions, and I chose B₃ because it looked like it had the least visual clutter.

(5) Table 1: Typo for LTD

Now fixed.

(6) Line 21: „thehsold"

Now fixed.

(7) Line 50: Closing parentheses missing.

Now fixed.

(5) Line 55: "All metaplasticity models so far have only one modifiable threshold". This is not true as it stands. Multiple sliding thresholds have been proposed before:

- experimentally by Ngezahayo et al. (2000)

- multiple pathways reviewed by Abraham (2008)

- multiple structural LTP thresholds observed experimentally by Ueda et al. (2022)

- models of synaptic states and cascade models can be considered to employ multiple thresholds (depending on state); e.g., Fusi et al. (2005)

Thank you for providing these references! The sentence has been changed (it was supposed to refer only to computational models), and the studies have been added in the text where appropriate.

Importantly, Fusi et al. (2005) is now being discussed throughout the text, as it contains important results and conclusions about metaplasticity which are used as comparison. (In the first version of the article I did not include it because I was not sure about the interpretation of the thresholds – strictly speaking there is only one plasticity threshold (q, determining whether a synapse will switch sign), while the other is a metaplasticity threshold (p, determining whether the synapse will change its metaplastic state). However, the precise number of thresholds is not as important, as the study’s results are relevant to compare with.)

(9) Lines 117/118: Missing parentheses around reference.

Fixed.

(10) Line 140: "a small difference". I feel like "small" is a bit of an understatement here, as from what I can see, the differences are almost a magnitude -- see blue/black traces in Figure 2B4 vs. 2C4.

Thank you for noticing this. It was meant to refer only to the amplitude of the somatic voltage when the cluster size is small (in Fig 2D₁). The text has been clarified now.

(11) I think it's unnecessary to rewrite Eq. 1 in Eq. 3.

I decided to keep this.

(12) Lines 181-183: It would probably still be useful to show that NFBP can't be solved by distributed inputs.

It is now shown in Figure 4 – figure supplement 1, and briefly described in the text in lines 298300.

(13) Line 210: Typo, double "(the"

Fixed, thank you.

(14) Lines 248-249: Typo, double partial sentence.

Now fixed.

(15) Line 760: The year in the „STDP rule endowed with the BCM sliding threshold accounts for hippocampal heterosynaptic plasticity" should be corrected to 2007. Also, all other references should be checked for mistakes and missing pages, etc. (see e.g., also line 882).

Thank you for noticing this! The references have been checked.

References

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Author response image 1.

Plateau potentials (A1, B1) and their somatic amplitudes in dSPNs (A) and iSPNs (B) when the location of the synaptic cluster is varied. Distally evoked plateaus have a smaller somatic amplitude in both dSPNs and iSPNs, bust still exhibit a nonlinear jump in the somatic voltage. In (A2, B2) all 71 dSPN and 34 iSPN models were tested, color coded with respect to their excitability to a synaptic cluster of 10 synapses.

Author response image 2.

Two learning simulations on the NFBP where different metaplasticity rates for LTP and LTD were used. (Top) The metaplasticity rate for LTD is higher, stopping the LTD process prematurely (D1, D2), resulting in less weakening of the synapses (B1, B2) and spiking for one irrelevant pattern (A1). (Bottom) The metaplasticity rate for LTP is higher, preventing frequent synaptic strengthening(C1, C2). As a result, it takes a longer time for synapses to strengthen and trigger plateaus (B3, B4).

Author response image 3.

Learning on the NFBP with a nonlinear (quadratic) metaplasticity rule, which implements the BCM rule. (A) Somatic and dendritic voltage before and after learning. (B-D) Evolution of synaptic weights (B), LTP (C) nad LTD thresholds (D). Weights in (B) seem to stabilize around a high value once the LTP threshold reaches the maximal [Ca]NMDA; however, the value is too high and triggers plateau potentials for all patterns.

Author response image 4.

Learning to solve the NFBP in one dSPN and one iSPN model. (A, B) Schemes describing the requirements for cortico-striatal synaptic plasticity in dSPNs (A) and iSPNs (B). (C) Dopamine peaks are emitted from the midbrain after the relevant patterns, and dopamine pauses after the irrelevant patterns. (D) Stimulation protocol. (E, F) A single learning simulation in a dSPN (E) and an iSPN (F) model. Before learning the neurons spike to all patterns (due to additional feature-unspecific distributed inputs, shown with the third panels in E3, F3). After learning, the dSPN spikes only for the relevant patterns (E2) and the iSPN only for the irrelevant ones (F2). (E3, F3) The evolution of clustered and distributed synptic weights (In dendrite 1 of the iSPN, the synapses for 'red' experienced some strengtheneing after being weakened, but this does not seem to affect learning in this example.) The neurons in th enew study receive less background synaptic input than in the current article, and additional distributed synapses are needed along with a plateau for somatic spiking, making for a more challenging learning scenario.

eLife Assessment

This valuable study provides a practical computational framework for inferring latent neural states directly from calcium fluorescence recordings, bypassing the traditional need for a separate spike deconvolution step. The evidence supporting the method is convincing, featuring rigorous validation across multiple latent variable model families (including HMM, GPFA, and LFADS) using both simulated and experimental data. To further strengthen method's generality, it would require further application to a broader range of experimental datasets, such as recordings from different brain regions or using different calcium indicators.

Reviewer #1 (Public review):

Summary:

In this study, the authors elegantly combined latent variable models (i.e., HMM, GPFA and dynamical system models) with a calcium imaging observation model (i.e., latent Poisson spiking and autoregressive calcium dynamics (AR)).

Strengths:

Integrating a calcium observation model into existing latent variable models improves significantly the inference of latent neural states compared to existing approaches such as spike deconvolution or Gaussian assumptions.

The authors also provide an open-source access to their method for direct application to calcium imaging data analysis.

Weaknesses:

As acknowledged by the authors, their method is dependent on the quality of calcium traces extraction from fluorescence videos. It should be noted that this limitation applies to alternative strategies.

While the contribution of this study should prove useful for researchers using calcium imaging, the novelty is limited, as it consists of an integration of the calcium imaging model from Ganmor et al. 2016 with existing LVM frameworks.

Comments on revised version.

The authors addressed my comments and I have no further concerns.

Reviewer #2 (Public review):

Summary:

This compelling study proposes a framework to implement latent variable models using population level calcium imaging data. The study incorporates autoregressive dynamics and latent Poisson spiking to improve inference of latent states across different model classes including HMMs, Gaussian Process Factor Analysis and nonlinear dynamical systems models. This approach allows for a more seamless integration of existing methods typically used with spiking data to apply on calcium imaging data. The authors test the model on piriform cortex recordings as well as a biophysical simulator to validate their methods. This approach promises to have wide usability for neuroscientists using large population level calcium imaging.

Strengths:

The strength of this study is the flexibility in the choice of models and relatively easy adaptation to user-specific use cases.

Weaknesses:

The weakness of the study lies in its limited validation of biological calcium imaging data. Calcium dynamics in a task-specific context in a sensory brain region might be very different from slower dynamics in a region of integration.

Reviewer #3 (Public review):

Summary:

S. Keeley & collaborators propose a computational approach to infer time-varying latent variables directly from calcium traces (e.g., obtained with 2p imaging) without the need for deconvolving the traces into spike trains in a preliminary, independent step. Their approach rests on 1 of 3 families of latent models: GPFA, HMM and dynamical systems - which they augment with an observation model that maps latent variables to fluorescence traces. They validate their approach on simulated data as well as a single real dataset, showing that the approach improves latent variable inference and model fitting, compared to more traditional approaches (although not directly compared with the 2-step one; see below). They provide a GitHub repository with code to fit their models (which I have not tested).

Strengths:

The approach is sound and well-motivated. The authors are specialists of latent variable models. The manuscript is succinct, well-written and the figures are clear. I particularly liked the diversity of latent models considered, in particular latent models with continuous (GPFA) vs. discrete (HMM) dynamics, which are useful for characterizing different types of neural computations. The validation on both simulated and real data is convincing.

Weaknesses:

The main weakness point that I see is that the approach is tested only on a single real dataset (odor response dataset). The other model fits are obtained from simulated data. While the results are convincing, it would be useful to see the approach tested on other datasets, for instance datasets with different brain areas, different behavioral conditions, or different calcium indicators. This would help assess the generality of the approach and its robustness to different experimental conditions.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

In this study, the authors elegantly combined latent variable models (i.e., HMM, GPFA and dynamical system models) with a calcium imaging observation model (i.e., latent Poisson spiking and autoregressive calcium dynamics (AR)).

Strengths:

Integrating a calcium observation model into existing latent variable models improves significantly the inference of latent neural states compared to existing approaches such as spike deconvolution or Gaussian assumptions.

The authors also provide an open-source access to their method for direct application to calcium imaging data analysis.

Weaknesses:

As acknowledged by the authors, their method is dependent on the quality of calcium trace extraction from fluorescence videos. It should be noted that this limitation applies to alternative strategies.

While the contribution of this study should prove useful for researchers using calcium imaging, the novelty is limited, as it consists of an integration of the calcium imaging model from Ganmor et al. 2016 with existing LVM frameworks.

Reviewer #2 (Public review):

Summary:

This compelling study proposes a framework to implement latent variable models using population level calcium imaging data. The study incorporates autoregressive dynamics and latent Poisson spiking to improve inference of latent states across different model classes including HMMs, Gaussian Process Factor Analysis and nonlinear dynamical systems models. This approach allows for a more seamless integration of existing methods typically used with spiking data to apply on calcium imaging data. The authors test the model on piriform cortex recordings as well as a biophysical simulator to validate their methods. This approach promises to have wide usability for neuroscientists using large population level calcium imaging.

Strengths:

The strengths of this study are the flexibility in the choice of models and relatively easy adaptation to user-specific use cases.

Weaknesses:

The weakness of the study lies in its limited validation of biological calcium imaging data. Calcium dynamics in a task-specific context in a sensory brain region might be very different from slower dynamics in a region of integration. The biophysical properties of the data would also be dependent on the SNR of the imaging platform and the generation of calcium indicator being used.

Reviewers 1 and 2 correctly point out that our method depends on the quality of the upstream calcium trace extraction. As they noted, these traces can vary based on the specific indicator used, the signal-to-noise ratio (SNR) of the recording, and the region of the brain being imaged (such as sensory vs. integrative areas). As Reviewer 1 rightly mentions, this is a universal challenge that applies to alternative strategies as well, rather than a limitation unique to our framework. To address these points, we have added a paragraph to our Discussion section.

Reviewer #3 (Public review):

Summary:

S. Keeley & collaborators propose a computational approach to infer time-varying latent variables directly from calcium traces (for instance, obtained with 2p imaging) without the need for deconvolving the traces into spike trains in a preliminary, independent step. Their approach rests on 1 of 3 families of latent models: GPFA, HMM and dynamical systems - which they augment with an observation model that maps latent variables to fluorescence traces. They validate their approach on simulated and real data, showing that the approach improves latent variable inference and model fitting, compared to more traditional approaches (although not directly compared with the 2-step one; see below). They provide a GitHub repository with code to fit their models (which I have not tested).

Strengths:

The approach is sound and well-motivated. The authors are specialists in latent variable models. The manuscript is succinct, well-written, and the figures are clear. I particularly liked the diversity of latent models considered, in particular latent models with continuous (GPFA) vs.

discrete (HMM) dynamics, which are useful for characterizing different types of neural computations. The validation on both simulated and real data is convincing.

Weaknesses:

One advantage … is that one can inspect the quality of the deconvolution step independently from the latent variable inference step. For instance, if the inferred latent variables are not interpretable, how can one determine whether this is due to a poor choice of latent model (e.g., HMM with too few states), or a poor fit of the observation model (e.g., wrong parameters for the calcium dynamics)?

We agree with the reviewer that integrating the calcium likelihood introduces additional parameters that require careful diagnostics. However, for the vast majority of imaging datasets, there is no simultaneous electrophysiology to verify the deconvolution step. If the final latent states are not interpretable, it remains impossible to determine whether the error originated in the initial spike inference from deconvolution or the subsequent model fitting.

Our framework addresses this by maintaining the raw fluorescence as the fixed observation. We suggest for those using this model to employ cross-validation using this data to select model parameters. We outline how to do this below, but because the data itself does not change with each model fit, you can compare P(data | λ) across any model configuration. In contrast, different deconvolution methods change the data itself (the spiketimes) making comparison across models impossible.

Could the authors comment on whether their approach allows for instance to compare different forms of latent models (e.g., HMM vs. GPFA) in terms of model evidence, cross-validated log-likelihood or other model comparison metrics?

We thank the reviewer for highlighting this. In short: yes. Because our framework integrates the calcium observation likelihood with various latent variable models, we can assess held-out prediction P(data | λ) irrespective of the specific latent structure.

However, because fitting the LVM requires inferring the latent state z to determine the firing rate λ, proper cross-validation across models involves holding out both neurons and timepoints. A principled approach—which our framework supports—is as follows:

(1) Train both the latent states z and the model parameters (e.g., the mapping from latent space to observations) on a training portion of the recording.

(2) On a held-out test segment, withhold a subset of "test" neurons and infer the latent states using only the "held-in" neurons.

(3) Calculate the likelihood of the observed fluorescence for the test neurons given the inferred rates.

We clarify this procedure in the revised manuscript. While a comprehensive benchmarking across all possible LVM architectures is beyond the scope of this study, we provide the statistical infrastructure for users to perform such comparisons. Furthermore, we would like to emphasize that while predictive likelihood is a rigorous metric for model selection, the primary utility of these LVMs often lies in the interpretability of the latent states themselves, which can remain biologically informative even if cross-validated performance is not the sole optimization target.

While it certainly makes sense that models accounting for the full transformation of latent => spikes => fluorescence data should outperform the two-step (1) deconvolution => (2) latent variance inference approach, the amount of improvement is not clear. A direct comparison … would be useful

We thank the reviewer for this point. Figure 4 was designed to address this comparison directly. By using a biophysical simulator, we generated a pseudo-realistic spiking network with ground-truth latent trajectories governed by a Gaussian Process. This allowed us to explicitly compare our unified approach against the traditional deconvolution-then-Poisson-GPFA pipeline. While a first-order (AR1) calcium likelihood did not show improvement over the two-step deconvolution method in recovering the ground-truth latents, the second-order (AR2) process demonstrated an improvement. Because there are no ground-truth parameters in the model, we use the reconstruction error of the latent values as our primary metric for recovery. These results suggest that when the observation model sufficiently captures the underlying calcium kinetics, the unified approach offers a more accurate estimation of the neural state.

It would be useful to discuss the possible extension of the approach to other types of data that … have different observation models.

We thank the reviewer for this helpful comment. We agree that the general framing of the likelihood has potential use in a wider range of data modalities.

Specifically, all sensors (aside from some voltage sensors) have a rise and decay time in line with our model. Thus the autoregressive (AR) nature of the calcium likelihood we utilize makes the current implementation particularly well-suited for a broad range of fluorescence-based sensors with similar temporal profiles. The specific use and extension would depend heavily on the biological target of the sensor. For example Glutamate, dopamine, and similar indicators can be thought of as having a similar underlying Poisson firing model, as the release of these products is tied to neural firing. Other sensors that might relate to other biological processes, such as hemodynamics (via imaging or ultrasound) or broader neuromodulation (Norepinephrine imaging with nLight) might be more continually varying and therefore would require changing the Poisson with an appropriate alternative, for example a Gaussian Process or similar.

Voltage imaging is the one exception that may require more complex observation models. However, the challenge in voltage imaging is not the ability to identify individual spikes, but more that the speed and scope of imaging is inherently limited by the speed of the voltage process and signal-to-noise ratios induced by the low quantum efficiency and membrane-bound nature of these indicators. If imaged well, single spikes would be clearly visible and the two-stage likelihood would not be necessary—one could simply use the spike times in a Poisson model just as with electrophysiology. We have added a paragraph in the discussion highlighting these points.

eLife Assessment

This important study identifies underappreciated experimental factors that influence α-synuclein amyloid polymorphism, with practical implications for the reproducibility of in vitro fibril preparations. Extensive cryo-EM analyses provide convincing evidence that protein purity, monomer preparation, and agitation conditions influence polymorph selection, including substantial effects from small amounts of an N-terminally truncated variant. The study provides a substantial resource for researchers studying amyloid assembly and synucleinopathies, although the proposed nucleation mechanisms need stronger kinetic support and reliable protocols for producing specific polymorphs require further development.

Reviewer #1 (Public review):

In this work, Frey and colleagues have carried out a very large study of α-synuclein polymorphism as a function of aggregation conditions and sample preparation. They provide valuable insight into the many critical factors affecting α-synuclein polymorphism, thereby illuminating the need for detailed reporting in the literature as well as both rigorous and detail-oriented protocols when working with this protein. Indeed, their observations are in line with the difficulties of reproducing structural outcomes across different laboratories and experiments. The authors must be complemented on their openness about the difficulties experienced and the thoroughness of their work. Efforts like these are going to be crucial to achieve an understanding of the unparalleled structural plasticity of α-synuclein amyloid fibrils. It is particularly notable that the authors have managed to optimize protocols to form single-polymorph aggregation reactions with high reproducibility.

In this work, the authors focus on the influence of α-synuclein purity in aggregation reactions. They find that using reverse-phase HPLC to purify the protein significantly alters the aggregation behaviour. It is interesting, and rather uncommon in the field, to use reverse-phase HPLC as a final purification step, rather than SEC, which is commonly used in many laboratories. It would be useful to compare this new protocol even more directly and extensively with the commonly used SEC protocol. When mentioning their previously published work, it should be mentioned explicitly how the protein was purified in these previous studies.

On the point of protein purification, the authors lyophilize their protein prior to storage. In their work, they also find that pre-aggregation oligomer formation alters the aggregation pathway of α-synuclein. While they demonstrate that this can be solved by appropriate filtration, it should be discussed why the lyphilizaiton step was not reconsidered/omitted given that this process is known to facilitate oligomer formation. Do the authors have experience with aggregation studies using α-synuclein that has not undergone lyophilisation and are able to comment on the influence of this step in the protocol?

The authors make note of several degradation products affecting their aggregation reactions, which is why they employ a much more thorough purification protocol. However, they also point out that some of the degradation products found at the end of their reaction could form during the reaction itself. Unfortunately, they never investigate this further. In particular, it would be very useful to know if different aggregation conditions (pH, salt, agitation) lead to different and characteristic degradation patterns. HPLS/mass spec of the supernatant at the end of each aggregation reaction would have been a very insightful thing to do.

With respect to degradation products, in this work a NΔ4-variant is produced to mimic a disease-relevant degradation product and indeed it is found to alter the structural outcome even at low relative concentrations (5%). Have the authors investigated the minimal fraction of the NΔ4 variant necessary to still influence the structural outcome of the predominant WT protein? This type of analysis could have significant relevance to disease-related analysis, where several variants (truncations and PTM variants) are present in trace amounts.

While on this topic, the authors note that in several of their type 5 fibrils, they find unresolved peptide fragments in their cryo-EM structures. Can the authors speculate if these fragments are indeed peptide degradation products or residues wrapping around the fibril originating from the fibril-incorporated protein?

In this work, the authors have performed an extensive study of α-synuclein polymorphism. However, despite generating what is likely the largest single data set of fibril structures, they perform very little quantitative analysis of their data. It would be interesting to analyse the relative abundance of fibril polymorphs produced in each reaction. Perhaps from the particle-picking data it could be estimated the relative abundance of each polymorph as well as non-resolved fibrils to generate a more nuanced view of polymorphism beyond overall classifications of the resolved structures. Indeed, from such data it could also be studied if certain protofilaments are more prone to pair in asymmetric fibril structures over others or if fibril asymmetry can be attributed to random pairing of protofilaments in accord with their abundance. This latter point is particularly interesting for the type 1 fibrils. Perhaps, the propensity of α-synuclein to form specific symmetries could also be estimated.

The authors note that pH is a strong factor in determining polymorph selection. This does indeed appear to be the case, but other parameters do not appear to show any clear trend. Have the authors investigated the influence of aggregation parameters (agitation, duration) on structural outcomes systematically or quantitatively, such as with principal component analysis? Indeed, they also find that some fibril types that otherwise are not compatible at the same pH appear to co-exist when the shaking parameter is modified. Are the authors then confident in the claim that pH is a deterministic parameter?

It is evident from this and other work that amyloid aggregation is highly sensitive to kinetic effects. It is therefore curious that the effect of protein concentration and reaction time has not been systematically investigated. The authors have some data studying dilution series (Figure 6A) and different reaction times (reaction 56 & 57). Could the authors comment on the effects of these two parameters, and might there be more information touching upon this that could be highlighted in this work?

The authors state that this work likely underreports fibril polymorphisms in samples due to population size or data quality challenges. Could the authors, based on their extensive experience, try to quantify this statement?

Additionally, the authors point out that the current framework for classifying α-synuclein fibril polymorphism is not sufficient to describe the real complexity of this protein system. However, they do not seem to address some of the recent literature aiming to solve such issues (see Scheres 2026, Connor et al. 2025, Milchberg et al. 2025 & Price et al. 2025).

Was any biophysical/biochemical analysis performed of the many structures produced here, such as CD spectroscopy, Proteinase K digestion, dye binding or FTIR, which could act as low-resolution structure identifiers and might help to retrospectively explain some findings in the older literature? Such data would be very useful for the vast majority of researchers, who do not have access to cryo-EM.

Reviewer #2 (Public review):

Summary:

This manuscript describes insights gained during efforts to reproduce disease-relevant alpha-Synuclein (aSyn) fibrils using recombinant protein in vitro. It follows up on a similar article from this team published in 2024. Although the authors have not been able to produce fibrils with the structure of ex vivo fibrils isolated from patients, they share insights gained into which factors influence the formation of specific fibril polymorphs.

Strengths:

This is quite an unusual manuscript because it goes into minute detail about sample preparation that are usual just mentioned in the Materials and Methods sections of other manuscripts (if at all). This makes it very valuable for the scientific community working on exactly the problem of reproducing disease-relevant aSyn fibrils in vitro (which will be a major breakthrough in the field). The authors present an impressive array of cryo-EM fibril structures, some of which have not been described before.

Weaknesses:

A major concern with the manuscript is that its story and messaging are a bit murky. The authors describe a few new polymorphs, show that some polymorphs (type 1) have small variations, show that sample purity and fragmentation will influence polymorph formation, and present a helical-symmetry mystery. This all reads like a loose collection of findings without any major takeaway. Looking at Table 1, it still seems that the authors do not have a good control over any of these polymorphs. Are they able to make any of these polymorphs reliably? I think the impact of this work could be strengthened if it ended with a reliable protocol for the production of any of the polymorphs described.

A second major concern is the quality of the aggregation kinetics and their interpretation. Are these kinetics just done once per concentration? The figure caption talks about 'three independent samples' but it is unclear if this refers to the three different concentrations or NΔ4 percentages used, or true repetitions. Looking at the curves themselves, it seems that only one of the conditions was actually done in triplicate, which should be the minimum to draw conclusions. Further, it would have been helpful to characterize the kinetic data quantitatively. Finally, because there are only kinetic data for a fraction of the conditions tested, it is not clear what they add to the overall manuscript. My recommendation is to either remove the kinetics from the manuscript or substantially expand this section.

Author response:

Reviewer #1 (Public review):

In this work, Frey and colleagues have carried out a very large study of α-synuclein polymorphism as a function of aggregation conditions and sample preparation. They provide valuable insight into the many critical factors affecting α-synuclein polymorphism, thereby illuminating the need for detailed reporting in the literature as well as both rigorous and detail-oriented protocols when working with this protein. Indeed, their observations are in line with the difficulties of reproducing structural outcomes across different laboratories and experiments. The authors must be complemented on their openness about the difficulties experienced and the thoroughness of their work. Efforts like these are going to be crucial to achieve an understanding of the unparalleled structural plasticity of α-synuclein amyloid fibrils. It is particularly notable that the authors have managed to optimize protocols to form single-polymorph aggregation reactions with high reproducibility.

In this work, the authors focus on the influence of α-synuclein purity in aggregation reactions. They find that using reverse-phase HPLC to purify the protein significantly alters the aggregation behaviour. It is interesting, and rather uncommon in the field, to use reverse-phase HPLC as a final purification step, rather than SEC, which is commonly used in many laboratories. It would be useful to compare this new protocol even more directly and extensively with the commonly used SEC protocol. When mentioning their previously published work, it should be mentioned explicitly how the protein was purified in these previous studies.

On the point of protein purification, the authors lyophilize their protein prior to storage. In their work, they also find that pre-aggregation oligomer formation alters the aggregation pathway of α-synuclein. While they demonstrate that this can be solved by appropriate filtration, it should be discussed why the lyphilizaiton step was not reconsidered/omitted given that this process is known to facilitate oligomer formation. Do the authors have experience with aggregation studies using α-synuclein that has not undergone lyophilisation and are able to comment on the influence of this step in the protocol?

We will include details in our revised version on how samples were prepared in our previously published work. However we do not plan to do a comparison between SEC and HPLC as final purification steps because these are truly orthogonal separation methods. SEC is the gold standard for oligomer removal but not particularly useful for removing degradation products of similar size (which we believe to affect aggregation outcomes). In our hands, the highest purity and reproducibility come from HPLC-purified material followed by a stringent oligomer removal. Because oligomers in the solubilized sample are a concern, SEC as a final post-solubilization/pre-aggregation step might be ideal. However, as we mentioned in the manuscript, SEC dilutes the sample to the point that much of the sample is too dilute for our purposes (aggregation without seeds) and adding an additional concentration step would risk promoting the formation of new oligomers in the concentration device. That is why we resorted to using a 100 kD MWCO filter to remove oligomeric species.

We considered skipping the lyophilization step and dialyzing the HPLC-purified sample into the buffer of choice but stuck with lyophilization because it provides an easy control over the protein concentration in the solubilized sample.

To clarify the logic in this choice of sample preparation steps, we will add a section to the revised manuscript listing/explaining our suggested protocols for preparing alpha-synuclein samples for reproducible aggregation experiments.

The authors make note of several degradation products affecting their aggregation reactions, which is why they employ a much more thorough purification protocol. However, they also point out that some of the degradation products found at the end of their reaction could form during the reaction itself. Unfortunately, they never investigate this further. In particular, it would be very useful to know if different aggregation conditions (pH, salt, agitation) lead to different and characteristic degradation patterns. HPLS/mass spec of the supernatant at the end of each aggregation reaction would have been a very insightful thing to do.

In retrospect, we agree that this could have been important from the standpoint of understanding how in situ degradation during the aggregation at 37º C could also play a role in polymorph selection. We have begun to save frozen aliquots of our aggregation samples for subsequent MS analyses of the interesting samples in order to be able to address this in the future. However, it was outside the scope of our original search for the PD polymorph.

With respect to degradation products, in this work a NΔ4-variant is produced to mimic a disease-relevant degradation product and indeed it is found to alter the structural outcome even at low relative concentrations (5%). Have the authors investigated the minimal fraction of the NΔ4 variant necessary to still influence the structural outcome of the predominant WT protein? This type of analysis could have significant relevance to disease-related analysis, where several variants (truncations and PTM variants) are present in trace amounts.

We did not try lower than 5% because it was our goal to test if impurities at this level (which usually go undetected) could influence the aggregation outcomes. We think that directly relating the precise impurity level in these in vitro experiments to in vivo aggregation would be difficult due to the many factors we do not yet understand that appear to guide in vivo polymorph selection.

While on this topic, the authors note that in several of their type 5 fibrils, they find unresolved peptide fragments in their cryo-EM structures. Can the authors speculate if these fragments are indeed peptide degradation products or residues wrapping around the fibril originating from the fibril-incorporated protein?

We will add this speculation to the revised manuscript. The unassigned peptide density most likely originates from the C-terminal residues of the intact chains rather than from a degradation product. The levels of degradation products observed by MS in our other samples were far too low to account for the amount of peptide that would be required for >50% of the fibrils in sample 23 to contain this extra density. Furthermore, in the 5A polymorph the extra peptide density is sometimes present (e.g. sample 52) and sometimes absent (e.g. sample 3), despite the fact that in both samples the coexisting type 5 polymorphs (5m and 5B, respectively) have the peptide bound. Therefore, it appears that subtle differences between 5A polymorphs determine the presence or absence of this density, whereas for 5m and 5B it is consistently present.

In this work, the authors have performed an extensive study of α-synuclein polymorphism. However, despite generating what is likely the largest single data set of fibril structures, they perform very little quantitative analysis of their data. It would be interesting to analyse the relative abundance of fibril polymorphs produced in each reaction. Perhaps from the particle-picking data it could be estimated the relative abundance of each polymorph as well as non-resolved fibrils to generate a more nuanced view of polymorphism beyond overall classifications of the resolved structures. Indeed, from such data it could also be studied if certain protofilaments are more prone to pair in asymmetric fibril structures over others or if fibril asymmetry can be attributed to random pairing of protofilaments in accord with their abundance. This latter point is particularly interesting for the type 1 fibrils. Perhaps, the propensity of α-synuclein to form specific symmetries could also be estimated.

We agree that Cryo-EM datasets contain considerable information that could potentially be used to better understand polymorph populations. We have previously used particle counts as an approximate measure of polymorph abundance; however, the biases introduced during particle picking and subsequent curation are substantial, and we therefore do not consider these counts sufficiently reliable for quantitative comparison of polymorph populations.

Regarding the symmetry of paired filaments, it is clear that the overwhelming preference of all filaments is to pair as symmetric dimers. Among the in vitro polymorphs, type 1 is the most commonly observed to form an asymmetric dimer, either with itself or with the new type 7. However, the number of observations is too small to establish that this represents a statistically meaningful preference. Types 2 and 3 have also been observed to pair in asymmetric fibrils. Overall, we do not think that our dataset is large enough to add statistical weight to previous observations.

The authors note that pH is a strong factor in determining polymorph selection. This does indeed appear to be the case, but other parameters do not appear to show any clear trend. Have the authors investigated the influence of aggregation parameters (agitation, duration) on structural outcomes systematically or quantitatively, such as with principal component analysis? Indeed, they also find that some fibril types that otherwise are not compatible at the same pH appear to co-exist when the shaking parameter is modified. Are the authors then confident in the claim that pH is a deterministic parameter?

We did not systematically vary the agitation but in two cases where it was either intentionally or accidentally varied, we found surprising polymorph outcomes. We felt that these observations were worth reporting, but on their own they do not constitute a thorough study. We would rather conclude that pH is a strong selector and can be deterministic under certain conditions: pure sample, no seeds, continuous or intermittent moderate agitation. We will revise the manuscript to make this clearer.

It is evident from this and other work that amyloid aggregation is highly sensitive to kinetic effects. It is therefore curious that the effect of protein concentration and reaction time has not been systematically investigated. The authors have some data studying dilution series (Figure 6A) and different reaction times (reaction 56&57). Could the authors comment on the effects of these two parameters, and might there be more information touching upon this that could be highlighted in this work?

We did not collect sufficient data to draw conclusions about the effects of protein concentration or aggregation time, and therefore do not think that a quantitative analysis of these parameters is justified by the present dataset.

The authors state that this work likely underreports fibril polymorphisms in samples due to population size or data quality challenges. Could the authors, based on their extensive experience, try to quantify this statement?

Precise quantification would be difficult. The literature has many mentions of amyloids that could not be solved by Cryo-EM due to a lack of twist. In our hands it is very common to have a small subset of non-twisted filaments in a sample and some samples appear to be exclusively non-twisted. Low-abundance or low-quality fibrils are also rather common in our data but also difficult to quantify. Nevertheless, we agree that it would be useful to place a lower bound on this estimate, and we will re-examine our datasets to determine whether this can be quantified in the revised manuscript.

Additionally, the authors point out that the current framework for classifying α-synuclein fibril polymorphism is not sufficient to describe the real complexity of this protein system. However, they do not seem to address some of the recent literature aiming to solve such issues (see Scheres 2026, Connor et al. 2025, Milchberg et al. 2025 & Price et al. 2025).

We agree that we should have discussed this literature in greater detail and will do so in the revised manuscript.

Was any biophysical/biochemical analysis performed of the many structures produced here, such as CD spectroscopy, Proteinase K digestion, dye binding or FTIR, which could act as low-resolution structure identifiers and might help to retrospectively explain some findings in the older literature? Such data would be very useful for the vast majority of researchers, who do not have access to cryo-EM.

We did not perform these analyses precisely because they are low resolution. Retrospectively, such analyses might have been useful for interpreting past data, but most of these methods (particularly Proteinase K resistance) are difficult to compare between laboratories and work best with side-by-side controls. This is why developing a facile method for polymorph identification is one of our main future research goals.

Reviewer #2 (Public review):

Summary:

This manuscript describes insights gained during efforts to reproduce disease-relevant alpha-Synuclein (aSyn) fibrils using recombinant protein in vitro. It follows up on a similar article from this team published in 2024. Although the authors have not been able to produce fibrils with the structure of ex vivo fibrils isolated from patients, they share insights gained into which factors influence the formation of specific fibril polymorphs.

Strengths:

This is quite an unusual manuscript because it goes into minute detail about sample preparation that are usual just mentioned in the Materials and Methods sections of other manuscripts (if at all). This makes it very valuable for the scientific community working on exactly the problem of reproducing disease-relevant aSyn fibrils in vitro (which will be a major breakthrough in the field). The authors present an impressive array of cryo-EM fibril structures, some of which have not been described before.

Weaknesses:

A major concern with the manuscript is that its story and messaging are a bit murky. The authors describe a few new polymorphs, show that some polymorphs (type 1) have small variations, show that sample purity and fragmentation will influence polymorph formation, and present a helical-symmetry mystery. This all reads like a loose collection of findings without any major takeaway. Looking at Table 1, it still seems that the authors do not have a good control over any of these polymorphs. Are they able to make any of these polymorphs reliably? I think the impact of this work could be strengthened if it ended with a reliable protocol for the production of any of the polymorphs described.

It is true that the initial results were a collection of findings compiled while searching for the PD polymorph. However, the trends that we saw in these data inspired us to pursue a more systematic approach which was used to show how impurities play a crucial role in polymorph selection even at low levels. We agree that the impact of the work will be enhanced by summarizing the protocols that can be used to obtain the types 1, 2, 3 and 5 polymorphs and will add this to the revised manuscript.

A second major concern is the quality of the aggregation kinetics and their interpretation. Are these kinetics just done once per concentration? The figure caption talks about 'three independent samples' but it is unclear if this refers to the three different concentrations or NΔ4 percentages used, or true repetitions. Looking at the curves themselves, it seems that only one of the conditions was actually done in triplicate, which should be the minimum to draw conclusions. Further, it would have been helpful to characterize the kinetic data quantitatively. Finally, because there are only kinetic data for a fraction of the conditions tested, it is not clear what they add to the overall manuscript. My recommendation is to either remove the kinetics from the manuscript or substantially expand this section.

In Figure 6A, the three curves represent three independent samples; in panels B–D, each curve similarly represents one independent sample. We will try to clear up the ambiguity in the revised version. We agree that the kinetic data have limited utility for determining kinetic parameters of the aggregation. The data were collected primarily to determine when the aggregation reactions were complete so that samples could be prepared for cryo-EM. Nevertheless, we think that the kinetic traces provide two qualitative observations that are relevant to the structural results: 1) In panels A and C of figure 6, the type 5 polymorphs are associated with shorter lag times, suggesting that they either nucleate faster, or as we propose, arise from a small amount of oligomeric protein in the original sample. 2) The longer lag phase associated with the NΔ4 construct was reproducible (panels B, C and D), suggesting that its intramolecular self-chaperoning effect is enhanced due to the increased positive charge in its N-terminal region. Future studies will determine whether this same electrostatic change also gives rise to enhanced secondary nucleation.

eLife Assessment

This useful study reports potential loss-of-function variants, pseudogenes and gene presence-absence variation across multiple chicken genomes, with potential implications for understanding genome evolution and domestication. The evidence for the central claims is unfortunately incomplete, as the inferences of gene loss are not sufficiently robust to account for assembly and annotation artifacts, and, in addition, the analyses can not distinguish between positive selection and relaxed constraint. The overall claim of large-scale gene loss being adaptive and thus being a major driver of chicken evolution and domestication is therefore not sufficiently supported. The area of the study is of interest to colleagues in evolutionary and comparative genomics as well as animal domestication.

Reviewer #1 (Public review):

Summary:

The authors have assembled the genome of four local chicken breeds from China and analysed their gene content. They come to the conclusion that thousands of genes present in the current reference genome of chicken have become pseudogenized during chicken evolution and domestication. They argue that their study provides strong support for the importance of the "less-is-more" hypothesis for adaptive evolution.

Strengths:

The paper provides medium-quality genome assemblies for four individuals representing four local populations of chickens and analyses their gene content.

Weaknesses:

They have not excluded the possibility that the high rate of putative pseudogenes reflects the presence of errors in gene models, in particular in GC-rich microchromosomes that are challenging to assemble correctly. The paper contains no genotype-phenotype analysis, which means that the adaptive significance of a high rate of pseudogenization, if it exists, is unknown.

Reviewer #2 (Public review):

Summary:

The authors set out to investigate the evolutionary role of gene presence-absence variation and pseudogenization in chicken evolution and domestication. By comparing draft genome assemblies of four indigenous Chinese chicken breeds against the red junglefowl reference genome (GRCg6a) and four PacBio HiFi assemblies, the study proposes that the common ancestor possessed nearly 22,000 genes, and that each domestic lineage independently lost thousands of genes (identifying ~8,000 dispensable genes). The authors conclude that massive loss of function and pseudogenization represent major drivers of chicken evolution under the "less-is-more" hypothesis.

While the concept that gene loss can drive phenotypic diversification during domestication is compelling, the results do not convincingly support the central conclusions. The scale of reported gene loss and the specific patterns of pseudogenization appear to be potentially driven by well-known genome assembly gaps, annotation errors, and sequencing dropouts rather than genuine evolutionary events, and the authors do not provide enough convincing evidence that this is not the case.

Strengths:

(1) The study addresses an important and timely evolutionary question regarding the role of gene loss and loss-of-function variation in animal domestication.

(2) The inclusion of multiple indigenous Chinese chicken breeds alongside high-accuracy PacBio HiFi assemblies provides a valuable comparative genomic dataset.

(3) The authors attempt to evaluate pseudogene transcription using RNA-seq data and check for transcript isoforms that bypass candidate loss-of-function mutations.

Weaknesses:

(1) Unvalidated gene and pseudogene annotations: Long-read and consensus genome assemblies are known to suffer from residual indel errors that create artificial frameshifts and premature stop codons. The frequency of predicted pseudogenes in this study (~3.5%-4.5%) aligns closely with expected baseline annotation error rates. Although the authors state in their Methods that mutations were validated using short reads, this validation is never quantitatively demonstrated or shown in the results. The fact that most proposed pseudogenes are actively transcribed and lack a paralog strongly suggests that many are intact, functional genes affected by sequencing or annotation artifacts.

(2) Assembly gaps and GC-bias mistaken for gene loss: The claim that ancestral chickens possessed ~22,000 protein-coding genes and lost thousands of genes in only ~10,000-50,000 years is inconsistent with the evolutionary conservation of avian genomes. The missing genes are enriched for high GC content and preferentially located on microchromosomes. Avian microchromosomes and dot chromosomes are notoriously GC-rich, repeat-dense, and prone to severe assembly gaps in non-telomere-to-telomere assemblies. The reported gene absences reflect assembly fragmentation and coverage dropouts rather than evolutionary deletions.

(3) Lack of synteny validation: Genuine gene absence requires demonstrating conserved collinear synteny of flanking orthologous genes with an unambiguous sequence deletion at the locus. Relying on sequence alignment or short-read mapping failures across fragmented scaffolds substantially inflates false-positive gene loss calls.

(4) Positional bias of pseudogenization mutations: The observed concentration of pseudogenization mutations in the terminal 10% of coding sequences (the "bathtub" distribution) is characteristic of alignment boundary artifacts and non-canonical translation start/stop annotations, rather than positive selection to disrupt gene ends. Mutations in the terminal 3' region often produce functional proteins with slightly altered C-termini rather than complete loss of function.

(5) Inconsistent terminology: The manuscript alternates between identifying pseudogenes as unitary (lacking a functional paralog in the same genome) and evaluating sequence identity against "parental genes," creating substantial confusion regarding whether loci are duplicated paralogs or orthologous reference genes.

Reviewer #3 (Public review):

Summary:

The authors reanalyze genome assemblies of four indigenous chicken breeds from Yunnan Province together with the red jungle fowl reference (GRCg6a), and search for genes with disrupted protein-coding sequences. They catalog candidate pseudogenes and missing genes to estimate that 7,993 of the ancestral genes are dispensable. They characterize the positional distribution of pseudogenization mutations along coding sequences, their fixation in breeds, their estimated ages, and their pathway enrichments. Most results are replicated in four independent PacBio HiFi-based chicken assemblies. From the biased position of pseudogenization mutations toward CDS ends, their frequent fixation, and the phylogenetic signal in gene-loss patterns, the authors conclude that large-scale loss of function is a major driver of chicken evolution and domestication, consistent with the "less-is-more" hypothesis.

Strengths:

The catalog itself is a substantial resource: the comparison spans multiple closely related genomes, the main patterns are checked in a second, independently assembled set of HiFi genomes, and population resequencing data are used to ask whether the pseudogenization mutations are fixed rather than segregating. The finding that candidate loss-of-function genes are under relaxed purifying selection is well supported. The question of what gene loss contributes to domestication is worth asking, and this is a useful dataset for asking it.

Weaknesses:

The finding that genes carrying disruptive mutations are under relaxed selection is not particularly surprising, and the more interesting claim, that the observed patterns reflect positive selection for gene loss, is less certain in my opinion.

(1) Relaxed purifying selection versus positive selection. The bias of pseudogenization mutations toward the two ends of coding sequences is interpreted as positive or artificial selection, along with elevated dN/dS. But the alternative, that disruptive mutations at gene ends are simply better tolerated, is equally consistent with the results. Several mechanisms would produce this pattern under relaxed constraint without positive selection per se: alternative downstream start sites that rescue 5-prime disruptions; the small fraction of protein truncated by 3-prime disruptions; and the enrichment of disordered regions at protein termini.

(2) The functional status of the pseudogenes is assumed, not demonstrated. Genome-scale work cannot be expected to validate individual genes, but the language of the paper should reflect the candidate status of these calls. Nearly all predicted pseudogenes (~95%) were reported as transcribed in multiple tissues. It is possible for a nonfunctional coding sequence to retain intact regulatory sequences, but the observation deserves more attention in the paper, particularly because transcripts carrying premature termination codons can be the targets of nonsense-mediated decay, which is not discussed. These remain candidate pseudogenes defined by the presence of a putatively large-effect mutation (e.g. premature stop or frameshift).

(3) What "missing" means. For a gene to be scored as completely absent, it could be genuinely deleted, or its allele could be diverged enough that annotation and orthology/mapping no longer detect it. These are different phenomena. Related, since most pseudogenization mutations are reported as fixed or nearly fixed in their populations, the history of alleles matters: it is not clear how the authors established which state is derived, and whether the reference sequence assumed to be functional is in fact the "functional" version.

(4) Limited biological insight into domestication. The main biological interpretation rests on hierarchical clustering of dispensable genes followed by ontology enrichment within clusters (Figure 7a), with narrative connections to breed phenotypes. Only 19.6% of dispensable genes have Gene Ontology assignments, and the phenotype links are speculative. The section on the subspecies origin of the GRCg6a reference is only loosely connected to the loss-of-function story, and the population-genetic analysis supporting it is thin as described.

eLife Assessment

This study provides a valuable and comprehensive in vivo map of proteins in proximity to three vesicle-tethering complexes. The evidence supporting the overall proximity mapping is convincing. However, some aspects of the functional characterization of selected candidates remain incomplete.

Reviewer #1 (Public review):

Summary:

The CATCHR complexes are a family of five multisubunit complexes that act in vesicle tethering in several key transport steps. COG and GARP act at the Golgi, EARP acts on early endosomes, EXOCYST acts in transport to the cell surface, and DSL1 acts on the endoplasmic reticulum (ER). The authors have used in vivo proximity biotinylation and mass spectrometry to look for new neighbours of three of these complexes, COG, GARP, and EARP (despite the title, only two of the three are on the Golgi). The authors then follow up two of the hits, CCDC186 and WWOX, with more directed experiments.

Strengths:

The strength of the paper is that proximity biotinylation is of a high standard. To avoid overexpression, the authors express TurboID-tagged CATCHR subunits in cell lines from which the genes have been deleted. This allows them to confirm that the tagged proteins are functional and correctly located. Mass spectrometry is used to identify the proteins biotinylated in each cell line with four replicates, and the data are clearly presented in figures and supplementary tables. The authors make a good choice of proteins to follow up, as both CCDC186 and WWOX appear potentially interesting.

Weaknesses:

Overall, although the paper is based on a high-quality initial set of data, it seems somewhat incomplete and preliminary. There is undoubted value in presenting a through if descriptive set of in vivo proximity labelling data for a comprehensive overview of proteins or complexes. However, in this case the authors have only addressed three of the five CATCHR complexes, and so it is not a complete overview. It was also somewhat unclear why they examined VPS52 and VPS53, as these are present in both GARP and EARP, which adds some ambiguity, even if they did at least provide useful confirmation of some of the hits with EARP. Of course, a proximity biotinylation analysis does not need to cover all members of a family if it generates substantial biological insight.

However, the investigation of CCDC186 and WWOX does not provide significant insight into either function or mechanism. CCDC186 has already been identified in C. elegans as a protein involved in dense core vesicle biogenesis (CCCP-1, as the authors acknowledge), and work in C. elegans and mammalian cells has already linked it to EARP function. Less has been published on WWOX, but all that is found here are some small changes in Golgi appearance and glycosylation when it is reduced by RNAi. Thus, the paper falls between two stools: it is neither a comprehensive application of proximity biotinylation to the CATCHR family, nor is it the application of proximity biotinylation to reveal new insight into membrane traffic. I feel that for a broad-interest journal such, it should be one or the other of these.

Reviewer #2 (Public review):

In this manuscript, Aragon-Ramirez et al. present the first systematic proximity-interaction map of the three Golgi/endosomal CATCHR tethering complexes - COG, GARP, and EARP. They generated hTERT-RPE1 knockout lines rescued with C-terminally TurboID-tagged subunits (COG4, COG6, VPS50, VPS52, VPS53, VPS54) expressed from the COG4 promoter at near-endogenous levels, verified that each construct rescues its KO phenotype, and confirmed expected localization by immunofluorescence. Fifteen-minute biotin pulses followed by streptavidin capture and label-free DIA mass spectrometry, benchmarked against GFP-TurboID, yielded compartment-resolved neighbor lists. The central claim of this work is that each complex sits within a distinct "trafficking module" of coiled-coil tethers (CCTs), SNAREs, SM proteins, Rab GTPases, coats, and homeostasis regulators. COG neighbors nearly all Golgi golgins plus the STX5-SCFD1 fusion machinery, with COG4 and COG6 lobes showing overlapping but non-identical hierarchies - this is offered as in vivo support for a two-lobe model. GARP associates with TGN golgins GOLGA1/GOLGA4, STX16 and partners, TBC1D23, and CLINT1. EARP associates with GRIPAP1, RELCH, RAB11FIP5, and the VPS33B-VIPAS39 (CHEVI) SM complex; a VPS53 MUN-domain mutant loses VPS33B proximity while retaining VPS50 labeling. Two hits are followed up in this study. CCDC186, a poorly characterized coiled-coil protein, localizes to the TGN and, when ectopically anchored to mitochondria, captures ~60 nm vesicles - presented as direct evidence of tethering activity. WWOX, a tumor suppressor with no prior trafficking role, colocalizes with COG8 in the medial Golgi; siRNA knockdown reduces Golgi area, increases HPA and GNL lectin binding (O- and N-glycosylation defects), and displaces COPB2 from the Golgi. Based on these findings, the authors conclude that CATCHRs are not isolated tethers but organizing hubs that assemble compartment-specific tethering-and-fusion modules. Overall, this is a solid piece of work that will be of interest to cell biologists.

(1) The CCDC186 mitochondrial assay demonstrates sufficiency in a non-native context but includes no loss-of-function work, and the cargo-specificity result carrying most of the interpretation is "data not shown." At a minimum, the authors should show KO/KD and rescue data.

(2) The WWOX section rests on a single siRNA with no second oligo, no rescue, knockdown shown only by RT-PCR, and localization based entirely on overexpressed myc-tagged protein.

(3) Proximity of labeling does not distinguish direct from indirect interactions. When referring to "interactions", the authors either need to show recombinant protein binding data, or soften the tone to acknowledge potential indirect interactions.

(4) The VPS53 MUN-domain mutant design rests on a "manuscript in preparation," and the mutant's localization isn't shown (VPS50 labeling establishes complex incorporation, not correct targeting). The HEK293T WWOX replication is "data not shown." The authors should either show the data or delete these claims.

(5) References 73 and 78 are duplicates.

(6) "NZR" is used in the introduction. Should this be NRZ?

Reviewer #3 (Public review):

Summary:

This manuscript presents a comprehensive proximity proteomics analysis of Golgi- and endosome-associated CATCHR complexes, including COG, GARP, and EARP, using near-endogenously expressed TurboID-tagged subunits. The study aims to define how these tethering complexes organize distinct trafficking modules involving coiled-coil tethers, Rab-associated proteins, SNAREs, SM proteins, and other trafficking regulators. In addition to validating known associations, the authors identify CCDC186 as a candidate vesicle tether and WWOX as a potential regulator of Golgi homeostasis and glycosylation. The work provides a broad resource for understanding the spatial organization of CATCHR-associated trafficking networks. However, several conclusions require further experimental and statistical support, particularly those interpreting proximity-labeling data as physical interactions or evidence of discrete functional complexes.

Strengths:

The manuscript addresses an important question in membrane trafficking and provides a systematic comparison of the proximity interactomes of COG, GARP, and EARP complexes. The use of near-endogenously expressed TurboID-tagged subunits is a strength, as it may reduce artifacts associated with protein overexpression. The dataset is comprehensive and has the potential to serve as a valuable resource for investigators studying Golgi and endosomal trafficking. The comparative analysis identifies both known trafficking factors and potentially novel regulators, including CCDC186 and WWOX. The functional follow-up experiments add biological relevance to the proteomic findings and extend the study beyond descriptive mapping. Overall, the scope is well defined, and the manuscript proposes an interesting model in which CATCHR complexes act as organizing hubs for vesicle tethering and fusion.

Weaknesses:

A major limitation is that TurboID proximity labeling is repeatedly interpreted as evidence of physical interaction or assembly into discrete complexes, although the method primarily reports spatial proximity. The soluble GFP-TurboID control may not adequately account for enrichment caused by membrane confinement and high local protein concentration in Golgi/endosomal microdomains. Some spatial enrichment analyses do not reach statistical significance, weakening claims of compartment-specific labeling. Several low-fold-change SNARE hits are emphasized despite limited enrichment. Additional quantitative imaging is needed, including colocalization analysis of streptavidin labeling with Golgi/endosomal markers and localization of GFP-TurboID. The WWOX knockdown phenotype requires validation by rescue, independent siRNA, or CRISPR-based approaches. Several supporting data, quantifications, figure corrections, and nomenclature revisions are also needed.

eLife Assessment

This important study investigates how GDNF treatment restores nerve cells in the bowel of a mouse model of Hirschsprung disease, and proposes that this regeneration occurs through diverse resident precursor cells and a non-canonical signaling pathway. The evidence is solid for the ability of the treatment to induce new bowel nerve cells and for a contribution from multiple precursor populations, supported by extensive cell tracing and imaging experiments. This work will be of interest to researchers in developmental biology and peripheral neurobiology.

Reviewer #1 (Public review):

Gary, Soret et al., present an interesting and ambitious study investigating the cellular and signaling mechanisms by which GDNF induces enteric neurogenesis in a disease model of HSCR. The manuscript combines scRNA-Seq, pharmacological inhibition, and several lineage-tracing strategies. The lineage tracing experiments in particular are technically impressive and clearly represent a substantial amount of work. The figures are generally beautiful and high quality, and the biological question is an important one.

However, while I found the study interesting, I also think that several of the major conclusions are substantially stronger than what the current data support. In particular, the scRNA-Seq dataset that the study is founded on is difficult to interpret because of the RFP-based enrichment strategy, the lack of WT reference controls, and the very non-stringent FACS gating. Several mechanistic claims are also based primarily on expression patterns or sequencing results.

Major concerns:

(1) The G4-RFP based enrichment strategy raises some concerns. The authors note that 88-90% of SOX10+ glial cells (where did this number come from, it doesn't seem to match the range in the bar graph?) and only 70% of GDNF-induced neurons. They then sort in "yield" mode using a non-stringent gating strategy, but do not provide the flow graphs in the supplements for interpretation. Consistent with this, the initial dataset contains multiple non-ENS populations, including lymphoid, myeloid cells etc, suggesting that their strategy, in addition to missing cell populations, additionally includes potential negative cells based on background fluorescence.

(2) It's not clear to me why the authors did not include a wild-type control for comparison. Due to the RFP-enrichment strategy, it is additionally difficult to compare to integrated with scRNA-seq datasets. The comparison seems important because the central question is not only whether GDNF induces neurons in the mutant colon, but whether the induced cells and associated populations resemble those found in a normal ENS.

(3) The proportional changes in Figure 2 are hard to interpret. The authors write that GDNF treatment leads to an enrichment in enteric neurons, "at the expense of" SCPs. This seems to be a strange conclusion or writing, unless the authors are suggesting that certain cell populations are additionally depleted by GDNF treatment. I think the authors should provide stronger support, or dial down on conclusions based on cluster proportions, given the sorting strategy.

(4) Some of the mechanistic conclusions are far too strong for the evidence. For instance, the claim that GDNF signals through GFRa1/2 based on only expression UMAPs is not justified. The authors should at least confirm some of the major findings via smFISH (HCR or RNA-Scope), and dial down the mechanistic claims. The pharmacological data is more supportive but still indirect. This section would be stronger if the authors validated NCAM1/FAK activation in the specific progenitor populations proposed to respond to GDNF.

(5) The inhibitors are administered during the same P4-8 window as GDNF. Given that the authors report cellular-level responses as early as 6 hours post GDNF treatment, it is important to know whether the inhibitors were already active at the time of GDNF administration. Why were the inhibitors not administered prior to the start time of GDNF treatment?

(6) The authors draw inferences and conclusions based on IHC images, but do not provide any details on the analysis procedures. For example, in Figure 3, the authors interpret changes in NCAM and FAK expression level. However, it does not appear that there are notable differences in intensity between the two timepoints. There are however, differences in signal coverage. Without knowing what was actually measured and quantified, it is not possible to interpret the results. Please provide the necessary information for all experiments in the methods section.

(7) The final results section introduces one of the more surprising claims in the paper, that a non-neural crest-derived progenitor contributes to regeneration, but the section ends quite quickly and abruptly after introducing the observation. The authors should provide additional validation or interpretations of the data.

Reviewer #2 (Public review):

Summary:

Previous work from this group demonstrated regeneration of the ENS following exogenous GDNF treatment within the aganglionic portion of the bowel in several Hirschsprung (HSCR) murine models as well as colon from HSCR patients (Soret, et. al., Gastro. 2020). Focusing on the Holstein (HolTg/Tg) HSCR mouse model, the authors build upon their prior work utilizing lineage tracing, immunohistochemistry, scRNA sequencing, and pharmacological methods to further delineate the mechanisms and cell types contributing to ENS regeneration in this context. This work adds to the knowledge base regarding natural ENS development as well as ENS generation outside of natural ENS development. Furthermore, this work provides important clinical implications for potential curatives treatments for HSCR disease.

The conclusions in the paper are overall well supported by the data with the majority of technical and model limitations openly acknowledged. Strengths include the use of scRNA sequencing, several genetic mouse models with ample, well-planned time points within experiments. However, additional analysis, clarity or more detail around experimental protocols, and broader discussion of prior studies would strengthen the manuscript by improving interpretation of the findings and placing them more clearly within the context of existing work in the field.

First, utilizing the G4-RFP transgene for ENS cell selection and subsequent scRNA sequencing of RFP+ cells, the authors nicely demonstrate the presence of known cell clusters (based on markers and analysis from prior sequencing studies) including Schwann cell precursors (SCPs), enteric glial cells (EGCs) and neuron subtypes in the aganglionic colon of HolTg/Tg GDNF-treated and untreated mice. Further use of this dataset led to the discovery of Ncam1 expression, a GDNF receptor, within all ENS cell clusters, suggesting importance of this protein in the GDNF-induced ENS regeneration phenotype. Interestingly, Ret was limited to some neuron types. On the protein level, temporal and GDNF-treatment changes in NCAM1 expression and downstream phospho-FAK(Y397) were nicely demonstrated via Western blot. Mechanistically, the importance of NCAM1 in ENS regeneration was demonstrated given pharmacologic blockade of downstream FAK signaling via PF-562271 resulted in significantly fewer GDNF-induced neurons. The paper would be strengthened here, however, if the following areas were addressed:

1) Although the GDNF-induced regeneration appears likely through an NCAM1 signaling mechanism, inhibition of FAK phosphorylation by PF-562271 could affect more than NCAM1 signaling. Blocking NCAM signaling through another method (such as through NCAM1 targeted monoclonal antibodies or small molecules) would support the authors' interpretations further.

2) A point of ambiguity is the exact cells included in the final scRNAseq analysis. The authors noted they flowed and gated broadly, including RFP negative cells, in the initial set of cells selected for sequencing (given RFP expression is not visualized within all neurons and glia in GDNF-treated HolTg/Tg mice.) Pan-neuronal (Elavl4, Tubb3) and pan-glial (Sox10) marker expression were utilized to select cells for final analysis (unsupervised analysis, pseudotime trajectories, etc.) Here, it is unclear if RFP expression was examined in these cells, either by looking at unmapped reads or if included in the initial alignment. If this is discernable within the authors' data set, this provides an opportunity for an interesting additional analysis to determine if progenitors or neuronal or glia populations differ in the RFP+ and RFP- groups.

3) The authors presumably sequenced both the submucosal and myenteric plexus ENS components within their scRNAseq analysis. Given the relatively sparse numbers of ENS cells in the submucosal plexus compared to myenteric plexus in the distal colon, this is unlikely to change their analysis or conclusions. However, given their tissue analysis focuses on the myenteric plexus, this difference should be acknowledged.

The authors go on to further to utilize their scRNA sequencing data set with pseudotime trajectory analysis to determine that SCPs appear to go through an EGC-like state prior to GDNF-induced neurogenesis. This was followed nicely by use of transgenic mice (Dhh-Cre) and immunohistochemistry within their HolTg/Tg model to capture the SCP population and demonstrate in vivo this progression. Additionally, they were able to demonstrate that temporally, SCPs generated neurons much sooner (within 6 hours of GDNF-treatment) compared to neural crest derived EGCs (labeled by Slc18a2-Cre and GFAP-CreERT2 lines).

Fascinating here as well is that the authors unearthed that most generated neurons following GDNF-treatment appeared to derive from direct cell transdifferentiation (suggested by EdU incorporation investigation at various time points) and that these neurons did not seem to originate from SCPs or EGCs (i.e. a non-neural crest origin.) Acknowledging that their mouse genetic tools and sequencing could have missed a NCC-derived population, the authors go on to label neural crest derivates utilizing the Wnt1-Cre2 transgene in their wildtype and HolTg/Tg mouse model and find that while Wnt1 labels the vast majority of neurons in wildtype mice, nearly 25% of neurons in P20 HolTg/Tg mice appear non-NCC derived. Finally, once again utilizing various genetic mouse lines for lineage tracing and immunohistochemistry, the authors demonstrate NCC-derived neural progenitors (SCPs, EGCs) appear to preferentially give rise to cholinergic neurons where non-NCC derived neurons tend to be more nitrergic.

4) The high magnification of the majority of images provides the reader with extremely compelling evidence in regard to visible overlap or lack thereof across various reporter lines, antibody markers, and EdU labeling. Unfortunately, this can somewhat create a trade off with the area or number of cells examined which appears somewhat less than the number of cells and/or area examined by many prior studies in the field. The near equal averages across the three mice in each group in many of their experiments makes this less of a concern, but the paper may be strengthened by noting exactly how the 3-11 images per mouse were selected. Were these randomly selected across the tissue, moving from mesenteric to anti-mesenteric? Or caudally to distally?

5) In line with this, the authors report a near 100% of Wnt1-Cre2 driven reporter expression in wildtype mice but a large portion (~25%) of neurons in HolTg/Tg model appear non-NCC derived (i.e. not Wnt1-Cre2 labeled.) The original Wnt1Cre line (Danielian, et.al., Curr Biol. 1998) has been reported to incompletely label all neural crest derivatives/ENS (Hari, et. al., Development. 2012.; Deal, et. al., Dev Bio. 2021). To my knowledge, the same type of analysis has not been carried out with the same rigor in the ENS with the Wnt1-Cre2 line. It could be -- depending on tissue sampling, area covered via imaging, and if there is any patchy or unique patterning to non-NCC derived neuro regeneration -- any incomplete labeling of neural crest by Wnt1-Cre2 could be missed. Of course, alternative interpretations are that the non-labeled cells are truly non-NCC derived. Utilizing other lineage tracing models for other non-NCC derived lineages may help address this issue, but would require many mouse crosses and additional experiments, and thus likely outside the scope of this manuscript. However, this caveat should be addressed.

6) A very important and fascinating find by the authors is that the NCC versus non-NCC derivatives appear to preferentially give rise to cholinergic or nitrergic neurons respectively. This will have important implications in treatment options for ENS regeneration not only within HSCR disease, but other ENS disorders as well. A point of discussion the authors missed out on is several previous reports regarding skewing of ENS neurons (typically toward higher nitrergic numbers) in ganglionic and/or hypoganglionic segments of HSCR bowel in murine models and patients (Zaitoun, et.al., Neurogastroenterol. Motil. 2013.; Musser, et.al, CMGH. 2015.; Cheng, et.al., J Pediatr Surg, 2017.; Sukhada, et. al., Front. Cell Dev. Biol. 2022.) Could ganglionic portions of the bowel in HSCR disease contain more of the non-Wnt1 labeled population? Why do proportions in the aganglionic region generate correct proportions following GDNF-induced treatment compared to ganglionic bowel? This does not need to be experimentally addressed in the manuscript, but including in the discussion impresses upon the audience the importance of the authors findings and that these factors need to be further experimentally delineated and considered with any therapeutic interventions.

Reviewer #3 (Public review):

Summary:

In this work, the authors aim to build on their previous work to further define the mechanism by which GDNF can induce enteric nervous system migration and differentiation in the Holstein mouse model (Hol Tg/Tg) of Hirschsprung's disease (HSCR). They show that GDNF can cause neuronal differentiation from either Schwann cell precursors (SCP) that migrate from the periphery and/or enteric glia (or neural crest precursors located in the intestine). Surprisingly, the rescue effect of GDNF is mediated through signaling with NCAM1 rather than the canonical receptor RET, with blockade of NCAM1 significantly reducing the number of GDNF-treatment induced neurons in the distal colon of Holstein mice. The authors then perform scRNA-seq data of the colonic ENS from Holstein mice +/- GDNF, and pseudotime analysis of this data indicates the SCP downregulate SCP genes and upregulate classical enteric glial genes on their transition to becoming enteric neurons. Following this, the authors employ Dhh-Cre mice (to label SCP), Slc18a2Cre and GFAPCreERT2 (to label enteric glia) and finally Wnt1Cre2 mice (to label neural crest derived cells) to assess the kinetics and end identity of enteric neurons driven by GDNF treatment. Using these animal models, the authors propose a model by which transdifferentiation of SCP gives rise to enteric neurons first, followed by transdifferentiation of enteric glia; the resulting enteric neurons labelled by Dhh, Slc18a2 or GFAP Cres are all biased to a cholinergic lineage, raising a questions about the source of nitrergic neurons. Finally, the authors postulate that at least some nitrergic neurons come from a non-neural crest lineage in GDNF treated Hol Tg/Tg mice as they are not labelled by a Wnt1Cre2 model, while all ENS cells are labelled in three wildtype Wnt1Cre2Tg/+;R26YFP/+ mice.

Strengths and Weaknesses:

This work convincingly shows that NCAM1 is required for GDNF-induced rescue of the Holstein mouse model of HSCR and, along with the NCAM1 staining in human HSCR tissue, highlights the potential of this treatment even in HSCR patients with loss of function RET mutations. The major weakness of this study is in the interpretation of the mouse models; many of these models are not fully penetrant/show mosaicism in other studies (like the DhhCre and Wnt1Cre) or may not only label the specific subpopulation they present (in this case, the GfapCreERT2 and Slc18a2Cre; these genes have been shown in Schwann cells/SCP in other studies, and the expression pattern of these two genes outside of the gut at the relevant developmental timepoints are not shown). While these are unavoidable limitations with our current mouse models, the authors need to clearly acknowledge these limitations in the interpretation of their data (with the DhhCre and Wnt1Cre) or more definitively show the models are only labelling enteric glia (in the case of the Gfap and Slc18a2Cre). In addition, in some figures the authors should add untreated Hol Tg/Tg and ideally WT mice so readers can contextualise the effect of GDNF on Hol Tg/Tg mice. Finally, it appears the statistics throughout the paper are performed on using each ROI taken from n=3-5 animals - this is inappropriate, as images from the same animal are not independent samples. The statistical unit in question for every analysis performed should be 1 animal, thus the statistics should be done on the n=3-5 animals, not the n=3-11 images from 3-5 animals (which leads to an n of 6-55).

Specific comments:

In general I find the author's conclusions are relatively well supported, albeit a little overstated for the evidence presented in the later figures and with the need to correct the statistical analysis. For Figures 1-5, I have only minor comments, as follows.

In Figure 1-2, the Gata4-RFP reporter is used to sort cells for scRNA-seq, and the authors get a large number of non-ENS cells so utilise Elavl4 and Sox10 expression to pull out neurons and glia to analyse. Do other putative neuronal/glial genes pull out the same cells, and can the authors find evidence of non-neural crest derived glia/neurons in this dataset? This would ensure there isn't a bias in this first analysis and strengthen the later claims respectively.

In Figure 3, the interpretation of increased NCAM1 and pFAK would be aided by adding the MFI for the untreated Hol Tg/Tg and ideally WT mice at p10 to assess if this is a normal developmental increase or induced by GDNF treatment - I would ask the authors add at least untreated Hol Tg/Tg at p10 as authors already present this data as images in figure 3D. Similarly, it would be nice to have neuronal counts of untreated Hol Tg/Tg and WT mice presented in Figure 4c to assess if NCAM1 inhibition completely or only partially prevents the effect of GDNF.

In the text accompanying Figure 2 and 5, the authors use a variety of markers of assign SCP or enteric glia identity to the clusters, but some of the enteric glia genes can be expressed by Schwann cells/SCP in other contexts - it is worth adding references to the genes chosen to define SCP and enteric glia so readers can understand why those were chosen and the strength of evidence for each marker. For me, with the exception of Dhh I do not find any of these genes definitive as, at least on the SCP/Schwann cell side, they have been shown to express Gfap, Slc18a2, Sox2 and single cell analysis indicates they also express Cpe. The ability for SCP/Schwann cells to express both Gfap and Slc18a2 is important for the interpretation of the upcoming experiments.

In Figure 6, the authors state in line 213 that "quantitative analysis as a function of time revealed that GFAP+ cells in the distal colon are not all derived from Dhh-expressing SCPs on the first day of treatment"; however, the DhhCre is restricted to specific SCP subsets (Xie, Meng, et al. "Schwann cell precursors contribute to skeletal formation during embryonic development in mice and zebrafish." Proceedings of the National Academy of Sciences 116.30 (2019): 15068-15073) and thus may not be labelling all SCP coming into the intestine. As far as I know there are no models that would allow labelling of all SCP without labelling enteric glia so would require the generation of a new models or techniques that is out of scope for this work - however, the authors should acknowledge the possibility of Dhh negative SCP contributing to the ENS.

Figure 7 and 8 focuses on the contribution of Dhh+ cells, Slc18a2+ cells and cells expressing GFAP between p3-p8 to the ENS of GDNF treated Hol Tg/Tg mice. The authors first show that by p20 the number of neurons per mm2 is equivalent to those at p60, indicating p20 as an appropriate timepoint to assess the relative contribution of each pool of glia to the resulting neurons. The authors show that neurons derived from a DhhCre are detectable first, then Slc18a2, followed finally by GFAP. This data supports the authors claims that neurons first arise from Dhh+ SCP, but as I raised earlier, both Slc18a2 and GFAP can be expressed by schwann cells later in development - the authors in fact show that GFAP is in fact expressed by Dhh+ cells in figure 6, and showed with pseudotime analysis that SCP undergo a transition to Gfap+ Slc18a2+ glial cells before becoming neurons. The data presented here negates that analysis, or at least suggests some Dhh+ cells skip this step, otherwise the kinetics of neuronal differentiation would align across the 3 lines used. Could the authors address this discrepancy? For example, one addition could be to show that SCP/schwann cells on extrinsic gut innervating nerve fibres do not express Gfap or Slc18a2 at the timepoints used. In addition, their scRNA-seq analysis suggests that Gfap & Slc18a2 are expressed in the same cells, so one would expect similar kinetics in both populations - what is the overlap of GFAP staining with Slc18a2-YFP expression at the earlier stages (say p6 and p10?). Alternatively, the inducible nature of the GFAPCreERT2 means some bona fide GFAP expressing cells may be missed if the tamoxifen dose is not saturating, thus underestimating the contribution of this population to the total neuron count. As such, could the authors please show co-staining with GFAP in some induced GFAPCreERT2 samples to assess the effectiveness of this Cre. As with other figures, it would also be nice to add Holstein negative reporters at p20 as a control to assess the level of contribution each one of these cell lineages has in a normally developing animal compared to GDNF treated Hol Tg/Tg mice.

In Figure 9, the authors show that neurons derived from labelled cells in the DhhCre-YFP or Slc18a2Cre-YFP skew strongly cholinergic (81%) compared to nitrergic (13%), but only 52% of the total neurons in GDNF treated Hol Tg/Tg mice are cholinergic, while 42% are NOS1+. The authors say that a similar trend is seen in Slc18a2Cre-YFP mice with a 'slightly higher percentage' reflecting Slc18a2 expression in neurons. However, this 'slightly higher' percentage looks to be about 40%, which is the amount expected in GDNF treated Hol Tg/Tg. I think the authors underplay the level of nitrergic neurons that are labelled in the Slc18a2Cre mice and should consider the possibility that Slc18a2+ glia can give rise to the nitrergic neurons seen in GDNF treated Holstein mice. This data also contrasts with prior reports that indicate SCP tend to become NOS1 expressing in a Ret or Ednrb loss of function HSCR model (Uesaka, Toshihiro, et al. "Enhanced enteric neurogenesis by Schwann cell precursors in mouse models of Hirschsprung disease." Glia 69.11 (2021): 2575-2590), a discrepancy worth discussing.

In Figure 10, the authors assess the contribution of neural crest to the ENS of WT and Hol Tg/Tg mice using a Wnt1Cre2 line, and conclude there is non-neural crest contribution to the ENS of GDNF treated Hol Tg/Tg mice. This is an interesting idea and supported by a few studies the authors mention in the discussion; however, the labelling of neural crest derived cells in Wnt1Cre2 may not be fully penetrant. While this line has a well established leaky phenotype, others have reported it can have patchy recombination in the neural crest too (potentially in a background dependent manner, according to the line information on Jackson laboratories). For example, recent works shows significant mosaicism in the embryonic phase (Gandhi, S., Du, E. J., Pangilinan, E. S., & Harland, R. M. (2024). The Wnt1-Cre2 transgene causes aberrant recombination in non-neural crest cell types. bioRxiv, 2024-11.) This may not be the case in the authors home institution in a FVB background, as they show all HuCD+ and Sox+ cells overlap with the Wnt1Cre2 reporter, but the Hol Tg/Tg mice have aberrant neural crest development - this could interfere Wnt1 expression thus the effectiveness of the Wnt1Cre2, thus leading to non-labelled, but actually neural crest derived cells. It is also possible that those neurons are truly from a non-neural crest background, and the neural crest labelling tools are all flawed in one way or another - as such, I think the authors just need to discuss this alternative possibility in the discussion.

Finally, Figure 11 shows NCAM1 expression in human tissue resections from HSCR patients. This data bolsters the idea that GDNF treatment could be an effective treatment for HSCR. The methods indicate that 3 tissue samples from HSCR patients were obtained, but staining is only shown for one - could all 3 be included, along with secondary only controls? This is important as human tissue resections are often processed many hours after removal, so are prone to higher background. It would also be interesting to include tissue from non-HSCR patients (the controls used most often in other studies are resections from anorectal malformations which are performed at approximately the same age as HSCR resections) to see if NCAM1 expression is influenced by the absence of an ENS in human patients, but I understand these samples are not always possible to obtain. If not possible, the authors could consider analysing publicly available RNA sequencing datasets to assess if RET is solely expressed in mature neuronal populations while NCAM1 is expressed by glial and neuronal populations like in their mice data.

Overall, the authors clearly show that GDNF can drive differentiation of neurons from different glial populations through NCAM1 not RET, and supports continued effort to translate this work to the clinic as a potential therapy for HSCR patients. I am not convinced that the relative contributions of each glial subpopulation can be extrapolated from the mouse models used - this is a problem across the field, and will only be rectified with the development of new models, which is out of scope for this work. This work complements recent work showing NCAM1-GDNF signaling promotes neurogenesis in glia in Ednrb-/- mice (Mueller, Jessica L., et al. "Intramuscular enteric glia persist in Hirschsprung disease and undergo neurogenesis in response to GDNF-NCAM1 signaling." Scientific Reports 15.1 (2025): 33200), and will add to our understanding of neural development.

Reviewer #4 (Public review):

Summary: The manuscript by Gary et al works to reveal processes that generate enteric neurons in the distal colon of Holstein mutant mice that experience aganglionosis and are an established model of Hirschsprung disease (HSCR) following GDNF enema infusion. The primary goal of the study is to determine the how rectal infusion (enema) of GDNF drives neurogenesis in these mutants. The studies focus on determining the molecules that mediate this GDNF effect and identifying the cellular origins of the newly formed neurons. Given that prior work from this group and others has indicated formation of postnatal enteric neurons is feasible, understanding this process is an important step for the field. The data presented partially support the claims of the study. The analysis described do not support unequivocable conclusion that "transdifferentiation" is occurring. To instill confidence in the stated conclusions and make the text appropriately clear, clarifications of the methods and additional information is needed.

Strengths:

(1) The authors use in vivo experimentation with multiple mouse lines including Dhh-cre, Slc18A2-cre, and GFAP-creERT2 to trace the production of enteric neurons in the context of GDNF enema in the established Holstein mouse model of Hirschsprung disease over a time line of postnatal days 4 (P4) to P10.

(2) The authors generate novel molecular profiles of enteric neurons induced in the distal colons of Holstein HSCR mice after GDNF enema induction by flow sorting for fluorescently labeled and adjacent populations with novel gating parameters followed by single cell RNA-sequencing.

(3) The authors recognize broad expression of NCAM1 amongst the induced neurons in scRNA-seq data and apply experimental approaches to further investigate the role NCAM1 in generation of GDNF-induced ENS neurons.

(4) The authors apply a widely utilized experimental approach, EdU-labeling, to assess proliferation in the immediate timeframe of GDNF-inducation in an effort to discern the timing of when the newly produced neurons exit the cell cycle.

Weaknesses:

(1) The article lacks sufficient information justifying use of the Holstein HSCR mouse model for the study. Authors need be more thorough when introducing the readers to the various HSCR mouse models they consider analyzing and provide an expanded justification for use of the Holstein model in the introduction so the audience can appreciate the rationale behind the analysis presented.

(2) The text minimally describes the G4-RFP reporter that is a critical element of the analysis and upon which the scRNA-seq profiling hinges. Given the data presented in this submission it's not clear how much of the ENS this G4-RFP line labels.

(3) The authors state that "NCAM1 is already present in SOX10+ cells before GDNF treatment begins at P4, both within and outside extrinsic nerve fibers (Fig.3b,c)." However, the data shown in Figure 3 panels B and D do not allow one to conclude co-localization of Sox10 with NCAM1 or FAK. Because ENS cells are so closely positioned with one another the signal the authors present could be due to adjacent cells or processes of cells above and below the plane of Sox10+ nuclei.

(4) The authors use the inhibitor PF-562271 in an attempt to specifically inhibit phospho-FAK[Y397] shown in Figure 4. This particular inhibitor has the known side effect of causing apoptosis in phospho-FAK[Y397]+ cells as shown by Hu et al 2017 Cancer Sci (DOI: 10.1111/cas.13256). Because this compound causes apoptosis in phospho-FAK[Y397]+ cells, the data presented do not prove that the lack of neurons produced in this condition is due to inhibition of phospho-FAK[Y397]+ cells making the neurons versus those phospho-FAK[Y397]+ cells simply dying very early in the process.

(5) In the text describing the results of Figure 1A compared to Figure 1B the authors have missed an opportunity to elaborate on the spatial distribution of what appear to be small ganglia in the GDNF treated colon of Holstein mutant mice. The schematic shown is rather simple and it's unclear from the text where these ganglia are distributed circumferentially around the gut wall.

(6) The immunohistochemical labeling for Phox2b shown in Figure 6 is odd. Phox2b is expressed in neuronal progenitors, enteric glia, and ALL enteric neurons as shown in multiple publications. The images shown in Figure 6 offer an outlined region that appears to be a ganglion; however, within that encircled area fewer than half of the cells are labeling with Phox2b by this study.

(7) The authors conclude that "transdifferentiation" is the origin of the ENS neurons that appear in GDNF-treated Holstein mice. However, the data show simply that most of the newly produced neurons have not recently gone through cell division based on lack of EdU incorporation. Given the data presented, other mechanisms may be occurring and should be considered as possibilities.

(8) The authors utilized a Wnt1-cre2 transgenic line that has known issues with expression in the male germline and ectopic expression in cells that are dependent upon the reporter line utilized, like the Rosa26-YFP of this study. The methods lack information on whether crosses were performed in such a manner as to avoid issues with male germline activation of this reporter and the potential for ectopic expression cannot be excluded based on the information provided in the study.

(9) The study lacks data on how GDNF enemas affect enteric neuron density and ganglia distribution in wildtype animals. If the signaling mechanism that produces new neurons in the Holstein model is also operating in wildtype animals, this could be crucial information for investigators interested in neuronal replacement to treat ENS damage resulting from environmental damage, disease, or age.

eLife Assessment

This work demonstrates an objective way to select parameter values for a quadratic integrate-and-fire model so that its bifurcation diagram matches a specific target diagram, generated from the Wang-Buzsaki model. The method is useful for the field and is presented with convincing evidence. The method is currently limited in its ability to be applied to data, but improves our mathematical tools to treat a rarely studied type of bifurcation.

Reviewer #1 (Public review):

[Editors' note: this version has been assessed by the Reviewing Editor without further input from the original reviewers. The authors have addressed the comments raised in the previous round of review.]

Summary:

From a big picture viewpoint, this work aims to provide a method to fit parameters of reduced models for neural dynamics so that the resulting tuned model has a bifurcation diagram that matches that of a more complex, computationally expensive model. The matching of bifurcation diagrams ensures that the model dynamics agree on a region of parameter space, rather than just at specially tuned values, and that the models share properties such as qualitative features of their phase response curves, as the authors demonstrate. A notable point is the inclusion of extracellular potassium concentration dynamics into the reduced model - here, the quadratic integrate-and-fire model; this is straightforward but nonetheless useful for studying certain phenomena.

Strengths:

The paper demonstrates the method specifically on the fitting of the quadratic integrate-and-fire model, with potassium concentration dynamics included, to the Wang-Buzsaki model extended to include the potassium component. The method works very well overall in this instance. The resulting model is thoroughly compared with the original, in terms of bifurcation diagrams, production of various activity patterns, phase response curves, and associated phase-locking and synchronization properties.

Weaknesses:

It is important to note that the proposed method requires that a target bifurcation diagram be known. In practical terms, this means that the method may be well suited to fitting a reduced model to another, more complicated model, but is not likely to be useful for fitting the model to data.

Reviewer #2 (Public review):

Summary:

The authors derive an integrate-and-fire model to describe the dynamics of a more complex Wang-Buzsaki model and compare the two models. A detailed discussion of bifurcation schemes in both models is convincing and allows us to evaluate the simpler model.

Strengths:

The idea is interesting, and the mathematical approach appears to be convincing. In addition, differences between the simple and original models are also discussed.

Author response:

Public Reviews:

Reviewer #1 (Public review):

Summary:

From a big picture viewpoint, this work aims to provide a method to fit parameters of reduced models for neural dynamics so that the resulting tuned model has a bifurcation diagram that matches that of a more complex, computationally expensive model. The matching of bifurcation diagrams ensures that the model dynamics agree on a region of parameter space, rather than just at specially tuned values, and that the models share properties such as qualitative features of their phase response curves, as the authors demonstrate. A notable point is the inclusion of extracellular potassium concentration dynamics into the reduced model - here, the quadratic integrate-and-fire model; this is straightforward but nonetheless useful for studying certain phenomena.

Strengths:

The paper demonstrates the method specifically on the fitting of the quadratic integrateand-fire model, with potassium concentration dynamics included, to the Wang-Buzsaki model extended to include the potassium component. The method works very well overall in this instance. The resulting model is thoroughly compared with the original, in terms of bifurcation diagrams, production of various activity patterns, phase response curves, and associated phase-locking and synchronization properties.

Weaknesses:

It is important to note that the proposed method requires that a target bifurcation diagram be known. In practical terms, this means that the method may be well suited to fitting a reduced model to another, more complicated model, but is not likely to be useful for fitting the model to data. Certainly, the authors did not illustrate any such application. Secondly, the authors do not provide any sort of general algorithm but rather give a demonstration of a single example of fitting one specific reduced model to one specific conductance-based model.

We thank the reviewer for this critical assessment. It is true that we demonstrate our approach using as target the bifurcation diagram of a more realistic model. In principle, the method would be applicable to experimental systems if parameter space is sampled under appropriate experimental conditions, e.g., by recording at different extracellular potassium concentrations. However, this is challenging: generating reliable” experimental bifurcation diagrams” would require tightly controlled experimental repetitions under various conditions, particularly for reconstructing two-dimensional bifurcation diagrams. We hope that this work encourages the development of such methods. We have added a discussion of this point; see the paragraph starting at line 549.

We have also included a general algorithm (Table I) and provide a second example illustrating the procedure (Supplementary Fig. S2).

Finally, the main idea of the paper seems to me to be a natural descendant of the chain of reasoning, starting from Rinzel - continuing through Bertram; Golubitsky/Kaper/Josic; Izhikevich; and others - that a fundamental way to think about neuronal models, especially those involving bursting dynamics, is in terms of their bifurcation structure. According to this line of reasoning, two models are “the same” if they have the same bifurcation structure. Thus, it becomes natural to fit a reduced model to a more complicated model based on the bifurcation structure. The authors deserve credit for recognizing and implementing this step, and their work may be a useful example to the community. But the manuscript should have described and cited this chain of works to put the current study in the correct context.

We have added a paragraph in the Discussion section (starting at line 517) to better situate the manuscript within the relevant literature and to explicitly acknowledge the chain of work.

Reviewer #1 (Recommendations for the authors):

Please see my public review. In line with my comments, I recommend that the authors either (a) provide a general algorithm for fitting at least a class of reduced models (i.e., those that satisfy some general assumptions) to a class of bifurcation diagrams, or (b) provide at least one more example of implementing their method. Step (b) would not need to be done to the same degree of thoroughness as the example they provided (e.g., the PRCs and synchrony need not be considered), but to me, this step would be very important if (a) is impractical. Otherwise, the paper should probably be rewritten to de-emphasize the message that this is a general method; instead, this should be a paper about specifically fitting the QIF (with potassium dynamics) to the Wang-Buzsaki model (with potassium dynamics).

We provide a general algorithm for deriving a quadratic integrate-and-fire model with dependence on a biophysical parameter by fitting the bifurcation structure of a given class I conductance based neuron model near an SNL bifurcation induced by this parameter; see Table I.

In addition, we provide a second example of the reduction procedure: motivated by Hesse et al. (Nature Communications, 10.1038/s41467-022-31195-6, 2022), we derive a QIF model that captures dependence on temperature instead of potassium concentration; see Supplementary Fig. S2.

Not surprisingly, I also think it’s essential that the authors describe and cite the chain of works on thinking of neuronal models in equivalence classes based on bifurcation diagrams, and make clear that this paper builds on the ideas set forth in that chain.

We thank the reviewer for this comment. As mentioned above, we have added a paragraph in the Discussion section, starting at line 517, to acknowledge this chain of work.

Also, the authors should make clear that their method is not one for fitting a model directly to data, which will require rewriting at least the first paragraph of their Discussion section.

We thank the reviewer for helping us make our manuscript clearer. To avoid confusion, we have clarified this point already in the Introduction (see lines 52-57) and have included a new paragraph in the Discussion (starting at line 549).

Other specific corrections are:

(1) Typos should be fixed, as the paper has several. The first line of the abstract has one (“concentrations” → “concentration”), for starters. “Original model” on pg. 3 is missing “be” in “can defined”. “ceases” → “cease” on pg. 13. “nerons” → “neurons” on pg. 19. “standart” → “standard” pg. 24.

Done. Additional typos were also corrected.

(2) The abstract mentions “consequences in networks” in its second sentence. This is misleading because studying network dynamics is not at all the main emphasis of the paper, but rather a corollary application of the main ideas, so some restructuring of the abstract is needed. Similarly, the final abstract sentence overstates somewhat what was done with studying synchronization and should be rewritten more precisely.

We have restructured the abstract accordingly.

(3) For readers who are interested in the ideas here but not familiar with the QIF model, it will be very difficult to follow the first paragraph of Results. Elementary aspects of QIF dynamics should be explained here (e.g., what is the saddle-node bifurcation), and a basic figure panel about this should be included in Figure 1.

We added a supplementary figure (Figure S1) adapted from Izhikevich for readers who might not be familiar with the QIF model.

(4) Bottom lines of page 3 should be reworded to make clear that the slow variables are averaged over each member of a family of fast subsystem limit cycles. Also, “one limit action potential cycle” is an awkward phrase.

We rephrased this sentence (see paragraph starting at line 140).

(5) Text under system (1) – why isn’t c mentioned? Also, references to Figure 3 should be to Figure 2 here. And authors should state what they mean by “target model” and be clear about whether it includes potassium dynamics and/or pump current.

c scales the parabola corresponding to the branch of fixed points, given by c(I_app − I_SN,0 − I_pump) = −a(ν − ν_SN)². Consequently, it also affects the position of the homoclinic bifurcation: In the previous version of the manuscript, c was inadvertently omitted from the expression for the branch of fixed points; this has now been corrected. See paragraph starting at line 154.

Figure references have been corrected.

By target model, we mean the conductance-based model that includes potassium dynamics and a pump current, in our case System 4. We clarified this point at the beginning of the Results section (see paragraph starting at line 116). Throughout the manuscript, we now explicitly indicate when we refer only to its fast subsystem and whether the pump current is included. In particular, note that the parameter derivation shown in Figure 4 is performed on the fast subsystem of the target model, in the absence of the pump current. I_pump can be considered as a potassium-dependent contribution to the applied current, and can be added a posteriori to the QIF model. See paragraph starting at line 162.

(6) Next par: is the “saddle-node bifurcation” that with I_app as bifurcation parameter? Please clarify.

Yes, it is the saddle-node bifurcation with I_app as bifurcation parameter. We have clarified this in the manuscript; see the paragraph starting at line 170.

(7) Bottom pg. 5: does “beyond” mean above? below?

We meant above (larger values of ). In the text, we have replaced “beyond” with “larger than”. See paragraph starting at line 178.

(8) Formula for v_r at top of page 6: Please specify what formula for I_pump is being used here.

The formula for I_pump is given in Eq. 5d. We are using the same formula throughout the paper.

Note that to clarify the reduction procedure, we derive QIF parameters to match the bifurcation diagram with respect to the applied current of the fast subsystem of the target model when I_pump = 0. Reintroducing I_pump produces the same horizontal shift in this bifurcation diagram for both the QIF and Wang–Buzsáki versions.

We have restructured the paragraph starting at line 178 to clarify these aspects.

(9) Three lines below this: I don’t understand what “matching...is appreciable” and “in the continuity of...” mean. Please revise and also explain why a closer matching of v_r to the min voltages in Figure 4d was not used, and exactly how the v_r that is shown was chosen.

With “matching...is appreciable”, we meant that values assigned to v_r should be close to the minimum voltage values reached during spiking. With ”in the continuity of...”, we meant that when .(SNIC case), we choose v_r by extrapolating the linear fit performed on the values of v_r assigned when , (homoclinic case).

When , v_r was chosen so that the homoclinic bifurcation occurs at the same value of applied current as in the fast subsystem of the target model. This is explained in the paragraph starting at line 178 (see Eq. 2). This criterion also allows the minimum voltage values reached during spiking to be captured reasonably well (compare the green dotted line and the purple solid line in panel e of Figure 4).

We have rewritten the paragraph starting at line 186 to clarify these aspects.

(10) Bottom page 6 - reference to Figure 3e should be 4e. Also, the text mentions the shrinkage of spike amplitude, but the figure shows that vth increases over most of the K+ range before decreasing, so a correction is needed.

We corrected the figure reference.

The maximal voltage of the limit cycles of the target model’s fast subsystem (upper purple curve in Figure 4e) increases slightly between and , by less than 1mV. It then decreases by about 27mV before the fold of limit cycles. The sigmoidal function vth () allows us to capture this substantial decrease in the QIF model. The small preceding increase is not captured. We reformulated the text to avoid confusion (see paragraph starting at line 209).

(11) Figure 4d: Why is E_K plotted here? It should be mentioned in the caption and text. More generally, the caption for Figure 4e should be expanded to mention what the purple curves are, what is the black curve for K < K_SNL, and what the other structures shown are. Finally, the text describes that theSNIC/SNL/Hom is determined by the choice of v_r relative to v_SN, so it’s not clear what is I_app,SNL in the caption - please clarify.

In conductance-based models, higher weakens the potassium concentration gradient, thereby raising E_K. The sodium and potassium reversal potentials typically bound voltage oscillations during spiking (see for example Chander and Chakravarthy, PLOS ONE, 10.1371/journal.pone.0048802, 2012), so the minimum voltage of spikes is expected to be higher when is larger. We plotted E_K in Figure 4d to show that the increase of the reset voltage v_r at larger reflects this effect in the QIF version of the model. We clarified this in the caption of Figure 4 and in the text (see paragraph starting at line 199).

Purple curves show families of limit cycles, while black curves, including the one for , show families of fixed points. The green curve shows the linear fit of v_r from panel d. All these have now been included in the legend.

In the QIF model, the onset bifurcation (SNIC, SNL, or homoclinic) is indeed determined by the choice of v_r relative to v_SN. Figure 4e shows the bifurcation diagram of the fast subsystem of the conductance-based model (Wang-Buzsáki). This is a bifurcation diagram with respect to , for a fixed value of applied current. We chose to fix I_app at its value at the SNL bifurcation, denoted I_app,SNL. I_app,SNL is near 0.22 (see Figure 3a).

(12) Eqn. (2a): Shouldn’t v_SN depend on potassium like I_SN and I_pump do? What is the formula for Ipump there? Why isn’t the RHS of (2b) dependent on v as in the original model? Please clarify.

For simplicity, we did not include a potassium dependence for v_SN in the QIF model. Instead, we set it to its value at the SNL bifurcation (Figure 4b). This is explained in the paragraph starting at line 199: “We notice that v_SN and the normal form coefficient a are relatively conserved in this interval. We fix them to their value at [K⁺]_o,SNL.”

The formula for I_pump is given in Eq. 5d. The potassium dynamics depends on the voltage via the reset rule in Eq. 3d. This allows us to capture the small increments in at each action potential in the original model (see for example Figure 6c,h). We have clarified these two points in the manuscript (see paragraph starting at line 223).

(13) Figure 3: Please indicate the criticality of the Hopf bifurcations shown.

The legend of Fig. 3 now indicates that the Hopf bifurcations are subcritical. The same clarification has been added to the following figures as well.

(14) Bottom pg. 9: Why isn’t there an I_pump term as in eqn. (6a)? Please clarify. 

You are correct, the I_pump term should be included in the equation for the averaged slow subsystem of the QIF model (see paragraph starting at line 243); it was accidentally omitted in the manuscript. Thank you for pointing this out.

(15) Top pg. 11: It’s important to reference the slow averaged dynamics here, which allows K+ to increase. Also, this first paragraph should already explain that this averaged dynamics is only relevant along the family of FS periodic orbits, not during the recovery when the FS has a branch of stable equilibria.

The averaged slow subsystem is indeed only relevant along families of limit cycles of the fast subsystem. Along families of equilibria, averaging is not necessary and the standard slow subsystem can be used. We now explicitly define this standard slow subsystem for both Wang-Buzsáki and the QIF model (see paragraphs starting at lines 241 and 628). In panels e and j of Figure 6, both systems are now represented.

In the paragraph starting at line 273, we now refer to the averaged slow subsystem to explain the overall increase of during bursts (purple curves in Fig. 6e,j), and to the standard slow subsystem to explain the decrease of during quiescent phases (black curves).

(16) Pg. 11, par 3: This is unnecessarily confusing. Please try to reword and clarify this paragraph.

We have simplified this paragraph (starting at line 293). The key point is that the reduction to the averaged slow subsystem is not valid too close to the homoclinic bifurcation.

(17) Pg. 13, end of Scenario 2: Is there any evidence this is a canard effect and not a noise effect? If so, please mention the evidence; otherwise, perhaps take this out.

What happens there appears to be a noise-induced canard effect: in the beginning of the burst, the system follows a family of stable limit cycles of the fast subsystem, i.e. a stable object. However, at some point, noise induces a transition to a portion of trajectory where the system evolves near the saddle branch, i.e. a repelling object, for a substantial amount of time. Such phenomena have been thoroughly investigated in the literature, and can also be obtained in a deterministic way; see for example Marin et al. (Physical Review E 90, 042718, 2014). Bursting traces similar to the one in Figure 7c are observed experimentally (see, for example, Figure 4c of Marin et al.), which is why we considered it worth mentioning. We have revised the paragraph starting at line 332 to clarify this point.

(18) I only see 4 curves in Figure 9a,c, but the legend has 5. Are two on top of each other? Please clarify.

Yes, the curve for = 7.21mM lies beneath the curve for = 5.21mM. This has been clarified in the figure caption.

(19) Text should note that the QIF iPRC does not develop a negative region at high K+ and high phase, as WB iPRC does.

We have updated the paragraph starting at line 409 to mention this.

(20) Pg. 16, line 4: “at the network scale” is cryptic - a more precise phrase would be preferable.

We have reformulated the sentence to clarify its meaning (see paragraph starting at line 380).

(21) Pg. 16, line 9: Reordering of words could make this clearer.

Done (see paragraph starting at line 385).

(22) Pg. 16: I am confused by line 14 because the big changes in the iPRC in Figure 9c do not align with the spike phase in Figure 9d. Please clarify what is meant here.

In the QIF model, at a given phase, the iPRC is the inverse of the slope of the voltage trace as a function of phase. Flatter slopes in Figure 9d therefore correspond to larger iPRC values in Figure 9c. This is illustrated in Figure S5. We have revised the paragraph starting at line 393 to make this point clearer.

(23) Pg. 16: Please clarify what is meant by a “delta synapse”.

By “delta synapse,” we meant a configuration in which each spike induces an instantaneous voltage jump in the postsynaptic neuron, modeled using the Dirac delta distribution. We have replaced the term “delta synapse” with “pulse-coupled,” which is more commonly used in the literature, and have added a clarification at its first occurrence in the manuscript.

(24) Discussion, line 2: Delete comma.

Done.

(25) Importantly, as noted above, the first par. needs to be rewritten since the presented method won’t work directly from data or from a target model for which most of the parameters, and hence the bifurcation diagram, are not known.

As mentioned above, we have included a new paragraph in the Discussion, starting at line 549, to clarify this point.

(26) Pg. 18: ”Originally” → ”Typically”, perhaps?

Done.

(27) Note the work of Marder et al. on temperature-related neural variability.

We thank the reviewer for this comment. We have added two relevant references from the work of Marder and colleagues addressing temperature-dependent neural variability and ionic concentrations in our manuscript (see the sentence starting on line 537).

(28) Pg. 20: Cut the ”Potassium dynamics and network models” subsection since it does not add anything substantive as written (or else expand it and include it in the subsection below).

We have expanded this paragraph and incorporated it into the subsequent subsection, as suggested by the reviewer.

(29) Finally, it’s a bit confusing that the authors refer to the potassium concentration as a slow variable yet have an instantaneous jump in this quantity at reset in their QIF model (i.e., instantaneous is VERY fast). Some explanation about this should be provided. Do they make the general assumption that ∆_K is small, for example, such that this reset reflects the slow nature of K+ evolution (i.e., during the reset period, K+ would only change slowly, and hence by a small amount)?

Yes, ∆_K is chosen to be small, to capture the behavior of the original model (compare for example panels c and h of Figure 6). As a result, in the QIF model, in the same way as in the original model, despite the fact that the dynamics of includes a fast component, on average evolves slowly. By using the averaging method, we can determine whether overall increases or decreases.

We clarified this in the manuscript, in the paragraph starting at line 243.

Reviewer #2 (Public review):

Summary:

The authors derive an integrate-and-fire model to describe the dynamics of a more complex Wang-Buzsaki model and compare the two models. A detailed discussion of bifurcation schemes in both models is convincing and allows us to evaluate the simpler model.

Strengths:

The idea is interesting, and the mathematical approach appears to be convincing. In addition, differences between the simple and original models are also discussed.

Weaknesses:

A comparison to experimental data is necessary to support the theoretical work.

As mentioned above in our answer to Reviewer 1, we demonstrate our method using as target the bifurcation diagram of a more realistic neuron model. Ideally, one would want to derive phenomenological models that capture bifurcation structures obtained from data. However, this is challenging and beyond the scope of the present study. We hope that this work encourages the development of such methods. We have revised the Introduction (see lines 52-57) and added a paragraph in the Discussion (see the paragraph starting at line 549) addressing this point.

Reviewer #2 (Recommendations for the authors):

The manuscript is well-structured; however, it appears that it has been edited with less care. Please see comments below:

(1) Page 2: “A third bifurcation, the saddle-homoclinic orbit (HOM) bifurcation,”: provide a reference for the bifurcation.

We have added a reference to the book by Izhikevich (see paragraph starting at line 63).

We have added additional references in the Introduction that we considered helpful.

(2) Page 3: “while a larger concentrations it is mediated by...”: remove “it”.

There was indeed a typo in this sentence. The intended phrasing is: “while at larger concentrations it is mediated by...”. We have corrected it accordingly (paragraph starting at line 134).

(3) Figure 2, caption: “dashed lines for unstable branches”: this is a dotted line.

Corrected to “dotted lines”. Thank you.

(4) Page 4: “is smaller than vSN (Fig. 3c),”: this figure panel does not exist, as well as the Fig.3d referred to afterwards. Please correct.

We intended to refer to Fig. 2. Figure references have been corrected. See paragraph starting at line 154.

(5) Page 6: “Fig. 3a-d shows ISN,0, vSN and a for [K]+o between 4 and 16 mM”: Fig.3c+d do not exist, please correct. Similar comment to “the absence of pump (Fig. 3e).” on the same page.

We intended to refer to Fig. 4. Figure references have been corrected (paragraphs starting at lines 199 and 209).

(6) Page 8: “(panel A)” → ”panel (a)”.

Done.

(7) Figure 4e: What is the meaning of the green dotted curve?

This curve represents the linear fit of the reset voltage v_r from panel d of Fig. 4, to show that the minimal voltage values of the limit cycles are also well captured. We have added this curve to the legend and included a brief explanation in the figure caption.

eLife Assessment

This important study investigates how experimentally introducing two facultative bacterial endosymbionts into the Russian wheat aphid, Diuraphis noxia, affects aphid performance, dispersal, and damage to cereal host plants and the authors provide solid evidence for contrasting symbiont-associated phenotypes under controlled conditions: Rickettsiella increases plant damage while reducing wing production and dispersal, whereas Regiella reduces feeding damage and, at some time points, aphid population growth. The stable establishment of these novel symbiont-host associations and complementary experiments spanning individual aphids, whole plants, populations, and mesocosms are notable strengths and the revised manuscript better clarifies the experimental approaches and the context dependence of symbiont effects; however, the underlying mechanisms remain unresolved, horizontal transmission is inferred rather than directly demonstrated, and limited replication and temporal variability constrain some population-level conclusions. Potential applications to pest management therefore require further validation under field conditions. The study will interest researchers working on insect symbiosis, plant-insect interactions, and biologically based pest management.

Reviewer #1 (Public review):

[Editors' note: this version has been assessed by the Reviewing Editor without further input from the original reviewers. The authors have addressed the comments raised in the previous round of review.]

Summary:

In this study, the authors examine what happens when two facultative endosymbionts, Rickettsiella viridis and Regiella insecticola, are introduced into a novel aphid host, the Russian wheat aphid (Diuraphis noxia). They ask whether these introduced symbionts affect aphid performance, plant damage, alate production, dispersal, plant defense responses, and symbiont dynamics. The main result is that the two symbionts have contrasting effects: Rickettsiella tends to increase plant damage and reduce dispersal-related traits, whereas Regiella tends to reduce plant damage and aphid population growth, with less evidence for an effect on dispersal.

Strengths:

The manuscript presents successful establishment of stable transinfected populations of an agriculturally important aphid species, which is a substantial technical achievement in itself. I also appreciated that the authors examined the system across several experimental contexts, including different host plants, mixed cages at two temperatures, whole-plant assays, and a mesocosm dispersal experiment, rather than relying on a single laboratory setup. Taken together, these experiments provide a useful and reasonably convincing demonstration that novel symbiont associations can generate contrasting phenotypes in this system.

Reviewer #2 (Public review):

Summary:

The authors generated two novel aphid-symbiont associations and examined the impact of these new symbiotic associations on plant-insect-symbiont interactions. The authors notably provide detailed phenotypic assessments of the insect hosts and host plants. They show that one introduced symbiont, Rickettsiella, increases aphid-induced damage to host plants, while the other, Regiella, ameliorates aphid damage. The authors suggest that such novel insect-symbiont pairings may be used as tools to mitigate crop damage in the future.

Strengths:

Although a few experiments seem to have limited sample sizes and limited statistical power, these are often complemented with highly replicated smaller-scale experiments. The combination of larger mesocosm and population-level experiments along with assessments of individual insects generally provides a comprehensive depiction of the effects of these symbionts on their hosts. The opposing impacts of Regiella and Rickettsiella infection on the aphid host plant are of broad interest. It is also surprising that the host plants did not exhibit strong differences in canonical defensive signalling, despite these differences.

Weaknesses:

It is a little surprising that mesocosm-dispersal experiments were not also conducted using Regiella-infected lines. At several points throughout the manuscript, the idea of using symbiont transfections to reduce plant harm is raised. I can understand that these experiments are likely time-, space-, and resource-intensive, but that seems like these would have been relevant experiments, especially in the context of controlling damage to plants.

Reviewer #3 (Public review):

Summary:

The authors were investigating the impact of introducing novel facultative bacterial endosymbionts into the pest aphid, Diuraphis noxia, to explore the possibility of using facultative symbionts as a crop protection tool. They successfully established the vertical transmission of both endosymbionts and performed a series of aphid performance and dispersal experiments together with measurement of aphid feeding on host plant health, growth, and metabolism. While most of the experiments revealed no effect of the endosymbionts, some significant treatment effects were found, showing that Rickettsiella reduced aphid dispersal, and Regiella reduced aphid population growth and feeding damage.

Strengths:

The team worked with two novel facultative symbionts (Rickettsiella viridis and Regiella insecticola) that they were able to successfully establish in D. noxia. The data were collected and analyzed using solid, well-described methodology.

Weaknesses:

While interpretation of the data is reasonable, the few experiments which revealed significant treatment effects rest on relatively small sample sizes.

Measuring symbiont density is difficult. The authors use quantitative PCR to measure the "density" of endosymbionts relative to a host gene. This is a standard approach in the field; however, recent work has shown that endosymbionts like the aphid primary endosymbiont, Buchnera, are variably polyploid [1]; further the aphid cells that house the symbionts are also highly polyploid and variable in their ploidy [2]. It is important to understand that what is being measured when using qPCR is DNA copy number and not quantification of the number of symbiont cells. Alternative approaches to measuring symbiont density include flow cytometry [3], and SymbiQuant [4], a machine vision tool that can quantitatively characterize symbiont populations from DAPI-stained confocal images. These alternate approaches also have their limitations. Currently, there is no perfect approach to measuring symbiont density, which remains an important measure in experiments such as these. Put simply, it is important for a reader to be aware of the limitations of each approach and interpret data accordingly.

[1] Komaki, K., and H. Ishikawa. 2000. Genomic copy number of intracellular bacterial symbionts of aphids varies in response to developmental stage and morph of their host. Insect Biochemistry and Molecular Biology 30:253-258.

[2] Nozaki, T., and S. Shigenobu. 2022. Ploidy dynamics in aphid host cells harboring bacterial symbionts. Scientific Reports 12:9111.

[3] Simonet, P., G. Duport, K. Gaget, M. Weiss-Gayet, S. Colella, G. Febvay, H. Charles, J. Viñuelas, A. Heddi, and F. Calevro. 2016. Direct flow cytometry measurements reveal a fine-tuning of symbiotic cell dynamics according to the host developmental needs in aphid symbiosis. Scientific Reports 6:19967.

[4] James, E. B., X. Pan, O. Schwartz, and A. C. C. Wilson. 2022. SymbiQuant: A machine learning object detection tool for polyploid independent estimates of endosymbiont population size. Frontiers in Microbiology 13:816608.

Impact and Significance:

Food security and production, and pest control are major challenges facing the human population. This work contributes knowledge that will benefit the development of alternate pest control strategies in agriculture.

Author response:

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

eLife Assessment:

This important study investigates how experimentally introducing two facultative bacterial endosymbionts into the Russian wheat aphid, Diuraphis noxia, affects aphid performance, dispersal, and damage to cereal host plants. The authors provide solid evidence that the two symbionts can generate contrasting phenotypes: Rickettsiella increases plant damage while reducing wing formation and dispersal, whereas Regiella reduces aphid population growth and feeding damage. The successful establishment and stable transmission of these novel symbiont-host associations, combined with experiments spanning individual, whole-plant, population and mesocosm scales, are notable strengths of the work; however, the mechanisms underlying these effects remain unresolved, evidence for horizontal transmission is indirect, and some population-level conclusions rely on relatively small sample sizes or effects that are not consistently detected across time points, and therefore the potential application of these findings to pest management remains promising but speculative. The study will be of broad interest to researchers working on insect symbiosis, plant-insect interactions, and biologically based approaches to pest management.

We have made revisions to the manuscript to cover issues raised around sample numbers and mechanisms. We appreciate that we have not been able to finalize the exact mechanism underlying plant damage effects. We note that while comparisons of population performance were limited by the number of populations we could feasibly maintain; sample sizes were substantial in some of the other experiments. We also do substantiate effects through a combination of experimental approaches that start with controlled conditions and then encompass more complex environments.

Public Reviews:

Reviewer #1 (Public review):

Summary:

In this study, the authors examine what happens when two facultative endosymbionts, Rickettsiella viridis and Regiella insecticola, are introduced into a novel aphid host, the Russian wheat aphid (Diuraphis noxia). They ask whether these introduced symbionts affect aphid performance, plant damage, alate production, dispersal, plant defense responses, and symbiont dynamics. The main result is that the two symbionts have contrasting effects: Rickettsiella tends to increase plant damage and reduce dispersal-related traits, whereas Regiella tends to reduce plant damage and aphid population growth, with less evidence for an effect on dispersal.

Strengths:

The manuscript presents successful establishment of stable transinfected populations of an agriculturally important aphid species, which is a substantial technical achievement in itself. I also appreciated that the authors examined the system across several experimental contexts, including different host plants, mixed cages at two temperatures, whole-plant assays, and a mesocosm dispersal experiment, rather than relying on a single laboratory setup. Taken together, these experiments provide a useful and reasonably convincing demonstration that novel symbiont associations can generate contrasting phenotypes in this system.

We thank the reviewer for recognizing the strengths of the work and for providing extensive comments.

Weaknesses:

There are some major aspects of this paper that I thought could be strengthened. My main concern is that the manuscript feels broader than it is conceptually focused. A wide range of outcomes is measured, which gives the study breadth, but it also makes the central question harder to identify. As written, the paper reads more strongly as a proof-of-principle demonstration of ecologically relevant phenotypes than as a tightly framed test of a specific biological idea.

The broad range of tests in our work was intentional. Rather than relying on a single experimental approach or scale, we designed the study using multiple complementary approaches to independently evaluate the effects of endosymbionts. Thus, our conclusions are supported across multiple experimental contexts rather than by a single experiment or scale. For example, the effects on plant damage were consistent across different host plants, including wheat and barley (Figures 1 & S1), and across different experimental scales, ranging from individual plants maintained in small cages (Figure 1) to a dispersal experiment involving 24 plants (Figure 5). Similarly, aphid fitness was evaluated both at the individual level, using single aphids maintained on individual plants under favorable conditions (Figures S5 & S6), and at the population level under crowding conditions (Figures 3 & 4).

Despite the breadth of measurements, the study is focused on establishing robust evidence for the contrasting effects of the two endosymbionts on aphid dispersal and plant feeding damage. To help address this concern, we have moved the summary table from the Supplementary Materials to the main text (now Table 1), which provides an overview of the experimental approaches and main findings and should help readers more clearly see how the different experiments are connected.

A second issue is that the biological basis of the reported phenotypes remains less developed than the phenotypic description itself. The authors make a genuine effort to address mechanism through JA, JA-Ile, SA, and metabolomic profiling, but these analyses only partially explain the main results. The negative result for the canonical defense markers is informative, yet it still leaves a substantial gap between the observed variation in plant damage and the processes responsible for it.

Our analyses of JA, JA-Ile, SA, and the metabolomic profiles provide some initial insights, but we appreciate that they do not fully explain the differences in plant damage observed between treatments. The primary aim of this study was to evaluate the phenotypic effects of the endosymbionts and their potential for agricultural application, rather than to provide a comprehensive mechanistic explanation. We have accordingly avoided overinterpreting the mechanistic results and now explicitly state that elucidating the underlying biological mechanisms will be an important direction for future research in Discussion section.

I also think some caution is needed in how the two symbionts are compared. The authors explain why some follow-up experiments were designed differently for Rickettsiella and Regiella, and that rationale is understandable. Still, because the downstream assays were not fully matched, the paper is strongest when each symbiont is interpreted on its own terms rather than as a strict comparison.

Our initial plant-damage experiment was designed as a first comparison to test whether different endosymbionts can have diverse and contrasting effects on their aphid host population and plant damage. We then investigated the individual phenotypes of each endosymbiont in greater detail, particularly in relation to their potential agricultural applications. Specifically, our results suggest that Regiella may reduce plant damage, whereas Rickettsiella may reduce dispersal. Based on these early findings, some further experiments were conducted with slightly different experimental setups. Nevertheless, many of the experiments conducted for the two endosymbionts were broadly comparable. We designed the additional experiment carried out only with Rickettsiella to test whether reduced alate production observed in our earlier experiments also translated into reduced dispersal at the population level. An equivalent experiment with Regiella was not undertaken because we failed to detect an effect of this endosymbiont on alate frequency in our preceding experiments. We have clarified this rationale in the Materials and methods section (“Aphid dispersal ability and plant feeding damage in mesocosms”).

Overall, I would suggest softening the Significance Statement so that it more clearly reflects what is directly shown here, namely that introduced symbionts can alter plant damage and dispersal-related phenotypes under controlled conditions, rather than implying that the study directly tests management utility in agricultural settings.

We have done this in the Significance Statement. We appreciate that the current experiments have been carried out under controlled conditions, rather than in agricultural settings. Pending permit approval, we are currently planning to extend this work to contained field settings to test whether effects on plant damage and dispersal ability are also observed under less controlled conditions.

Reviewer #2 (Public review):

Summary:

The authors generated two novel aphid-symbiont associations and examined the impact of these new symbiotic associations on plant-insect-symbiont interactions. The authors notably provide detailed phenotypic assessments of the insect hosts and host plants. They show that one introduced symbiont, Rickettsiella, increases aphid-induced damage to host plants, while the other, Regiella, ameliorates aphid damage. The authors suggest that such novel insect-symbiont pairings may be used as tools to mitigate crop damage in the future.

Strengths:

Although a few experiments seem to have limited sample sizes and limited statistical power, these are often complemented with highly replicated smaller-scale experiments. The combination of larger mesocosm and population-level experiments along with assessments of individual insects generally provides a comprehensive depiction of the effects of these symbionts on their hosts. The opposing impacts of Regiella and Rickettsiella infection on the aphid host plant are of broad interest. It is also surprising that the host plants did not exhibit strong differences in canonical defensive signalling, despite these differences.

Weaknesses:

One thing that I struggled a little with was the rapid spread of Regiella in the shared plant experiments. Possibly this could be attributed to an increased reproductive output (due to faster developmental time, and/or an increase in fecundity) or efficient horizontal transmission. However, the other experiments performed indicate a slight negative impact (Figure 4a) or no influence (Figure 4C, 4D, Figure S6) of Regiella infection on host fitness. Given these other results, it seems that Regiella must spread fairly efficiently between hosts, which comes as a surprise, and there are very few examples of horizontal transmission of Regiella like this in the literature. The manuscript would benefit from a clear and direct demonstration of horizontal transmission, rather than it being inferred indirectly. The similar spread observed in the Rickettsiella mixed cages is less surprising, because there are several examples where this has been demonstrated.

We agree that the rapid spread of Regiella in the shared-plant experiments cannot be readily explained by host fitness alone, though we have noted fitness benefits of Regiella in a different transinfection in oat aphids (Yu et al., 2025). In a previous study with transinfected green peach aphids and despite a substantial fitness cost, we found that Rickettsiella can spread relatively rapidly in a population and show high stability (Gu et al., 2023) and perhaps transmission of Regiella follows a similar pathway. However, whereas Rickettsiella may spread through plant tissues, Regiella showed relatively low levels of horizontal transmission through this pathway.

We certainly agree that more work is required to establish the mechanism and dynamics of horizontal transmission in this system. Rather than focusing on mechanism, our objective here was to examine endosymbiont spread where intact plants were available and where there was a mixed aphid population. Note that we also conducted an additional experiment in which Regiella-infected aphids were present at a frequency of only 10% of the initial population, and in this situation Regiella nevertheless still increased in frequency including to a low Cp value in most (8/10) replicates, highlighting its persistence and potential to increase in populations.

References:

Gu et al., A rapidly spreading deleterious aphid endosymbiont that uses horizontal as well as vertical transmission. Proc Natl Acad Sci USA 120, e2217278120 (2023).

Yu et al., A persistent bacterial Regiella transinfection in the bird cherry-oat aphid Rhopalosiphum padi increasing host fitness and decreasing plant virus transmission. Pest Manag Sci 81, 2791-2799 (2025).

It is also a little surprising that mesocosm-dispersal experiments were not also conducted using Regiella-infected lines. At several points throughout the manuscript, the idea of using symbiont transfections to reduce plant harm is raised. I can understand that these experiments are likely time-, space-, and resource-intensive, but that seems like these would have been relevant experiments, especially in the context of controlling damage to plants.

We conducted the final mesocosm-dispersal experiment specifically with Rickettsiella because our earlier individual-plant experiments had already shown a clear reduction in alate production in Rickettsiella-infected aphids, together with effects on plant damage (Figure S1I) and population growth (Figure 3C). In contrast, we did not detect a significant difference in alate frequency between Regiella-infected and wild type aphid strains in the similar set up experiments (Figure S1I and Figure 4C). We therefore designed the additional experiment to test whether the reduced alate production observed with Rickettsiella also translated into reduced dispersal at the population level. We did not conduct the same experiment with Regiella because there was no difference in alate frequency in our earlier experiments. We have also added this explanation in Materials and methods section (“Aphid dispersal ability and plant feeding damage in mesocosms”). We do appreciate however that future experiments on dispersal of Regiella will be worthwhile resources permitting.

Reviewer #3 (Public review):

Summary:

The authors were investigating the impact of introducing novel facultative bacterial endosymbionts into the pest aphid, Diuraphis noxia, to explore the possibility of using facultative symbionts as a crop protection tool. They successfully established the vertical transmission of both endosymbionts and performed a series of aphid performance and dispersal experiments together with measurement of aphid feeding on host plant health, growth, and metabolism. While most of the experiments revealed no effect of the endosymbionts, some significant treatment effects were found, showing that Rickettsiella reduced aphid dispersal, and Regiella reduced aphid population growth and feeding damage.

Strengths:

The team worked with two novel facultative symbionts (Rickettsiella viridis and Regiella insecticola) that they were able to successfully establish in D. noxia. The data were collected and analyzed using solid, well-described methodology.

Weaknesses:

While interpretation of the data is reasonable, the few experiments which revealed significant treatment effects rest on relatively small sample sizes.

We acknowledge that more replication is always desirable, but we would also argue that significant effects were not marginal and replication was substantial in many cases (e. g. 9-10 replicate plants per damage treatment evaluation). We were also focused on using multiple experimental approaches and scales to independently and repeatedly evaluate the effects of endosymbionts on aphid fitness, wing development, plant damage, and aphid dispersal. Thus, conclusions are not based on a single experiment or experimental scale. For plant damage, for example, we observed consistent effects across different host plants, including wheat and barley (Figure 1 and Figure S1), as well as across different experimental scales, from individual plants maintained in small cages (Figure 1) to a dispersal experiment involving 24 plants (Figure 5). Similarly, aphid fitness was evaluated both at the individual level using single aphids maintained on individual plants under favorable conditions (60 replicates per treatment) (Figures S5 & S6) and at the population level under crowding conditions (Figures 3 & 4). These complementary experimental designs allowed us to examine whether the observed phenotypes were consistent across different environmental and population contexts. We did face challenges in high levels of replication of independent aphid strains in population cage experiments but attempted to replicate as much as possible given the resources that were available.

Measuring symbiont density is difficult. The authors use quantitative PCR to measure the "density" of endosymbionts relative to a host gene. This is a standard approach in the field; however, recent work has shown that endosymbionts like the aphid primary endosymbiont, Buchnera, are variably polyploid [1]; further the aphid cells that house the symbionts are also highly polyploid and variable in their ploidy [2]. It is important to understand that what is being measured when using qPCR is DNA copy number and not quantification of the number of symbiont cells. Alternative approaches to measuring symbiont density include flow cytometry [3], and SymbiQuant [4], a machine vision tool that can quantitatively characterize symbiont populations from DAPI-stained confocal images. These alternate approaches also have their dlimitations. Currently, there is no perfect approach to measuring symbiont density, which remains an important measure in experiments such as these. Put simply, it is important for a reader to be aware of the limitations of each approach and interpret data accordingly.

(1) Komaki, K., and H. Ishikawa. 2000. Genomic copy number of intracellular bacterial symbionts of aphids varies in response to developmental stage and morph of their host. Insect Biochemistry and Molecular Biology 30:253-258.

(2) Nozaki, T., and S. Shigenobu. 2022. Ploidy dynamics in aphid host cells harboring bacterial symbionts. Scientific Reports 12:9111.

(3) Simonet, P., G. Duport, K. Gaget, M. Weiss-Gayet, S. Colella, G. Febvay, H. Charles, J. Viñuelas, A. Heddi, and F. Calevro. 2016. Direct flow cytometry measurements reveal a fine-tuning of symbiotic cell dynamics according to the host developmental needs in aphid symbiosis. Scientific Reports 6:19967.

(4) James, E. B., X. Pan, O. Schwartz, and A. C. C. Wilson. 2022. SymbiQuant: A machine learning object detection tool for polyploid independent estimates of endosymbiont population size. Frontiers in Microbiology 13:816608.

We agree that qPCR-based measurements of endosymbiont gene copy number have limitations even if they are the standard approach used in most studies. In the current set of experiments, qPCR provided a practical and efficient approach for assessing variation in endosymbiont abundance and infection status among samples and the only one feasible given the number of monitoring events and samples required. Nevertheless, we acknowledge the limitations of this approach (and have pointed this out ourselves in a recent COIS paper – Hoffmann et al 2026). We now mention this under further work and provide a couple of references (see Discussion).

Reference:

Hoffmann, A. A., Yang, Q. and P. A. Ross. Aphid endosymbionts revisited: molecular detection, diversity, and population dynamics. Curr Op Insect Sci (in press). (2026)

Impact and Significance:

Food security and production, and pest control are major challenges facing the human population. This work contributes knowledge that will benefit the development of alternate pest control strategies in agriculture.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) Overall, I found the study interesting and worthwhile, particularly because it shows that novel symbiont associations can generate contrasting phenotypes in an important pest species. My main suggestion would be to sharpen the framing of the paper and to bring the mechanistic and applied discussion into slightly closer alignment with the current evidence base. With those points addressed, I think the manuscript would read as a clearer and more balanced contribution.

We have rephrased the Discussion around the mechanistic component of the work to sharpen this and link more directly to evidence. For instance:

“Despite this, our metabolomic analyses suggest that endosymbionts in D. noxia may influence some other aspects of wheat metabolism in a spatially structured way. Within aphid-feeding areas, wheat exposed to Rickettsiella aphids showed increased valine and decreased 3-phenyllactic acid. Changes in valine have been reported in plants responding to herbivory and other forms of stress (43-45), while 3‑phenyllactic acid has been associated with antimicrobial and defense-related activity (46). In non-feeding areas, wheat exposed to Regiella aphids showed reduced urea and increased pantothenic acid. These changes may reflect differences in nitrogen metabolism and allocation (47), and in metabolic processes involving pantothenic acid (48) respectively. However, the present metabolomic data do not establish the functional consequences or causal mechanisms underlying these changes. They indicate that aphids carrying different endosymbionts are associated with some distinct metabolic responses in wheat, including responses that differ between aphid-feeding and non-feeding areas. Our findings are consistent with previous work showing that phloem‑feeding insects can induce changes in plant metabolites in response to herbivory (49, 50) and provide a basis for future studies to determine how endosymbionts influence aphid-induced plant responses and contribute to contrasting plant phenotypes.”

We have not undertaken a complete reframing of the paper but further emphasized the focus on phenotypic contrasts in a few places including incorporating some changes to the comments below.

(2) Lines 130-135: Please clarify more explicitly whether the main aim of the paper is to test a specific biological hypothesis about endosymbiont-mediated aphid-plant interactions or to provide a broader proof-of-principle survey of symbiont-associated phenotypes. As it stands, the framing moves between multitrophic biology and pest-management relevance, which makes the central conceptual contribution harder to identify.

We have rephrased this sentence as “By integrating these factors, we investigate how endosymbiont infection influences aphid fitness and aphid–plant interactions, providing insights into the ecological consequences of novel microbial associations and their potential relevance to sustainable pest management.”

(3) Line 205: For the metabolomic analysis, please consider adding a formal multivariate test for strain effects, especially for the comparisons shown in Figure 2C and 2D, or otherwise interpret the PCA more cautiously as descriptive rather than inferential.

We have emphasized the descriptive component and rephrased this sentence as “However, within either area, there was no clear separation among aphid strains (Figures 2C & 2D), suggesting broadly similar metabolomic profiles among strains of the same aphid clone carrying different symbionts.”

(4) Please clarify how the top and bottom feeding leaves were handled analytically in the analyses, and explain the rationale for collapsing them into a single "feeding area" category. If possible, it would be helpful to show whether leaf position itself influenced the plant-response patterns.

We combined the upper and lower leaves together to provide a representative measure of the plant-level responses, rather than focusing on responses at a particular leaf position. This approach was consistent with the main objective of our study, which was to investigate whole plant responses to aphids hosting different endosymbionts, rather than differences in responses among different plant parts. In addition, combining the two portions provided sufficient plant material for the GC-MS analysis and helped ensure reliable metabolite measurements from the same material. Because the two leaf positions were combined prior to GC-MS analysis, we were unable to separately test the effect of leaf position on the metabolomic response in this dataset. We have clarified this point in the revised manuscript in Materials and methods section (“Plant defense responses”).

(5) Line 228: The use of 19{degree sign}C and 25{degree sign}C is not unusual in aphid work, but it would still help the reader if the manuscript stated more explicitly why these two temperatures were chosen in this study.

We selected 19°C and 25°C because they represent contrasting temperature conditions within the range suitable for Russian wheat aphid development, allowing us to assess whether temperature influences Rickettsiella transmission and population dynamics. In particular, our previous observations indicated differences in the rate of Rickettsiella spread between these temperature conditions (Gu et al., 2023).

Reference:

Gu et al., A rapidly spreading deleterious aphid endosymbiont that uses horizontal as well as vertical transmission. Proc Natl Acad Sci USA 120, e2217278120 (2023).

(6) Lines 390-392: It would help to discuss more explicitly how the relatively modest effects in the individual life-history assays relate to the clearer signals seen at the whole-plant and population level.

In our experiments, we assessed aphid fitness under different environmental conditions. In the individual fitness assays conducted on cups with a single plant (Figures S5 & S6), aphids were maintained under relatively favourable conditions, with limited environmental stress and without substantial crowding. Under these conditions, we observed an increase in fitness associated with endosymbiont infection. In contrast, we also examined aphid performance at the population level (Figures 3 & 4), where populations were established from a small number of aphids and subsequently experienced increasing crowding and density-dependent stress. Under these conditions, the effects of endosymbiont infection differed from those observed in the individual assays, with Rickettsiella-infected aphids showing greater population growth and Regiella-infected aphids showing reduced population growth.

These results suggest that the effects of endosymbionts on aphid fitness are context-dependent and may become more pronounced as population density increases and density-dependent stress develops. Thus, relatively modest effects observed at the individual level where experiments are often undertaken may not translate to differences at the population level, and plant level effects may subsequently influence feeding pressure and plant damage. We have added this perspective in the Results and Discussion sections.

(7) Line 678 & 688: In both whole-plant experiments, please explain how 3 and 4 replicate plants were selected.

The replicate plants were randomly selected from the available plants for each treatment to minimize potential selection bias. We have clarified this procedure in the revised manuscript in Materials and methods section.

(8) Lines 686-690 / Figure 4: In the Regiella whole-plant experiment, the Methods state that 16 plants were established per treatment and that 4 plants per treatment were removed at each time point (days 4, 8, 12, and 16). However, in Figure 4B-D, day 12 appears to include 5 data points. Please clarify this apparent mismatch between the described sampling scheme and the data shown in the figure.

We thank the reviewer for pointing out this and we have corrected this mistake. We initially established 16 plants for the wild type and 17 plants for the Regiella treatment. Four plants per treatment were originally planned to be sampled at each time point (Days 4, 8, 12, and 16). However, because Day 12 was a key time point at which an obvious difference in plant damage was observed between the treatments, we selected one additional plant each treatment for measurement at Day 12, resulting in five data points for this treatment at that time point. The remaining plant was therefore measured at Day 16. We have clarified the sampling procedure in the revised Materials and methods section and figure legend.

(9) Figure 2A and Figure 4A: These schematics are helpful overall, but the brown supporting sticks stand out quite strongly and may make the panels a little harder to interpret at first glance. I wonder whether they could be simplified, made less prominent, or replaced with photographs of the actual setup if those are available.

We have revised Figures 2A and 4A to simplify the supporting structures and reduce their visual prominence.

Reviewer #2 (Recommendations for the authors):

Some of the statistics were not entirely clear to me, particularly the tests reported in the results which differ from what is described in the figure legends:

(1) Lines 306-308: "Total nymph numbers were higher on Rickettsiella aphids from Day 21 to Day 25" and indicates that this is based on GLM testing, but the figure does not indicate statistical significance, and the figure legend states independent sample t-tests were used. Similar comment for the following paragraph and corresponding figure.

The GLMs were used to test the overall patterns in nymph numbers across the relevant time periods, including Days 21–25, rather than testing each time point independently. We also conducted independent-sample t-tests to assess differences between treatments at individual time points. We have clarified this distinction in the Statistical section.

(2) Line 43: Does not seem like the appropriate reference (reference is on plant virus transmission, not salivary toxins).

We thank the reviewer for pointing this out. We have removed this reference and replaced it with reference 34 (Luna et al., 2018) that directly supports the statement regarding aphid salivary toxins.

Reference:

Luna et al., Bacteria associated with Russian wheat aphid (Diuraphis noxia) enhance aphid virulence to wheat. Phytobiomes J 2, 151-164 (2018).

Reviewer #3 (Recommendations for the authors):

Minor editorial comments:

(1) Figure S10 - the figure legend needs improvement as the current version does not help the reader understand the figure. Please also include a key.

We have changed the figure legend with reference to our aim, and also explained use of the Cp values. “Figure S10. Rickettsiella Cp values in (A) routine screening of laboratory Rickettsiella colonies and (B) the mixed cage experiment assessing endosymbiont frequency changes over time at 19 °C and 25 °C. The dark red area represents overlap between the 19°C and 25°C experiments. Cp values represent the quantification cycle values obtained from qPCR, with lower Cp values indicating a higher amount of Rickettsiella target DNA. This figure shows the typical range of Cp values observed in our laboratory Rickettsiella -infected aphid colonies. We used this range as a reference for identifying aphids that acquired Rickettsiella through horizontal transmission, as horizontally infected aphids generally showed much higher Cp values than vertically infected aphids.”

(2) Define Cp.

We have explained it as “Cp values represent the quantification cycle values obtained from qPCR, with lower Cp values indicating a higher amount of Rickettsiella target DNA.”

(3) Supplemental Information: Line 113 - T is missing from Table.

This has been added.

(4) Move Table S2 to the main paper - this table provides a useful summary of the work.

This has been moved.

Main Manuscript:

(1) Line 145: Serratia was not detected at G0 - was it detected later? It seems possible that titer could be very low to begin and increase in later generations; please clarify.

We have previously monitored the aphid populations for the presence of Serratia transinfected from the same donor resource across subsequent generations, and Serratia was not detected at any later generation. We also did not detect Serratia in the other aphid species we examined, including green peach aphids (Gu et al., 2023 & 2025) and oat aphids (Yang et al., 2026). Therefore, we believe that the absence of Serratia at G0 was not due to a very low initial titer followed by an increase in later generations but instead that Serratia had been lost from the aphid population.

References:

Gu et al., A rapidly spreading deleterious aphid endosymbiont that uses horizontal as well as vertical transmission. Proc Natl Acad Sci USA 120, e2217278120 (2023).

Gu et al., Transinfections of the endosymbiont Rickettsiella viridis in different Myzus persicae (Hemiptera: Aphididae) clones show consistent deleterious effects and stable transmission. J Econ Entomol 118, 1544-1552 (2025).

Yang et al., A Rickettsiella transinfection in Rhopalosiphum padi reduces fitness and alate production but not plant virus transmission. Pest Man Sci 82, 3894-3906 (2026).

(2) Line 206: "different aphid strain" - I learned from the manuscript that a single clone of D. noxia is found in Australia. Further, from my reading of the manuscript, I understand that one clonal isolate was propagated and then infected with symbionts. I think it is important to reword this sentence so that it is clear that the aphid genetic background is held constant, and that the only differences here are the presence or absence of the different symbionts. My reaction to this sentence was that you are working with the same aphid strain hosting different symbionts.

We have clarified it by adding “the same aphid clone carrying different symbionts” after the different aphid strains.

(3) Measuring symbiont "density" is a tricky thing to do; I explain this above in the public review. I suggest considering some revisions to the manuscript to be sure that you accurately reflect what has been measured and what can reasonably be inferred from using qPCR to measure gene copy number.

We agree that qPCR-based measurements of symbiont gene copy number have limitations. In this experiment, we had a relatively large number of samples, and qPCR provided a practical and efficient approach for assessing variation in endosymbiont abundance and infection status among samples. While we acknowledge the limitations of this approach, the relative differences in gene copy number can still provide an indication of variation in endosymbiont abundance and infection status among treatments. Unfortunately, other approaches remain challenging given resource and expertise limitations.

(4) I think that you may be undervaluing the results of the mixed infection experiments; I find them to be compelling. To me, the data suggest that the symbionts increase aphid fitness.

In our experiments, we assessed aphid fitness under different environmental conditions. In the individual fitness assays conducted on cups with a single wheat plant (Figures S5 & S6), aphids were maintained under relatively favourable conditions, with limited environmental stress and without substantial crowding. Under these conditions, we observed an increase in fitness associated with symbiont infection. However, we also examined aphid performance under population-level conditions, where populations were established from a small number of aphids and subsequently experienced increasing crowding and density-dependent stress (Figures 3 & 4). Under these conditions, the effects on fitness were different from those observed in the individual assays. We therefore agree that our results suggest that symbionts can increase aphid fitness under some conditions, but that this effect may be context-dependent and can differ under population-level conditions where density-dependent stress occurs. We have also added this information to our Results section to make this clear to readers.

(5) Lines 288-291: This sentence doesn’t make sense to me. What "minor fitness costs" are being referred to? If the infected lines are increasing in representation relative to the uninfected lines, that suggests that there are not fitness costs, but fitness advantages under the experimental conditions.

We have rephrased it to “minor fitness effects” which we refer to the fitness test under favourable conditions.

(6) The section that begins on line 293 - I find this part to not be particularly robust and suggest dropping it from the paper.

We appreciate the reviewer’s concern regarding the robustness of this section. We included this experiment to monitor changes in aphid population over time and to help explain the differences in plant feeding damage observed between aphids carrying different endosymbionts. Importantly, we conducted this experiment using whole wheat plants to evaluate whether the patterns observed in our other experiments were also evident. We believe that these results provide important complementary evidence for interpreting the differences in plant damage among the aphids hosting different endosymbionts and therefore are relevant to the overall conclusions of the study. For this reason, we prefer to retain this section in the manuscript.

(7) Line 298: three plants per time point - I do not think this sample size is reflected in the methods of the paper.

We have mentioned in the method part with “At day 14, three replicate plants were randomly selected from the available plants for both treatments and we counted the total number of nymphs, alate adults, and apterous adults. This was repeated again at Days 21 and 25”.

(8) Line 304: "the frequency of alates decreased as plant damage increased" - this seems to be counterintuitive!

As plant damage increased, the total aphid population also increased, resulting in an increase in the absolute number of alates. However, the frequency (proportion) of alates decreased because the increase in the total aphid population was greater than the increase in the number of alates.

(9) Line 404: "horizontal transmission through plant tissue and/or transfer via aphid contact or honeydew" - what evidence is there that this happens? I have not kept on top of the literature with respect to transmission of secondary symbionts in aphids, but back when I was very familiar with that literature, the data did not support transmission by any of those routes. If there is now evidence supporting transmission by these routes, please cite it here.

Previous studies have provided experimental evidence that horizontal transmission of aphid-associated endosymbionts can occur through plants. For example, plant-mediated transmission has been demonstrated for direct detection of secondary endosymbiont in the plant tissue including Hamiltonella defensa (Li et al., 2018), Rickettsia (Shi et al., 2024) and Serratia symbiotica (Pons, et al., 2019a). Our previous research also demonstrates that Rickettsiella endosymbionts were detected in uninfected aphids after feeding by infected aphids regardless of physical contact (Gu et al., 2023). Endosymbionts have also been detected in aphid honeydew (Darby and Douglas, 2003) and some primary transmission route appears to be horizontal, through honeydew (faeces) and host plant phloem (Pons, et al., 2019a & 2019b; Perreau et al., 2021). Appropriate references have been added to the revised manuscript in the Discussion section.

References:

Li et al., Plant-mediated horizontal transmission of Hamiltonella defensa in the wheat aphid Sitobion miscanthi. J Agric Food Chem 66, 13367-13377 (2018).

Shi et al., Rickettsia transmission from whitefly to plants benefits herbivore insects but is detrimental to fungal and viral pathogens. mBio 15, e02448-23 (2024).

Pons et al., Circulation of the cultivable symbiont Serratia symbiotica in aphids is mediated by plants. Front Microbiol 10, 764 (2019a).

Darby and Douglas, Elucidation of the transmission patterns of an insect-borne bacterium. Appl Environ Microbiol 69, 4403-4407 (2003).

Pons et al., New insights into the nature of symbiotic associations in aphids: infection process, biological effects, and transmission mode of cultivable Serratia symbiotica bacteria. Appl Environ Microbiol 85, e02445-18 (2019b).

Perreau et al., Vertical transmission at the pathogen-symbiont interface: Serratia symbiotica and aphids. mBio 12, e00359-21 (2021).

(10) Line 511: revise to "to measure their relative densities relative to a host gene".

We have revised it.

(11) Throughout the manuscript, please replace "five aged-matched" with an accurate description of the aphids used in the experiment. Please pay particular attention to the figure legends. Simply state e.g. "five 10-day-old apterous females" etc.

This has been replicated in the main manuscript and figure legends.

(9) Line 727 - lowercase t for Tests.

This has been added.

(10) Line 738 - what happens when you don’t exclude the early time points? Do your significant results go away? Also, please define what is meant by "early time points".

When the early time points (Day 14 for Rickettsiella and Day 4 for Regiella) were included in the analysis, the GLM still showed a significant effect of strain on alate production for Rickettsiella (F_1,12 = 26.434, P < 0.001). We excluded these early time points from the analysis presented in the manuscript because, at these stages, aphid population sizes were still similar between treatments. We also conducted independent-sample t-tests at individual time points and observed differences at the later time points, when aphid population sizes began to diverge. We therefore considered the later time points to be more informative for assessing fitness effects and population sizes under increasing crowding conditions. We have now clarified this as “The earliest time points in the experiments for Rickettsiella (Day 14) and Regiella (Day 4) were excluded” in the manuscript.

(11) In the legends of all figures, please be explicit about sample sizes.

We have added the relevant information about replicate number or sample sizes in the main and supplementary figures.

(12) Line 1010 - replace "each leave" with "each leaf" - there was at least one other place, I think in the supplemental information, that leave was used instead of "leaf".

We replaced this.

eLife Assessment

This valuable study provides a systematically curated atlas of non-canonical open reading frames translated across normal human and mouse tissues by uniformly integrating nearly 400 ribosome-profiling datasets with independent mass-spectrometry evidence for ncORF-encoded peptides. The convincing analyses connect ncORF evolutionary age and coding constraint with translation level, tissue distribution, and co-translation with canonical coding sequences, offering a broad comparative view of how non-canonical translation changes over mammalian evolution. Although the functions of most ncORF-encoded peptides remain unknown, the scale of their detection across tissues, together with their proteomic and evolutionary signatures, suggests that a substantial subset may have biological functions.

Reviewer #1 (Public review):

[Editors' note: This revised version has been assessed by the Reviewing Editor without further input from the original reviewers. The authors have satisfactorily addressed the substantive comments raised in the previous round of review. The qualifications and limitations are now more clearly acknowledged in the revised manuscript.]

Summary:

This work compiles a comprehensive atlas of ncORFs across mammalian tissues and cell types, derived from reanalysis of ~400 public ribosome profiling datasets. The authors then evaluate cross-species conservation and functional signatures, proposing that evolutionarily ancient ncORFs tend to have higher translation potential, stronger expression, and closer relationships with canonical coding sequences.

Strengths:

In general, the study provides a large-scale and timely resource of annotated ncORFs, which could be broadly useful for the community. The authors collected ~400 public ribosome profiling datasets for annotations of ncORFs, which, to my best knowledge, is the largest collection of data for such purpose. The catalog could facilitate future investigations into ncORF biology and broaden understanding of the coding potential of the "non-coding" genome.

Comments on previous version:

The authors have made efforts to address most of the previous concerns, and several points have been clarified or improved in the revision. However, in a number of cases, the responses rely more on acknowledgment and reframing rather than substantive analytical strengthening. Overall, the manuscript is improved, particularly in terms of clarity, transparency, and positioning of claims. I support its publication and look forward to seeing how the field engages with and discusses these claims.

Reviewer #2 (Public review):

Summary:

Chang et al. attempted to analyze a large number of ribo-seq datasets through a standardized pipeline, identifying novel non-canonical ORFs and elucidating their evolutionary and expression characteristics.

Strengths:

(1) The datasets analyzed by the authors are sufficiently comprehensive, and the use of standardized pipelines ensures excellent analytical consistency.

(2) Their analyses of ORF evolution and co-expression further deepen our understanding of these ORFs.

Weaknesses:

(1) The authors primarily conducted analyses through bioinformatics, lacking sufficient wet-lab experimental evidence.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

This work compiles a comprehensive atlas of ncORFs across mammalian tissues and cell types, derived from reanalysis of ~400 public ribosome profiling datasets. The authors then evaluate cross-species conservation and functional signatures, proposing that evolutionarily ancient ncORFs tend to have higher translation potential, stronger expression, and closer relationships with canonical coding sequences.

Strengths:

In general, the study provides a large-scale and timely resource of annotated ncORFs, which could be broadly useful for the community. The authors collected ~400 public ribosome profiling datasets for annotations of ncORFs, which, to my best knowledge, is the largest collection of data for such purpose. The catalog could facilitate future investigations into ncORF biology and broaden understanding of the coding potential of the "non-coding" genome.

Weaknesses:

Based on the ncORF catalog, some of the analyses were not properly done. Some of the results are descriptive.

(1) Bias and representations of data source. Public ribo-seq datasets are unevenly distributed across tissues and cell lines, raising concerns about heterogeneity and underrepresentation of certain contexts. This may limit the generalizability of the catalog.

(2) The discussion on modular domains of ncORFs is unclear, and the claim that they may originate via TErelated mechanisms is not well supported. Stronger evidence or clearer reasoning is needed.

(3) The conservation comparisons are not fully convincing. Figure S7 shows only mild differences between ncORFs and CDS, and statistical significance is not clearly demonstrated. Comparisons with other noncoding RNAs should be added, and overlapping sequences between ncORFs and CDS should be excluded to avoid bias.

(4) Figure 3 indicates that some ncORFs are subject to evolutionary constraints. This is not surprising. The authors should provide further analyses on more detailed features of these "conserved" ncORFs vs. the "non-conserved" ones. Some pretty informative works have been done in drosophila, worms, mouse, and human. Figure 3 suggests some ncORFs are under evolutionary constraint, but this is not unexpected. More granular analyses contrasting "conserved" versus "non-conserved" ncORFs would be informative. In fact, small ORFs, especially uORFs, have been extensively studied, for their functions and corss-species conservations. The authors should explicitly show what is new here in their analyses.

(5) Translation levels are reported using RPF counts. However, translation efficiency (normalized by RNA expression) is a more appropriate measure to account for expression heterogeneity.

(6) The correlation analyses between ncORF translation levels and PhyloCSF are confusing and largely descriptive. These sections need sharper framing and clearer conclusions.

(7) Public ribo-seq datasets, generated by different research labs, are known for their strong batch effects. Representations of tissues and cells are also very unbalanced. Therefore, the co-translation analysis between ncORFs and canonical CDS is not well controlled. This should be done by referring to a recent large-scale ribo-seq meta-analysis (Nat Biotechnol. 2025. doi: 10.1038/s41587-025-02718-5).

Comments on revisions:

The authors have made efforts to address most of the previous concerns, and several points have been clarified or improved in the revision. However, in a number of cases, the responses rely more on acknowledgment and reframing rather than substantive analytical strengthening. Overall, the manuscript is improved, particularly in terms of clarity, transparency, and positioning of claims. I support its publication and look forward to seeing how the field engages with and discusses these claims.

We thank Reviewer #1 for the constructive comments and recognition of the value of our ncORF atlas. We have addressed the key concerns by strengthening the analyses and clarifying the framing and limitations of our conclusions. We appreciate the reviewer’s support for publication and believe these revisions have further improved the manuscript.

Reviewer #2 (Public review):

Summary:

Chang et al. attempted to analyze a large number of ribo-seq datasets through a standardized pipeline, identifying novel non-canonical ORFs and elucidating their evolutionary and expression characteristics.

Strengths:

(1) The datasets analyzed by the authors are sufficiently comprehensive, and the use of standardized pipelines ensures excellent analytical consistency.

(2) Their analyses of ORF evolution and co-expression further deepen our understanding of these ORFs.

Weaknesses:

(1) The authors primarily conducted analyses through bioinformatics, lacking sufficient wet-lab experimental evidence.

(2) Some analytical methods and standards were not clearly presented in the manuscript.

We thank Reviewer #2 for the positive assessment of our comprehensive dataset and standardized analytical framework. We have clarified the analytical methods and criteria throughout the manuscript and better defined the scope and limitations of our bioinformatics-based analyses. We appreciate the reviewer’s constructive suggestions, which have helped improve the clarity and rigor of the manuscript.

Recommendations for the authors:

Reviewing Editor:

We have evaluated the revision together with the reviewers' second-round assessments and your responses. The reviewers agree that the manuscript has improved in clarity and that the standardized integration of large-scale Ribo-seq datasets provides a valuable resource for the field. However, several important concerns remain insufficiently resolved. In multiple cases, the revision relies primarily on acknowledgment or reframing of limitations rather than additional analyses or clearer methodological justification, leaving the evidential support for several conclusions incomplete.

Because the study is entirely computational, all analytical procedures, criteria, and thresholds should be explicitly defined and adequately justified to meet the expected standard of technical rigor. In particular, key components of the analytical framework require clearer description, including the definitions and criteria used for co-translation and ncORF classification. The limitations of the dataset should also be discussed more explicitly, especially regarding the heterogeneity of public Ribo-seq datasets, technical factors influencing detection sensitivity, and the interpretation of variable detection frequencies across samples.

In addition, several conclusions remain largely descriptive, and the distinction between novel findings and confirmation of previous observations should be clarified more carefully. Conclusions should be framed strictly within the limits of the presented data and positioned appropriately relative to prior work, with suitable citation to avoid overstating novelty.

We therefore ask the authors to refine the technical descriptions, ensure that all methods and analytical criteria are presented unambiguously, and expand the Discussion to clearly articulate the limitations of the dataset and analysis. The conclusions should also be revised to reflect an appropriately cautious interpretation of the findings.

The primary strength of this study lies in the scale and standardization of the dataset as a community resource. Given this substantial resource value, we believe the manuscript could become suitable for publication provided that the issues outlined above are addressed clearly and transparently. With these revisions, the work will provide a useful foundation for future studies in this area.

We therefore invite you to submit a final revised version addressing the points described above.

We thank the Editor for the careful assessment and constructive guidance. In the final revision, we have clarified all key methodological definitions and analytical criteria, expanded the Discussion of dataset and detection limitations, and revised the conclusions to avoid overstatement. We believe these changes improve the technical rigor, transparency, and overall value of the manuscript as a community resource.

Reviewer #1 (Recommendations for the authors):

The authors have made efforts to address most of the previous concerns, and several points have been clarified or improved in the revision. However, in a number of cases, the responses rely more on acknowledgment and reframing rather than substantive analytical strengthening. Overall, the manuscript is improved, particularly in terms of clarity, transparency, and positioning of claims. I support its publication and look forward to seeing how the field engages with and discusses these claims.

We appreciate the reviewer’s support for publication.

Reviewer #2 (Recommendations for the authors):

While the authors have made commendable efforts to revise the manuscript and address previous concerns, the revised version still falls short of fully resolving several critical issues regarding data interpretation and methodological transparency. I recommend the following modifications before the manuscript can be considered for publication:

(1) Although the authors have annotated the detection frequencies of individual sORFs in the revised

Supplementary Table 3 and Fig. S1B, the biological and technical implications of these data require further clarification:

(a) As the data demonstrates, even the most abundant sORFs were detected in no more than half of the samples. If the authors attribute this low detection rate to technical limitations (e.g., batch effects, sequencing depth, or threshold stringency), this must be explicitly discussed and annotated in the main text to prevent readers from misinterpreting this as low biological penetrance.

We thank the reviewer for this constructive comment. We have added a paragraph to the Discussion explicitly addressing the potential technical factors underlying the variable detection frequencies to avoid overinterpreting these frequencies as biological penetrance.

(b) The authors did not fully address my previous query regarding tissue specificity. Given the diverse and complex origins of the analyzed ribo-seq datasets, it is crucial to know whether any of these sORFs are tissue-specifically translated. The authors should analyze and state whether certain sORFs are exclusively detected in specific sample categories (tissues/organs), and whether this translation pattern aligns with the tissue-specific expression of their corresponding host transcripts.

We thank the reviewer for raising this important point. Strict tissue-exclusive translation is difficult to establish from heterogeneous public Ribo-seq datasets, as gene expression is inherently stochastic and most genes have some probability of being expressed across tissues, although expression levels may vary substantially between tissues. Moreover, failure to detect an ncORF in a given tissue may reflect low expression or insufficient sequencing depth rather than true biological absence. We therefore avoid making definitive claims about tissue-specific translation and instead quantify variation in ncORF expression across tissues using a tissue specificity index.

(2) Echoing the concerns raised by Reviewer #1, I remain concerned that the observed uORF-CDS cotranslation might be a computational artifact or false positive. The current Methods section lacks sufficient detail on how "co-translation" was strictly defined and quantified. I strongly recommend that the authors include a schematic diagram (e.g., in Figure 6 or supplementary figures) that explicitly details their analytical strategy, statistical thresholds, and evaluation criteria for defining co-translation. As was pointed out, it is well-established that uORFs typically exert an inhibitory effect on the translation of the main CDS. To validate the accuracy and robustness of their analytical pipeline, the authors should use their collected dataset to demonstrate the prevalence and nature of this canonical inhibitory phenomenon. Successfully capturing this expected repression would serve as a crucial positive control for their methodology. While the authors provided a theoretically acceptable mechanistic model in the text to reconcile co-translation with uORF-mediated repression, this hypothesis currently lacks literature support. The authors must cite relevant prior studies that support this specific regulatory dynamic to strengthen their argument.

We thank the reviewer for this important comment. We have further clarified the definition, detection criteria, and statistical framework for co-translation in the Methods, and have made the complete analysis code publicly available to facilitate reproducibility and independent evaluation. We have also added relevant literature supporting the proposed regulatory interpretation clarifying the relationship between our observations and the established inhibitory effects of uORFs.

eLife Assessment

This study presents valuable findings regarding cardiac and autonomic effects of seizures and epilepsy, with relevance to sudden unexpected death in epilepsy (SUDEP). They present solid evidence that genetic deletion of the potassium-chloride co-transporter in hypothalamic corticotropin-releasing hormone (CRH) neurons exacerbates bradycardia and enhances autonomic disturbances in a mouse model of temporal lobe epilepsy. This work will be of interest to neuroscientists working on epilepsy, the HPA axis, and autonomic control.

Reviewer #1 (Public review):

Summary:

The manuscript entitled "Autonomic reflex plasticity associates with time-dependent SUDEP susceptibility in a murine model with hyperactive stress circuits" by Dr. Saunders and colleagues combined a traditional mouse model of SUDEP, ventral intrahippocampal kainite (vIHKA) injection, with a genetic model of chronic hyperactivity of central corticotropin-releasing hormone (CRH) neurons (Kcc2/Crh) that further increases the risk of SUDEP in the weeks following seizure.

Strengths:

Their results show during spontaneous seizures Kcc2/Crh mice had more pronounced reflex-like ictal bradycardias compared to WT controls that notably occurred prior (~10 sec) to seizure termination and had greater autonomic disturbances compared to WT controls, including a pronounced serotonin-mediated Bezold Jarisch reflex. These results show chronic hyperactivity of central corticotropin-releasing hormone (CRH) neurons (Kcc2/Crh) increased autonomic disturbances and risk of SUDEP in a kainic acid model of epilepsy.

Weaknesses:

This study could be improved with a more thorough assessment of heart rate, blood pressure and breathing during and following the seizures, and in particular the fatal event. It is unclear if the bradycardias were spontaneous, or a result of preceding central or obstructive apneas, oxygen desaturations, hypercapnia, arrhythmias, or other possible triggers.

Considerable prior work in the literature suggests SUDEP could be mediated, in some patients, by a burst of parasympathetic activity to the heart. Were the heart rate changes in these animals during seizures inhibited or blocked by atropine, or atenolol? The injection of the 5HT agonist phenylbiguanide into the right jugular is not a selective approach for activating the Bezold Jarisch Reflex (BJR) which is caused by increased activity of intracardiac sensory neurons (generally activated with ischemia or a combination of low preload with high contractility). The results should be interpreted more cautiously, as a response to systemic administration of phenylbiguanide only.

Reviewer #2 (Public review):

Summary:

In this manuscript, the authors set out to evaluate the role of hypothalamic pituitary axis hyperactivity on cardiac and autonomic changes during epileptogenesis and following seizures in a mouse model of temporal lobe epilepsy. Epilepsy is very common. It can frequently result in death from sudden unexpected death in epilepsy, or SUDEP. SUDEP is thought to be at least in part due to seizure related cardiac and autonomic instability. Increased stress states are well known to be comorbid with epilepsy. This comorbidity is thought to increase the risk of SUDEP. Here the authors hypothesized that a mouse model of heightened stress in which there is hyperactivity of the CRH neurons in the hypothalamus would demonstrate exaggerated cardiac and autonomic effects of seizures and epilepsy.

Strengths:

For the chronic stress model, they employed the Kcc2/Crh mice that have a genetic deletion of the potassium chloride cotransporter in CRH neurons. They treated these mice and their wild type littermates with intra hippocampal kainic acid or saline, as epileptic and sham-treated animals respectively. The assessed cardiac activity, blood pressure, baroreflex, and the Bezold-Jerisch reflex during epileptogenesis. This in general is an interesting study. They make some interesting and potentially important observations regarding heart rate and blood pressure in seizures and epilepsy.

Weaknesses:

While the revised manuscript is much improved, there are still some concerns that should be addressed.

(1) The low-pressure baroreceptor responses they show in Figure 4 are somewhat confusing. Should they not be seeing a reflex increase in heart rate when blood pressure is lowered with sodium nitroprusside? It would be helpful if they could describe whether the control responses were as expected or not, and if not, why? This makes it difficult to assess changes seen in the different genotypes and conditions.

(2) It does not seem appropriate to label the assessments associated with Figure 5 as the Bezold Jarisch Reflex. This reflex involves bradycardia, hypotension, vasoconstriction, and hypopnea. They seem to be only looking at the cardiac component, which is likely mediated though peripheral 5HT3 receptors. Did they measure blood pressure and breathing? Can they include these? If they can only comment on HR, then the discussion should reflect this.

(3) In Figure 1B, it would be helpful to show some short (e.g., 0.5 sec) snippets of ECG traces that exemplify the changes in HR (spikes/second).

(4) The day 21 examples given in Figure 1B, do not seem to be representative of the data depicted in Figure 1C.

(5) From the top panel examples in Figure 2A it looks like there might be greater EEG suppression following seizures in the Kcc2/CRH mice. Was this consistent? It might be worth looking into.

(6) Can the authors include scale bars for the top panels in Figure 2A?

Author response:

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

eLife Assessment

This study presents valuable findings regarding cardiac and autonomic effects of seizures and epilepsy, with relevance to sudden unexpected death in epilepsy (SUDEP). They present solid evidence that genetic deletion of the potassium-chloride cotransporter in hypothalamic corticotropin-releasing hormone (CRH) neurons exacerbates bradycardia and enhances autonomic disturbances in a mouse model of temporal lobe epilepsy. However, the evidence that this deletion produces chronic hyperexcitability of the hypothalamic-pituitary-adrenal axis was incomplete, leaving a mechanistic gap. This work will be of interest to neuroscientists working on epilepsy, the HPA axis, and autonomic control.

We thank the editors and reviewers for their feedback. Although the loss of Kcc2 from CRH neurons in Kcc2/Crh mice has been confirmed (Melon et al., 2018) and leads to HPA axis hyperexcitability in response to stress or seizures, it does not chronically drive HPA axis hyperactivity in unstressed conditions (Basu et al., 2024).

The following details have been added regarding the Kcc2/Crh model. We now describe the Kcc2/Crh as “hyperreactive” rather than “hyperexcitable/hyperactive” throughout the manuscript.

-In the Introduction: “This loss of Kcc2 in CRH neurons has been previously confirmed and shown to cause an exaggerated HPA axis response to stress that is absent in baseline conditions (Basu et al., 2024; Melon et al., 2018)”

-In the Discussion: “This aligns well with lack of elevated plasma corticosterone at baseline in Kcc2/Crh mice, compared to WT, because elevated PVN^CRH neuron activity should otherwise increase this signal (Basu et al., 2024).”

-In the Discussion: “Most notable, our model utilizes a developmental strategy to knock out Kcc2 from CRH neurons, which has been confirmed previously (Melon et al., 2018).”

Public Reviews:

Reviewer #1 (Public review):

This study could be improved with a more thorough assessment of heart rate, blood pressure and breathing during and following the seizures, and in particular the fatal event.

Post-ictal HR data are now included in the Results, Table 2.1 and Figure 2. Overall, pronounced bradycardia that occurred near seizure termination was followed by recovery of HR to pre-ictal baseline in the early post-ictal period (30 sec). In Results: “Independent of genotype, HR recovered to baseline levels during the immediate post-ictal period (0-10 sec, Fig. 2G; 10-30 sec, Fig. 2K).

In pilot work, we determined that HR during spontaneous seizures were fundamentally different than HR during status epilepticus (see Author response image 1). Therefore, it was critical for us to examine HR during spontaneous seizures. We previously published that Kcc2/Crh+KA mice have a rate of 1-2 seizures per day. To limit additional stressors and seizure provocation, we employed radio telemetry (over tethered systems) and opted out of carotid instrumentation for BP as well as restricted environments of plethysmography chambers for these assessments of HR. After determining that heart rate was different between our mouse lines, we tested whether this change was mediated by central circuits regulating HR (ie: baroreflex, Bezold-Jarisch reflex) (Fig. 3, 4, 5).

Author response image 1.

In Discussion: “Although the present study includes only non-fatal seizures, our report of HR during spontaneous seizure events supports work suggesting physiological events during non-fatal seizures predict SUDEP risk (Lamrani et al., 2023; Ryvlin, Nashef, & Tomson, 2013; Schuele et al., 2011). It remains to be determined if ictal events during fatal and non-fatal spontaneous seizures are different and future studies could help clarify any distinctions. Our examination focused on HR (and not respiration or BP). Whether exaggerated BJR-mediated HR response co-occurs with greater magnitude BJR-mediated apnea and hypotension remains to be determined.”

It is unclear if the bradycardias were spontaneous or a result of preceding central or obstructive apneas, oxygen desaturations, hypercapnia, arrhythmias, or other possible triggers.

Our work demonstrates the occurrence of ictal bradycardia whereas identifying precipitating factor(s) and interaction(s) of this phenomenon will require alternate approaches. Normal activation of hypoxic and hypercapnic ventilatory responses would be expected to increase HR. However, whether these chemoreflex circuits undergo remodeling in Kcc2/Crh mice remains unknown. Obstructive apnea via laryngospasm can cause reflex bradycardia, but we did not record airflow or respiratory EMG in these studies to determine the existence of obstructive apnea. More testing is merited.

In Discussion, “…Additional seizure-related disturbances such as central or obstructive apneas may contribute to BJR activation. Hypoxia, which could result from ictal apnea, is known to increase excitatory neurotransmission to cardiac vagal motor neurons that cause vagal bradycardia (Griffioen et al., 2007) and induces platelet activation (Tyagi et al., 2014) which is considered the main source of circulating serotonin for the BJR. As such, hypoxia resulting from apnea may increase likelihood of exaggerated BJR during seizures. Consistent with this…”

Considerable prior work in the literature suggests SUDEP could be mediated, in some patients, by a burst of parasympathetic activity to the heart. Were the heart rate changes in these animals during seizures inhibited or blocked by atropine or atenolol?

With this study targeting spontaneous seizures we were unable to test acute pre-treatment with atropine or atenolol. We did observe reduced mortality in Kcc2/Crh+KA mice that underwent chronic parasympathetic blockade via osmotic minipump of methylscopolamine (Figure 5).

In Discussion:

“Chronic inhibition of vagal parasympathetic motor output (the driver of BJR reflex bradycardia) improved mortality by 10% in Kcc2/Crh mice. Although this improvement provides some hope for patients at high risk for SUDEP with no treatment options, additional avenues of investigation are needed to more directly link seizure-related bradycardias to vagal parasympathetic motor output.”

The injection of the 5HT agonist phenylbiguanide into the right jugular is not a selective approach for activating the Bezold Jarisch Reflex (BJR), which is caused by increased activity of intracardiac sensory neurons (generally activated with is chemia or a combination of low preload with high contractility). The results should be interpreted more cautiously, as a response to systemic administration of phenylbiguanide only.

BJR can be experimentally triggered with intravenous infusion of various compounds including veratrum alkaloids (Cramer, 1915), 5HT (Fozard 1983), or 5HT3R agonists (Verberne & Guyenet, 1992). We now specifically refer to BJR in our study as that induced by PBG (a 5HT3R agonist), as others have done (Yamano et al., 1995; PMID: 8786638) and acknowledge endogenous BJR activation in the discussion.

Added to the results: “As dysfunction of serotonergic signaling is implicated in the pathophysiology of SUDEP (Richerson & Buchanan, 2011), we investigated the Bezold Jarisch Reflex (BJR) (Fig. 5), a cardioinhibitory reflex that is reliably triggered experimentally by activation of cardiopulmonary vagal afferents containing serotonin type 3 receptors (5HT3R) (Fozard 1983; Yamano et al., 1995).”

Added to Discussion: “Although our report is the first to link BJR to SUDEP, serum serotonin levels are elevated following generalized seizures (Murugesan et al., 2018), likely via release from activated platelets (Cloutier et al., 2018). This surge in serum serotonin could lead to endogenous activation of BJR, as bolus intravenous infusion of serotonin reliably triggers BJR experimentally (Fozard 1983; Whalen et al., 2000).”

Reviewer #2 (Public review):

Some of the conclusions may be a bit overstated as is and would benefit from more discussion and perhaps additional data.

Post-ictal HR data are now included in the Results, Table 2.1 and Figure 2.

The Discussion now includes more details regarding respiration, BP, obstructive apnea, properties of the BJR, and distinctions in seizure type based on whether evoked or lethal.

eLife Assessment

This important study provides new insights into the patterns of organelle inheritance in the protozoan parasite Toxoplasma gondii. The authors introduce an innovative dual-labeling approach to distinguish maternally inherited from de novo synthesized organelles, representing convincing evidence that different organelles follow distinct inheritance fates during parasite replication. Future studies will be needed to determine whether the residual body functions as a central recycling hub, as the current data are also consistent with alternative models.

Reviewer #1 (Public review):

[Editors' note: this version has been assessed by the Reviewing Editor without further input from the original reviewers. The authors have addressed the comments raised in the previous round of 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) are 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 better understanding the mechanisms that drive the differences between structures and the universality of these processes in other apicomplexan parasites. In particular, this study shows that the residue body is a region of the cell syncytium that organelles can be actively transported from. Therefore, it is a space that can actively contribute to the segregation of the late segregating micronemes and rhoptries.

Reviewer #2 (Public review):

Summary:

Toxoplasma gondii is an obligate intracellular parasite and the causative agent of toxoplasmosis. Parasite invasion of host cells, intracellular replication, and subsequent egress, which results in destruction of the infected cell, are central to pathogenicity. This manuscript focuses on understanding how maternal resources, specifically cellular organelles, are shared between daughter parasites during cell division. Many organelles are present as a single copy, making their division and inheritance essential for successful replication. In T. gondii, our understanding of how organelles are divided during cell division remains limited, and this study helps address this important knowledge gap.

Strengths:

The major strength of this study is the use of a Halo-based pulse-chase assay to characterize patterns of organelle inheritance and to monitor protein synthesis, turnover, and movement. This approach will be of considerable interest to the field. Using this method, the authors identify three major modes of organelle inheritance:

(1) Organelles present in multiple copies (such as micronemes and rhoptries) are partitioned between daughter parasites, with additional contributions from newly formed vesicles. Newly synthesized and pre-existing material remain as distinct populations within the cell.

(2) Single-copy organelles, such as the Golgi and apicoplast, are expanded through the incorporation of newly synthesized material before division.

(3) Cytoskeletal structures are synthesized de novo during each round of cell division.

These findings provide a more refined understanding of organelle inheritance and demonstrate that secretory organelles are not generated entirely de novo during each round of division, as was previously thought.

The paper places particular emphasis on the fate of maternal micronemes and rhoptries during division. The data show that (1) during division in wild-type cells, maternal micronemes and rhoptries are detectable in the residual body (RB); however, the majority of these organelles are localized within the parasite body, either at the apical or basal ends of the daughter parasites (Fig. 6). (2) In the absence of the myosin motor MyoF, micronemes and rhoptries accumulate in the residual body and are not properly trafficked to the daughter cells. Upon restoration of MyoF protein levels, these organelles redistribute to the daughter cells, although in an uneven manner.

Weaknesses:

The second half of the paper focuses on a more detailed characterization of microneme and rhoptry recycling. While the authors propose that the RB acts as a central hub for recycling both organelles, the current data do not fully support this conclusion.<br /> The model that microneme and rhoptry recycling is RB-dependent relies largely on the MyoF depletion phenotype and the limited detection of maternal organelles in the RB of wild-type parasites. Alternative models remain plausible, including direct trafficking to daughter cells, with RB accumulation upon MyoF depletion reflecting impaired trafficking rather than an obligatory RB-dependent recycling pathway, as now discussed by the authors.

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 daughter-derived organelles using their dual-labeling Halo Tag approach. They reveal that different organelles are trafficked to daughter parasites in three broad patterns 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.

Strength:

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

Weakness:

The inability to achieve higher temporal resolution due to phototoxicity precluded tracking of single micronemes, thus it remains possible that some micronemes follow a path similar to rhoptries and enter daughter cells before development of the residual body while others are recycled via the residual body.

Author response:

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

Public Reviews:

Weaknesses:

(1) In addressing the question of residual body participation in sorting of organelles, a clear definition of this structure is required including when and where it is delineated from the posterior of a mother cell during the formation of daughter structures. The authors' definition is as follows: 'The RB originates from the collapse of the maternal parasite during daughter cell budding and occupies the space previously occupied by the mother cell.' As such, a clear marker of the mother cell 'collapse' is required, but such a marker is not identified or used in the study to separate what might be considered an active part of the mother cell during early daughter formation, and the residual body. This might seem like moot a point, but it would help to 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? The authors elegantly show that MyoF is necessary for segregation of micronemes and rhoptries into daughters, and that MyoF depletion leads to accumulation of these organelles within the residual body. Moreover, restored expression of MyoF can then recover these organelles. This clearly demonstrates the activity of the residual body as part of the syncytium space that participates in the maintenance of the vacuole. But does it imply that this space necessarily handles all inherited micronemes and rhoptries as a 'trafficking hub'? My concern with the lack of a clear definition could provide some misinterpretation or overinterpretation of the contribution residual body.

We thank the reviewer for raising this conceptual point. We agree that, in the absence of a molecular marker that uniquely defines the nascent RB, the precise transition between posterior maternal cytoplasm and a morphologically distinct RB cannot be determined during early daughter formation. We have therefore clarified our terminology in the revised manuscript and define the RB operationally as the posterior compartment/connection between daughter parasites. We also avoid assigning early posterior trafficking events unambiguously to a fully formed RB. We further agree that the current data do not establish that all inherited micronemes and rhoptries must transit through the RB. We have therefore revised the Results and Discussion and softened terminology such as “central trafficking hub” and now conclude that the RB represents an important dynamic compartment in organelle recycling and redistribution, without implying that it is an obligatory intermediate for every inherited secretory organelle.

(2) A further, remarkable conclusion is that maternal micronemes are evenly segregated into daughters through an active process for 'balanced microneme inheritance'. The proportion of maternal micronemes is quantified up to the 8-cell stage and shown to be not significantly different between cells. But would this result be expected with random assortment at this stage? The authors model the probability of a 32-cell stage vacuole occurring with each daughter having within 0-3 maternal micronemes and this is considered unlikely. However, the authors neither present the modelling for the 8cell stage or show quantification of 32-cell vacuoles. They do show some images of large vacuoles, but it is not possible to determine the distribution of maternal micronemes in these images. A regulated process of segregation would require a complex mechanism where some form of microneme counting would be required to create the proposed balance. It is, therefore, important to have strong data supporting such a hypothesis, but this is not currently presented.

We agree that the previous wording implied a mechanistic conclusion beyond what can be established from the present dataset. We have therefore revised the manuscript so that the relatively even distribution of maternal micronemes at the 8-cell stage is presented as an observation that is consistent with a non-random or regulated partitioning process, rather than evidence for an established microneme-counting mechanism. The 32-cell model is now presented as supportive rather than definitive evidence, and we explicitly acknowledge that the quantitative experimental dataset was obtained at the 8-cell stage. 

Reviewer #2 (Public review):

(1) The second half of the paper focuses on a more detailed characterization of microneme and rhoptry recycling. The authors strongly argue that the RB is a central hub for recycling micronemes and rhoptries; however, this conclusion is not fully supported by the data. For example, the authors state…Thus, the model that all microneme and rhoptry trafficking is RB-dependent is based primarily on the MyoF depletion phenotype (which results in RB accumulation) together with the observation that a relatively small amount of maternal microneme and rhoptry material is detectable in the RB of wild-type parasites. Although the authors' interpretation-that recycling is RB-dependent-is one possible explanation, alternative models are not discussed. For example, an alternative possibility is that the majority of micronemes and rhoptries are trafficked directly from the apical end of the mother parasite to the daughter cells without passing through the RB. In this scenario, only a subset of the organelles would enter the residual body, perhaps reflecting imperfect trafficking efficiency rather than an obligatory recycling step. Loss of MyoF would impair this trafficking pathway, resulting in the accumulation of secretory organelles within the RB. In other words, RB accumulation could be a consequence of MyoF depletion rather than evidence that all trafficking in wild-type parasites normally proceeds through the RB. This alternative interpretation seems particularly relevant for the rhoptries, given that the authors themselves state that "M-RON2 was integrated into daughter rhoptries prior to mother cell collapse and formation of the RB."

We agree with the reviewer that the current data do not establish obligatory transit of all maternal micronemes and rhoptries through the RB. We have revised the manuscript throughout to make this distinction explicit. In particular, we now emphasize that maternal MIC2 can be directly observed entering the RB, whereas most maternal RON2 is incorporated into daughter rhoptries before mother-cell collapse and formation of a morphologically distinct RB. This observation leaves open the possibility that a substantial fraction of maternal rhoptries is transferred directly from the mother to developing daughters. We have also revised our interpretation of the MyoF-depletion phenotype. The accumulation of maternal MIC2 and RON2 in the RB following MyoF depletion demonstrates that MyoF is required for efficient redistribution of both organelle populations, but does not by itself demonstrate that both normally follow an identical spatial route through the RB. We now explicitly state that their precise trafficking routes and timing may differ.

We nevertheless retain the conclusion that the RB is a dynamic compartment involved in organelle recycling because maternal MIC2 can be directly observed entering and leaving this compartment, and material accumulated there following MyoF depletion can subsequently be redistributed after restoration of MyoF.

(2) Figure S10C. To determine whether microneme degradation occurs in the RB, the authors quantified the fluorescence intensity of individual micronemes in control parasites and following auxin washout, showing that after redistribution the fluorescence intensity of individual vesicles is unchanged. However, this is not the appropriate analysis to address the question being asked. To conclude that micronemes are not degraded, the authors would need to quantify the total fluorescence intensity within the entire vacuole. For example, if half of the micronemes were degraded, the remaining micronemes would be expected to retain the same fluorescence intensity as those in the control parasites. Thus, unchanged fluorescence intensity of individual vesicles does not exclude the possibility that degradation has occurred.

We agree with this criticism and have revised the interpretation of the experiment accordingly. We no longer conclude that the analysis excludes microneme degradation. We now explicitly acknowledge that analysis of individual recovered micronemes cannot exclude degradation of a fraction of the total microneme population during RB retention. Thus, the experiment supports preservation of MIC2 signal in the recovered organelles but is no longer presented as evidence that no microneme degradation occurs.

Reviewer #3 (Public review):

Weakness:

The inability to achieve higher temporal resolution due to phototoxicity precluded tracking of single micronemes, thus it remains possible that some micronemes follow a path similar to rhoptries and enter daughter cells before development of the residual body while others are recycled via the residual body. 

We agree and have incorporated this limitation into the revised interpretation. Our live imaging demonstrates that maternal MIC2 can enter the RB and subsequently redistribute to daughter parasites, but it does not establish that every individual maternal microneme follows this route. We thank the reviewer for highlighting this distinction, which has helped us clarify the model presented in the Results and Discussion.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) Carruthers and Sibley, 1997, is still the cited ref for Tic20 in the apicoplast despite the authors saying that would correct this to a van Dooren publication.

Corrected

(2) In Figure 2B three biological replicates were used however there are no error bars shown. The only reason for performing replicates is the observe the variance in the data, so if this is not shown the replicates are effectively meaningless. I strongly advice that error bars are given to indicate this seeing that the data in this figure form the basis of the major conclusions of the study. It might be necessary to show this in supplemental forms with fewer proteins if the error bars are too difficult to see in the combined figure.

We agree and have corrected Figure 2B to display the variability between the three independent biological replicates. Error bars now represent the standard deviation.

(3) Line 136: Can you conclude that these inheritance patterns are 'organelle-specific' when each organelle is only sampled with one or two proteins. Isn't it better to conclude that these are protein-specific, with the hypothesis that they might represent the orgnalle as a whole. I imagine that some proteins in organelles such as the apicoplast have shorter half-lives than others, and therefore some apicoplast proteins might behave like 'Group 3' proteins.

We thank the reviewer for raising this point. We agree that individual proteins within the same organelle may differ in their turnover kinetics and that analysis of one or two markers cannot establish that every molecular component of an organelle behaves identically. However, we do not think that describing the observations exclusively as protein-specific inheritance would fully reflect the biological process investigated here. The proteins analysed are established markers of defined organelles, and our conclusions are based not only on changes in fluorescence intensity, but also on the localization, morphology, partitioning, and spatial relationship between maternally inherited and newly synthesized organelle populations.

This is particularly evident for micronemes and rhoptries, where maternal and de novo material remain spatially separated and individual organelles can be followed during inheritance.

In addition, the microneme phenotype observed with MIC2 was confirmed using AMA1, MIC4, and MIC8.

We therefore retain the terminology of organelle inheritance, while acknowledging that individual proteins within a given organelle may exhibit different turnover kinetics and that the markers analysed may not represent the behaviour of every molecular component of the organelle.

(4) Line 222: It is an odd phrase to suggest that the Golgi, ER etc 'bypass' the residual body, which suggests an active avoidance mechanism. Would the authors also conclude that the nucleus 'bypasses' the RB? Moreover, the ER and mitochondria are actually known to be present in the RB forming continuous organelles between daughters in a vacuole. So again, this might be an overstatement that mispresents how the RB participates in vacuole functions.

We agree and have removed the term “bypass.” The revised text now states only that we did not observe comparable accumulation of the analysed Golgi, ER, or apicoplast markers in the RB during inheritance. This avoids implying an active avoidance mechanism and is compatible with the known continuity of ER and mitochondria through the RB.

Reviewer #2 (Recommendations for the authors):

Minor comments:

Figure 8F and Video S6: The authors should specify the time point after IAA washout at which live imaging was initiated. Does time 0 in the video correspond to the point at which IAA was removed?

We have clarified this in the Results and Methods. Auxin was removed after 24 h of replication, and live imaging was subsequently initiated. Time 0 in Figure 8F and Video S6 corresponds to the first acquired frame after auxin washout.

Figure S10 should read auxin, not auxine.

Corrected

Reviewer #3 (Recommendations for the authors):

I have no further suggestions. Congratulations to the authors for a lovely study.

eLife Assessment

This important study shows that nutrient resorption efficiency in the widespread wetland grass Phragmites australis varies with population origin and remains largely stable under experimentally imposed salt stress, supporting limited short-term plasticity and a role for genetic differentiation. The findings suggest that predictions of wetland nutrient cycling under increasing salinization should account for intraspecific variation and phylogeographic composition, the evidence is compelling, based on a common-garden experiment involving 110 genotypes, paired control and salinity treatments, and convergent metabolomic, ionomic, and whole-plant evidence confirming substantial physiological stress. The revised manuscript clarifies the partial overlap between ecotype and phylogeographic lineage and appropriately qualifies the modest explanatory contribution of latitude, conclusions remain restricted to one species, one growing season, and a single moderate salinity treatment; an ecotype-specific nitrogen resorption response also indicates that plasticity is not entirely absent and the physiological mechanisms and responses to chronic, stronger, or multigenerational salinity exposure remain unresolved. The study will interest researchers working on plant functional ecology, nutrient cycling, and wetland responses to global change.

Reviewer #1 (Public review):

Summary:

This study demonstrates that nutrient resorption efficiency (NuRE) in Phragmites australis is genetically canalized rather than plastic to salt stress. Using 110 genotypes in a common garden, the authors show that intraspecific variation in NuRE is explained by phylogeographic lineage, ecotype, and latitude, not by effective salinity. Element specific regulatory strategies further reveal how N, P, and K resorption are differentially controlled. At the population level, this is an important study that fundamentally advances our understanding of plant functional trait evolution and its implications for ecosystem nutrient dynamics under global change.

Strengths:

This study is the first to demonstrate genetic determination of a key nutrient conservation trait under effective salt stress in a widespread macrophyte, directly testing the 'plastic acclimation versus inherent conservatism' paradigm in a non-nutrient stress context. The experimental design is rigorous: each genotype was paired across control and salt treatments, and multilevel stress effectiveness (metabolomics, biomass, Na accumulation) was confirmed before evaluating NuRE. The large sample size of a macrophyte and dual classification (phylogeography + ecotype) allow robust disentangling of genetic versus plastic sources of variation.

The analysis comprehensively tests three resorption control hypotheses using appropriate SMA regression, revealing element specific and condition dependent patterns. The latitudinal gradient and variation partitioning provide strong evidence that genetic origin and geographic context outweigh short term plasticity, with important implications for predicting ecosystem nutrient cycling under global change. This study provides a clear empirical demonstration that a key nutrient conservation trait can remain homeostatic under non nutrient stress, and that intraspecific variation is primarily a product of population differentiation rather than short term plasticity.

Weaknesses:

First, the salinity treatment spanned only one growing season. The conclusion of genetic canalization therefore specifically refers to the absence of plasticity to an acute salt shock. Whether long term, multigenerational chronic salinity could act as a selective agent or induce transgenerational plasticity remains an open and interesting question for further research. Likewise, the physiological mechanisms underlying the observed lack of plastic increase in NuRE (for example, phloem loading or senescence gene expression) are not directly resolved, leaving some inference about trade-offs versus true unresponsiveness. These points do not weaken the study's main conclusion. Instead, they suggest productive future directions, such as longer-term field manipulations and targeted molecular investigations.

Second, the test of nutrient limitation control relies on resorbed N:P and N:K ratios as proxies, an established but indirect approach. Direct nutrient addition experiments would provide stronger causal evidence. Also, the metabolomic analysis is used primarily to validate stress effectiveness; deeper integration of specific metabolites with NuRE variation across genotypes could have offered mechanistic insights but was not pursued. Additionally, the potential collinearity between ecotype and phylogeographic lineage among Chinese populations is not quantitatively addressed. None of these considerations undermine the main finding, which is supported by a robust experimental design and widely accepted analytical approaches.

Comments on revised version.

The author carefully revised the parts that might cause confusion.

Reviewer #2 (Public review):

Summary:

The manuscript shows that nutrient resorption efficiency in Phragmites australis is largely genetically canalized rather than plastic under effective salt stress, with variation mainly associated with phylogeographic lineage, ecotype, and latitude.

Strengths:

The common-garden experiment with 110 genotypes, paired control and salt treatments, multi-level stress validation, and element-specific analyses provides compelling support for the central conclusions.

Weaknesses:

The generality is limited by the focus on a single species and a single growing season, and some mechanisms are inferred indirectly.

Author response:

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

The major revisions include:

(1) Conceptual framing and scope: defined canalization in the Introduction and clarified that our conclusions are restricted to limited NuRE plasticity during one growing season under a single moderate salinity treatment.

(2) Methods and classification: clarified the substrate composition and elemental measurements, specified that the ecotype analysis included only Chinese populations, and explained the partial association between ecotype and phylogeographic group.

(3) Interpretation: expanded the discussion of K resorption and inverted nutrient limitation and tempered the interpretation of latitude and the substantial unexplained variation.

(4) Robustness and presentation: added Supplementary Figure S7 showing that carbon standardization did not alter the main conclusions, added significance symbols to Table 1, corrected the unit in Figure 2b, and revised repetitive wording in the Discussion.

Public Reviews:

Reviewer #1 (Public review):

Weaknesses:

(R1-P1) First, the salinity treatment spanned only one growing season. The conclusion of genetic canalization therefore specifically refers to the absence of plasticity to an acute salt shock. Whether long-term, multigenerational chronic salinity could act as a selective agent or induce transgenerational plasticity remains an open and interesting question for further research. Likewise, the physiological mechanisms underlying the observed lack of plastic increase in NuRE (for example, phloem loading or senescence gene expression) are not directly resolved, leaving some inference about trade-offs versus true unresponsiveness. These points do not weaken the study’s main conclusion. Instead, they suggest productive future directions, such as longer-term field manipulations and targeted molecular investigations.

We agree that our evidence is limited to the absence of NuRE plasticity during one growing season under the imposed salinity treatment and does not resolve chronic or multigenerational responses or their physiological basis. We therefore revised Discussion 4.1 to delimit the canalization inference, identify the proposed mechanisms as untested, and specify the longer-term and mechanistic studies needed to distinguish among them.

Discussion 4.1, fourth paragraph, inserted immediately after the sentence beginning “This discrepancy may stem from differences in the type and duration of stress applied ”.

“Our inference of canalization is therefore limited to the absence of a plastic NuRE response during one growing season under the imposed salinity treatment. Chronic, more severe, or multigenerational salinity exposure may produce acclimatory, epigenetic, or transgenerational responses that cannot be evaluated here. Moreover, although altered phloem loading, disruption of senescence-associated remobilization, and reallocation towards osmotic adjustment are plausible explanations for the observed response, we did not directly measure these mechanisms. Long-term experiments combined with targeted molecular and transport measurements are needed to distinguish among these possibilities.”

(R1-P2) Second, the test of nutrient limitation control relies on resorbed N:P and N:K ratios as proxies, an established but indirect approach. Direct nutrient addition experiments would provide stronger causal evidence. Also, the metabolomic analysis is used primarily to validate stress effectiveness; deeper integration of specific metabolites with NuRE variation across genotypes could have offered mechanistic insights but was not pursued. Additionally, the potential collinearity between ecotype and phylogeographic lineage among Chinese populations is not quantitatively addressed. None of these considerations undermines the main finding, which is supported by a robust experimental design and widely accepted analytical approaches.

We agree and have clarified all three evidential limits. First, the resorbed N: P and N: K analyses are now described as indirect evidence consistent with nutrient-limitation control, not as a causal test; direct nutrient-addition experiments would be required for causal inference. Second, metabolomics is identified as validation of physiological stress rather than a genotype-specific mechanistic analysis. Third, because ecotype and phylogeographic group are partly associated, they were fitted in separate models. The genotype random effect accounts for paired measurements but does not remove confounding between the classification schemes; ecotype differences are therefore interpreted as complementary rather than independent evidence.

Discussion 4.2, third paragraph.

“Within this context, the consistent ‘inverted’ nutrient limitation pattern (i.e., a slope significantly >1 for the relationship between log Resorbed N:P and log Green N:P) provides indirect evidence consistent with nutrient-limitation control at the intraspecific level in P. australis, but it cannot establish causal nutrient limitation. Direct factorial nutrient-addition experiments would be required to determine whether the observed resorption patterns are driven by the relative limitation of N, P, or K.”

Discussion 4.1, first paragraph, inserted immediately after the sentence ending “providing a robust foundation to evaluate NuRE responses”.

“In this study, metabolomic profiling was used primarily to confirm that the salinity treatment induced broad physiological stress, rather than to resolve genotype-specific metabolic mechanisms underlying NuRE variation. Integrating metabolite profiles with genotype-level NuRE responses would be a valuable direction for future mechanistic research.”

Methods 2.4.

“Phylogeographic group and ecotype were analysed in separate linear mixed-effects models because ecotype classifications were available only for Chinese populations and were partly associated with phylogeographic structure. Each model included salinity treatment and either phylogeographic group or ecotype as fixed effects, with genotype fitted as a random effect to account for the paired experimental design in which each genotype was exposed to both control and salt conditions.”

Discussion 4.4, first paragraph, inserted immediately after the sentence ending “governed by geographic origin (phylogeographic group and ecotype)”.

“The separate-model approach avoids including the two correlated classification schemes as simultaneous independent predictors, but it does not fully disentangle deep phylogeographic history from recent habitat-associated differentiation. We therefore interpret the ecotype analysis as complementary evidence of habitat-associated differentiation rather than as an effect independent of phylogeographic history.”

Reviewer #2 (Public review):

(R2-P1) The experiment covers only one growing season, with salinity applied in June and measurements in December. While the stress is clearly effective, longer-term or multi-year stress might reveal acclimation or epigenetic effects that are not captured. Given the author team’s expertise in parental and transgenerational effects in clonal plants, this limitation is particularly relevant and warrants more thorough discussion in the manuscript.

We agree. This concern overlaps with Reviewer #1’s temporal-scope comment. We have revised Discussion 4.1 to state explicitly that our inference is restricted to the absence of a plastic NuRE response during one growing season. We also acknowledge that chronic or multigenerational exposure could induce acclimatory, epigenetic, or transgenerational responses that were not captured by the present design.

See the full revised text under R1-P1 above.

(R2-P2) The salinity treatment uses a single moderate level of 10 ppt, which does not allow assessment of whether more extreme stress might trigger a plastic response. A dose-response design across a gradient would have provided stronger inference about the threshold at which NuRE canalization might be overcome. Additionally, the ecotype analysis in Figure 4 applies only to Chinese populations, as classification was not available for non-Chinese populations, which should be stated more explicitly in the Results.

We agree with both points. We have revised Discussion 4.1 to acknowledge that the single 10 ppt treatment does not exclude the possibility of a plastic NuRE response at higher salinity or along a broader dose-response gradient. We therefore frame the identification of a possible response threshold as a priority for future experiments.

We have also revised Results 3.2 to state explicitly that the ecotype analysis in Figure 4 included only Chinese populations because ecotype classifications were unavailable for non-Chinese populations.

Discussion 4.1, fourth paragraph, at the same revision point as R1-P1: immediately after the sentence beginning “This discrepancy may stem from differences in the type and duration of stress applied”.

“Because only one moderate salinity level (10 ppt) was tested, our results do not exclude plastic NuRE responses at higher salinity or along a dose-response gradient. Future experiments should determine whether a threshold exists beyond which the apparent stability of NuRE is overcome.”

Results 3.2, second paragraph, inserted immediately after the sentence reporting the ecotype effects and ending “(Figure 4; Figure S5)”.

“It should be noted that the ecotype analysis here was based only on Chinese populations, as ecotype classification was not available for non-Chinese populations.”

(R2-P3) The variation partitioning shows latitude as a significant predictor, but the R² values are relatively low, indicating that much variance remains unexplained. The manuscript should avoid overinterpreting latitude’s explanatory power and more openly acknowledge the role of unmeasured factors. The interpretation of slopes greater than 1 for the resorbed N:P versus green N:P relationship, labeled as “inverted limitation”, also needs further explanation regarding its functional significance.

We agree that the original wording overemphasized latitude. Results 3.4 and Discussion 4.3 now describe latitude as the largest contributor among the measured predictors while emphasizing its modest individual R² and the substantial unexplained variation. We also expanded Discussion 4.2 to explain that slopes greater than 1 indicate disproportionate recovery of P or K relative to N and to present nutrient balance, P conservation, K mobility, and constraints on N remobilization as non-exclusive hypotheses rather than established mechanisms.

Results 3.4, first paragraph, replacing the sentence beginning “Furthermore, variation partitioning analysis indicated that latitude”.

“Variation partitioning indicated that latitude had the largest individual contribution among the measured predictors, but its contribution was modest for N, P, and K resorption (individual R² = 0.092, 0.057, and 0.094, respectively; Table 1). The very small contributions of green-leaf P concentration (R² = 0.006) and stoichiometry (R² < 0.001) further indicate that most variation in P resorption was associated with factors not represented in the present models.”

Discussion 4.3, first paragraph.

“Although latitude explained more variation than the other measured predictors, its individual contribution remained modest. The substantial unexplained variance indicates that additional climatic, edaphic, demographic, or genetic factors also contribute to NuRE variation. We therefore interpret latitude as a significant but limited correlate of NuRE rather than as a dominant determinant.”

Discussion 4.2, first paragraph.

“Functionally, slopes greater than 1 indicate that changes in green-leaf N:P or N: K are accompanied by disproportionate changes in the corresponding resorbed ratio, consistent with relatively greater recovery of P or K than of N across the observed nutrient gradient. This pattern may contribute to maintaining internal N:P:K balance during regrowth. It may also reflect stronger conservation of P, the high mobility of K, or constraints on the remobilization of N retained in structural or metabolic compounds. Because the experiment did not include nutrient additions or direct measurements of remobilization costs, these explanations remain hypotheses.”

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(R1-R1) Clarify the concept of “canalization” early. Consider adding one sentence in the Introduction or Discussion explicitly defining canalization in this context (i.e., NuRE varies among populations but this variation is genetically determined and shows little plasticity to salinity). This will help readers less familiar with evolutionary biology terminology.

We thank the reviewer for this helpful suggestion. We agree that canalization should be defined when it is first introduced. We have therefore added a sentence to the Introduction, immediately after introducing the evolutionary canalization hypothesis, to clarify how this concept is used in our study.

Introduction, fourth paragraph.

“Here, canalization denotes genetically based differences in NuRE among populations, coupled with limited phenotypic plasticity of this trait under the short-term salinity treatment.”

(R1-R2) Discuss potassium more deeply. In the Discussion (section 4.2 or 4.4), speculate on why K resorption lacks concentration control. Does Na⁺ accumulation functionally substitute for K in osmotic adjustment, thereby decoupling resorption from green leaf K concentration?

We appreciate this suggestion and have expanded Discussion 4.2. We now propose partial functional substitution of K⁺ by accumulated Na⁺ during osmotic adjustment as one possible explanation for the weak coupling between green-leaf K concentration and K resorption. We explicitly frame this explanation as tentative because it was not directly tested in the present experiment.

Discussion 4.2, second paragraph.

“One possible explanation is the partial functional substitution of K⁺ by Na⁺ during osmotic adjustment. Na⁺ can replace part of the nonspecific vacuolar osmotic function of K⁺ in plants and has been reported to become a major osmoticum in P. australis from higher-salinity habitats (Wakeel et al., 2011; Zhao et al., 1999). Increased Na⁺ accumulation may therefore reduce reliance on K⁺ for osmotic adjustment, potentially contributing to the weak relationship between green-leaf K concentration and K resorption efficiency observed here.”

Wakeel, A., Farooq, M., Qadir, M., & Schubert, S. (2011). Potassium substitution by sodium in plants. Critical Reviews in Plant Sciences, 30(4), 401–413. https://doi.org/10.1080/07352689.2011.587728

Zhao, K. F., Feng, L. T., & Zhang, S. Q. (1999). Study on the salinity-adaptation physiology in different ecotypes of Phragmites australis in the Yellow River Delta of China: Osmotica and their contribution to the osmotic adjustment. Estuarine, Coastal and Shelf Science, 49(Supplement 1), 37–42. https://doi.org/10.1016/S0272-7714(99)80006-7

(R1-R3) Address the potential confounding of ecotype and phylogeography. The dual classification (Figure 3 vs 4) is elegant. However, Chinese ecotypes (freshwater, coastal, inland saltmarsh) may be partially confounded with phylogeographic lineages. A brief sentence explaining how the analytical approach (separate models, random effects) helps separate deep evolutionary history from recent local adaptation would strengthen the interpretation.

We agree. This concern is addressed in detail under R1-P2. We clarified why phylogeographic group and ecotype were fitted in separate models, what the genotype random effect accounts for, and why the ecotype results cannot be interpreted independently of phylogeographic history.

See R1-P2, Locations C1 and C2.

(R1-R4) In section 2.1, specify whether the soil mixture ratio (2 soil: 1 peat moss: 1 river sand) is by volume or by mass.

We thank the reviewer for identifying this ambiguity. The ratio was based on volume, and we have revised Methods 2.1 accordingly.

“The plants were planted in barrels (total volume 25 L; top diameter 32.5 cm, bottom diameter 28.4 cm, height 38.5 cm) containing 20 L of a substrate composed of soil, peat moss, and river sand in a 2:1:1 volume ratio (Figure S1).”

(R1-R5) In the Materials and Methods section, the element potassium (K) is described twice. Specifically, in line 176, the sentence “Besides C, N and P, other eight elements (K, Cu, Zn, Fe, Mn, Mg, Si, Na) were quantified in leaf tissues” should be revised to “Besides C, N, P and K, other seven elements (Cu, Zn, Fe, Mn, Mg, Si, Na) were quantified in leaf tissues” to avoid redundancy.

We thank the reviewer for identifying this redundancy. We have corrected the sentence in Methods 2.2.

“Besides C, N, P and K, seven additional elements (Cu, Zn, Fe, Mn, Mg, Si, and Na) were quantified in leaf tissues.”

(R1-R6) Citations should be formatted and ordered alphabetically or by year of publication.

We thank the reviewer for pointing out this issue. We standardized multi-reference citations, reordered the reference list alphabetically by first-author surname, and verified correspondence between in-text citations and reference entries.

Full-manuscript citation and reference-list audit.

Reviewer #2 (Recommendations for the authors):

(R2-R1) In the discussion of the “inverted” nutrient limitation, elaborate on why P and K are recovered more relative to N. Consider whether this reflects a strategy to maintain an optimal N: P: K ratio or arises from higher costs or lower availability of N.

We agree. This issue is addressed in detail under R2-P3, where we explain the meaning of slopes greater than 1 and present the possible functional mechanisms as hypotheses rather than established explanations.

See R2-P3, Location C.

(R2-R2) Expand Table 1 to include confidence intervals or p-values for individual effects. The extremely low R² for concentration and stoichiometry on P resorption should be more explicitly noted as evidence for the dominance of latitude.

We agree and have expanded Table 1 by adding significance symbols (*) to the individual R² values. Significance was assessed for the corresponding fixed effects in the full linear mixed-effects models using Type III tests with Satterthwaite’s approximation for degrees of freedom. For P resorption, latitude had the largest individual contribution and was significant (R² = 0.057, p = 0.005), whereas the contributions of green-leaf P concentration and stoichiometry were very small and nonsignificant (R² = 0.006 and < 0.001, respectively). We revised the Results to emphasize this contrast while acknowledging that latitude explained only a modest proportion of the total variation.

See R2-P3, Locations A and B, for the corresponding Results and Discussion revisions.

(R2-R3) Standardize the abbreviation to “NuRE” throughout, correcting the use of “NRE” in the introduction.

We thank the reviewer for identifying this inconsistency. We standardized the abbreviation to NuRE throughout the manuscript.

(R2-R4) Acknowledge in the discussion that the single moderate salinity level may not have been severe enough to trigger a plastic response, justifying future dose-response experiments.

We agree. This limitation is addressed under R2-P2, where we state that a single 10-ppt treatment cannot exclude plastic responses at higher salinity or along a broader dose-response gradient.

See R2-P2, Location A.

(R2-R5) In the Results section, explicitly state that the ecotype analysis in Figure 4 is based only on Chinese populations, not all 110 genotypes, because ecotype classification was not available for non-Chinese populations.

We agree. This clarification is provided under R2-P2, where Results 3.2 is revised to state that the Figure 4 ecotype analysis includes only Chinese populations.

See R2-P2, Location B.

(R2-R6) Consider adding a supplementary figure comparing raw and carbon-standardized NuRE values to show whether the correction altered main conclusions.

We agree and have added Supplementary Figure S7 comparing raw and carbon-standardized NuRE. The two estimates were strongly correlated for N, P, and K (Pearson’s r = 0.997–0.999), and analyses using raw NuRE retained the same conclusions for phylogeographic group, ecotype, salinity, their interactions, and latitude. Thus, carbon standardization slightly shifted the absolute values without altering the main conclusions.

Methods 2.3.

“Raw NuRE was calculated without carbon standardization and compared with carbon-standardized NuRE using Pearson correlations; the main linear mixed-effects analyses were also repeated using raw NuRE.”

Results 3.4, inserted after the existing paragraph reporting the latitude effects and referring to Figure 6 and Table 1.

“Raw and carbon-standardized NuRE were strongly correlated for N, P, and K (Pearson’s r = 0.997–0.999; Figure S7), and analyses using raw NuRE did not alter the conclusions for phylogeographic group, ecotype, salinity, their interactions, or latitude.”

Supplementary Figure S7 legend

“Figure S7 Comparison of raw and carbon-standardized nutrient resorption efficiency (NuRE) for N, P, and K. Points represent genotype-by-treatment observations (n = 206), coloured by treatment. Grey dashed lines indicate the 1:1 relationship, and black lines show ordinary least-squares fits. Pearson’s r and the mean standardized-minus-raw difference (Δmean, percentage points) are shown.”

(R2-R7) In Figure 2b, check the y-axis label; the text reports mg/kg, but the axis shows g/kg, which needs correction.

We thank the reviewer for identifying this unit discrepancy. We corrected the y-axis label in Figure 2b from g/kg to mg/kg so that it matches the units reported in the text.

(R2-R8) In the Discussion, rephrase the sentence “This indicates that NuRE is a conservative trait…” to avoid repetition with the Results summary, for example, “This finding highlights the conservative nature of NuRE.”

We thank the reviewer for this helpful wording suggestion. We have rephrased the sentence to avoid repetition.

eLife Assessment

Dohi et al. asked what role the dorsal hippocampus and medial prefrontal cortex play during different temporal epochs of a memory-guided navigation task, a long-standing question for neuroscientists studying hippocampal-prefrontal contributions to working memory. This useful study used a delayed, cue-guided T-maze task in mice and reported impaired choice accuracy when silencing occurred early in the central-arm run but not during the delay. However, the evidence for the study's claim is incomplete in its current form: the silencing windows are not duration-matched across epochs, key negative findings rest on three to four mice without power analysis or reported effect sizes, no non-mnemonic control task distinguishes disrupted memory-guided behavior from a general action-selection deficit, and no neural recordings accompany the causal manipulations to verify the manipulations' assumed mechanistic effects. The reported perseveration also reflects an increased directional bias rather than repetition of the previous choice, and the language should be revised accordingly.

Reviewer #1 (Public review):

Summary:

In this study, the authors trained mice to perform a memory-guided navigation task, in which they must navigate to a previously cued arm after a delay period. They optogenetically inhibited the dorsal hippocampus or mPFC (targeting PL) in different task epochs. They found that for both regions, inactivating at the beginning of the navigation epoch impaired performance and induced mice to revert to habitual side biases. Inactivating during other epochs, including a delay period before the navigation phase, had little or no impact on behavior. The relationship between trial duration and behavioral performance was differentially impacted by hippocampal and mPFC inactivation, suggesting that the nature of the deficits was somewhat different.

Strengths:

The effects of perturbations are robust across animals and generally convincing. The lack of effect at some task epochs serves as a nice internal control. The finding that hippocampus and mPFC inactivation produced subtly different effects is interesting.

Weaknesses:

The simplicity of the behavior makes it difficult to resolve how exactly the hippocampus and mPFC contribute to working memory. Also, the language does not always reflect the trends in the data: the authors claim that optogenetic perturbations cause mice to repeat previous choices, but the data show that perturbations increase the likelihood of choosing a preferred side (which is left for most mice). A side bias is not the same as choice repetition. This has implications for interpreting the nature of the behavioral effects.

Reviewer #2 (Public review):

Summary:

The study uses transient optogenetic silencing of the dorsal hippocampus or prefrontal cortex in mice using a delayed response task in a T-maze, with a temporal delay of 1s after a visual cue, followed by a central stem run period before choice execution. Silencing of either the dorsal hippocampus or the dorsal prefrontal cortex is executed for varying time periods during the stem/ central arm running epoch or the 1s temporal delay epoch by targeting either PV+ or Dlx interneurons in a block-wise or random-trial design. The main result reported is that silencing of either region during long periods of stem running impaired choice behavior, and silencing during the temporal delay period did not have an effect.

Strengths:

The major strength of the study is using the optogenetic silencing strategy to target different temporal periods of the task.

Weaknesses:

(1) A major weakness of the study is the lack of a balanced design with equal time periods of silencing during the stem running period and temporal delay period in many of the animals, which precludes any conclusion about distinct functional roles of the regions during these two phases of the task. The central question of this study is not new, with many previous studies investigating distinct and overlapping roles of hippocampus and prefrontal cortex in spatial working memory tasks and memory-guided navigation, using inactivation of one or both regions, crossed inactivation approaches, as well as targeting direct and indirect connections between the regions (PMIDs: 20074655, 9030646, 17045348, 30179661, 27511010, 10491611, 26017312, etc.), in addition to several physiology studies. A key extension for the current study would have been to show a distinction between roles in the temporal delay period after the cue and the stem-running working memory period. However, the inactivation period during stem running shows effects only for long inactivation periods, 2s initial periods and later ~1.6s periods (run after 0.8s, >2/3 total running periods), whereas the temporal delay period inactivation is 1s for the large majority of animals, which is a clear mismatch in inactivation periods, obviating this conclusion of distinction.

(2) It is not clarified why such short delay periods were used compared to long periods of ~10s in T-maze spatial alternation tasks with delay, and whether the temporal delay period of 1 sec is strictly distinct from the spatiotemporal delay period during stem running in terms of short-term memory function. The choice of time windows for inactivation needs to be better justified, which currently appears to be rather random (2s initial running period, run after 0.8s, run after 1.6s; for an average reported running period of ~2.4-2.5s). The ideal design clearly would have been to use a 2s temporal delay period so that the inactivation time in this epoch matched the initial 2s run period. Only a subset of 4 animals were run with a longer temporal delay period, and too with only with hippocampal inactivation (Figure 4d). The main conclusion of distinction between temporal delay and stem running delay periods is therefore not adequately tested for the prefrontal cortex, and the statistics in terms of number of animals for this important control for hippocampal inactivation are also not comparable to the main experiment.

(3) The mixture of PV-Cre animals (5 animals), Dlx targeting (2 animals), and one WT animal is also suggestive of a fragmented approach, and inactivation efficacy cannot be assumed to be similar for different animals. Importantly, there is no physiological evidence for confirmation of suppression in the optogenetic experiments, even in exemplar animals.

Reviewer #3 (Public review):

The authors sought to determine when the dorsal hippocampus and mPFC are causally required during a delayed spatial working memory task. Using temporally precise optogenetic silencing in mice performing a delayed cue-guided T-maze task, they tested the effects of transient perturbations during distinct behavioral epochs. Contrary to the common view that these regions are primarily required during the delay period to maintain working memory representations, they report that silencing during the delay had little effect on performance, whereas perturbation during the early phase of central-arm traversal consistently impaired performance. The authors conclude that hippocampal and prefrontal contributions to memory-guided behavior are dynamically engaged during active navigation rather than passive maintenance of information.

The study has several strengths. The behavioral paradigm is carefully designed to dissociate cue, delay, and movement epochs, allowing temporally specific causal manipulations. The systematic comparison of multiple task epochs represents a major strength and provides compelling evidence that the behavioral effects of perturbation are epoch-dependent. The authors also include several important controls, including stimulation during multiple task phases, a longer-delay condition to dissociate task epoch from elapsed time since cue presentation, and analyses of movement trajectories and perseverative behavior that provide additional insight into the nature of the behavioral deficits. Together, these experiments convincingly demonstrate that transient dorsal hippocampal and mPFC perturbations have markedly different behavioral consequences depending on when they occur within a trial.

The evidence is generally solid and supports the primary finding that perturbations during early navigation produce larger impairments than perturbations during the delay period. However, some aspects of the broader interpretation are less well supported. Most notably, the study lacks a non-memory control task, such as a visually guided version of the maze, making it difficult to determine whether the observed deficits specifically reflect disruption of memory-guided behavior or more general impairments in action selection, behavioral flexibility, or movement planning. The observed increase in perseverative responding and delayed commitment to a turn are consistent with either interpretation. In addition, several experimental conditions rely on relatively small numbers of animals, limiting confidence in some negative findings, particularly for the longer-delay and later-run manipulations. Finally, while the Discussion proposes that hippocampal-prefrontal circuits become engaged during the transformation of stored information into action, this mechanistic interpretation remains speculative because no neural recordings accompany the causal manipulations.

Overall, the authors achieve their primary aim of demonstrating that the behavioral consequences of dorsal hippocampal and mPFC silencing depend strongly on task epoch. The data convincingly support the conclusion that these structures are more vulnerable to perturbation during early navigation than during the brief delay period used in this task. The broader conclusion that these findings redefine when hippocampal-prefrontal circuits support working memory should be interpreted more cautiously, as alternative explanations involving action selection or behavioral state remain plausible in the absence of additional control tasks.

The findings are potentially important because they challenge the common assumption that hippocampal and prefrontal contributions to delayed-response tasks are centered on delay-period maintenance. Instead, the work supports the idea that these circuits may be recruited when remembered information is translated into goal-directed behavior. This framework is broadly consistent with recent distributed models of working memory and provides an interesting perspective that may help reconcile previous studies reporting effects during different task phases. The behavioral paradigm and temporally precise perturbation approach should also be useful for future studies aimed at dissecting the dynamic contributions of hippocampal-prefrontal circuits during memory-guided behavior.

Author response:

On the eLife Assessment. We appreciate the assessment’s recognition that this study addresses a long-standing question concerning hippocampal and prefrontal contributions to working memory. We think the broader significance lies in constraining how causal manipulations in working-memory tasks are interpreted. Working memory encompasses many processes distributed across a trial and showing that a region is required for a delayed-response task does not establish when its contribution is necessary. The observation that hippocampus and mPFC are required while navigating to a goal, but not during stationary delay, challenges a common assumption and, in our opinion, has implications across the broader field of working-memory research.

We agree that the original manuscript did not adequately report effect sizes or convey the uncertainty associated with some smaller samples. However, the dataset does include duration-matched stationary and running conditions, including a hippocampal long-delay control matched to early-running stimulation in both duration and elapsed time after cue onset. The new effect-size and within-animal analyses support a robust hippocampal epoch difference, while the corresponding mPFC comparison is less precisely estimated and should be interpreted more cautiously.

We therefore think the central finding remains well supported: hippocampal function, and potentially mPFC function, is required during the active navigation period of this memory-guided task but not detectably during the stationary delay. This does not establish the specific computation disrupted during running. Neural recordings would certainly provide further insight into the underlying mechanism, but their absence does not detract from the value of the behavioral result itself.

Reviewer #1 (Public review):

The simplicity of the behavior makes it difficult to resolve how exactly the hippocampus and mPFC contribute to working memory.

The task was designed to combine the temporal precision of cue-based delayed-response paradigms with the behavioral richness of freely moving navigation. Few tasks combine a fixed cue-presentation period, an explicit delay, and a subsequent navigation phase involving extended running. This structure creates well-defined behavioral epochs that can be targeted with temporally precise perturbations, allowing us to ask when hippocampal and mPFC contributions are required within an ongoing memory-guided behavior. How these regions contribute is the harder question, and one we are pursuing next. Identifying when perturbations disrupt behavior is an important step toward understanding how these regions support memory-guided navigation

Also, the language does not always reflect the trends in the data: the authors claim that optogenetic perturbations cause mice to repeat previous choices, but the data show that perturbations increase the likelihood of choosing a preferred side (which is left for most mice). A side bias is not the same as choice repetition. This has implications for interpreting the nature of the behavioral effects.

We agree that our results do not clearly distinguish a directional bias from a tendency to repeat the previous choice. To examine whether mice consistently favored a particular direction, we compared their side preferences during silencing across sessions. Mice generally favored the same side across silencing conditions, although some switched direction in individual sessions (Author response image 1a). Within sessions, the preferred side was maintained from no-stimulation to stimulation trials in 13 of 19 cases and reversed in six (Author response image 1b). These observations are consistent with a directional preference that can sometimes reverse during stimulation, and cannot be disambiguated from perseveration. In the revision, we will describe the effect as increased directional bias and revise the language concerning choice repetition and perseveration throughout the manuscript.

Author response image 1.

Silencing increases directional bias. (a) Fraction of choices made to the right in each session, for every mouse (rows) and each silencing condition (symbols). Open symbols, no-stimulation trials; filled symbols, stimulation trials from the same session; blue and red denote a left or right preference during silencing. Filled symbols falling predominantly on the same side of 0.5 within a row indicate that a mouse generally favored the same direction across silencing conditions, although some mice switched direction. One session per mouse and condition, hippocampal silencing only; T2 and T6 did not perform the 0.8 s condition. (b) The same sessions expressed as signed bias, from no stimulation to silencing. Black lines mark the six sessions in which the preferred side reversed; grey lines the thirteen in which it was maintained.

Reviewer #2 (Public review):

A major weakness of the study is the lack of a balanced design with equal time periods of silencing during the stem running period and temporal delay period in many of the animals, which precludes any conclusion about distinct functional roles of the regions during these two phases of the task. The main conclusion of distinction between temporal delay and stem running delay periods is therefore not adequately tested for the prefrontal cortex, and the statistics in terms of number of animals for this important control for hippocampal inactivation are also not comparable to the main experiment.

We agree that matching stimulation duration is an essential control and recognize that the relevant comparisons and statistics were not sufficiently clear in the original manuscript. Four hippocampal conditions used closely matched stimulation durations of 2 s: Cue+Delay, long delay, early running, and running with a 0.8 s onset (Author response image 2a). Crucially, the long-delay control matched both stimulation duration and elapsed time after cue onset to the early-run condition, while the mouse remained stationary.

Author response image 2b–c shows the estimated impairment and its 95% confidence interval for each condition. In the hippocampal experiments, the duration-matched stationary conditions showed effects close to zero, whereas the running conditions showed large impairments. Despite the smaller sample, the upper confidence limit for the long-delay impairment was approximately 10 percentage points, substantially below the observed early-running impairment. These estimates establish that despite the smaller sample, the data support a lack of effect compared to early running.

Author response image 2.

Duration-matched stimulation produces different behavioral effects across task epochs. (a) Stimulation timing relative to cue onset. Numbers within bars indicate calculated median stimulation duration in seconds; black ticks indicate door opening. Bold labels identify conditions with 2 s stimulation. (b-c) Mean impairment in choice accuracy for hippocampal and mPFC manipulations. Impairment is accuracy during baseline minus accuracy with stimulation, in percentage points. Error bars show 95% confidence intervals across animals; numbers indicate mice. Open circles denote single-animal observations, and arrows indicate confidence intervals extending beyond the plotted range.

For mPFC, the duration-matched Cue+Delay condition likewise showed an effect close to zero, whereas early-running stimulation produced substantial impairment. However, the long-delay condition included only one mouse. The later-running effects in both regions were also less precisely estimated. We will distinguish these limitations from the more informative stationary-condition results.

To directly test whether the duration-matched effects differed across epochs, we next compared impairment within the same mice, including only animals tested in both conditions (Author response image 3). For the hippocampus, every mouse showed greater impairment during early running than during either duration-matched stationary condition, and the confidence intervals for both paired differences excluded zero. These within-animal comparisons support an epoch-dependent effect that cannot be explained by stimulation duration alone. The mPFC comparison showed the same direction of effect, although the confidence interval for the Cue+Delay versus running difference narrowly included zero. We will therefore distinguish the stronger evidence for the hippocampal epoch difference from the more limited evidence for mPFC.

Author response image 3.

Within-animal comparisons of duration-matched stimulation effects. (a–b) Impairment during Cue+Delay or long-delay stimulation compared with early-running stimulation for hippocampal (a) and mPFC (b) manipulations. Points represent individual mice, lines connect observations from the same mouse, and black bars indicate mean. Annotations report the mean paired difference in impairment (running minus stationary), and its 95% confidence interval calculated using the t distribution. Positive differences indicate greater impairment during running. The single-mouse mPFC long-delay comparison is descriptive. Blue indicates stationary epochs and orange indicates running.

The central question of this study is not new, with many previous studies investigating distinct and overlapping roles of hippocampus and prefrontal cortex in spatial working memory tasks and memory-guided navigation, using inactivation of one or both regions, crossed inactivation approaches, as well as targeting direct and indirect connections between the regions (PMIDs: 20074655, 9030646, 17045348, 30179661, 27511010, 10491611, 26017312, etc.), in addition to several physiology studies.

We agree that hippocampal and prefrontal contributions to spatial working memory have been extensively studied. That’s precisely why we find these results impactful when placed in the rich context of the field. The requirement for these regions in delayed working memory tasks has often been interpreted in terms of their contributions during the delay period. However, a requirement during a delay-based task does not itself demonstrate a requirement during the delay. Previous manipulations have not isolated delay periods of waiting from the subsequent navigation within a trial.

Our experiments extend this work by separately targeting cue presentation, the delay, and different portions of navigation within the same task. This allows us to test whether the behavioral consequences of perturbation depend on the particular epoch in which it occurs. This distinction is important: knowing that a region is required for a memory-guided task does not establish when its contribution is needed. Identifying those periods constrains how we interpret the deficits produced by longer-lasting inactivation. We believe that this is an important result that should be considered when interpreting these broader findings. We will ensure that the appropriate literature and discussion are included in the revision.

It is not clarified why such short delay periods were used compared to long periods of ~10s in T-maze spatial alternation tasks with delay, and whether the temporal delay period of 1 sec is strictly distinct from the spatiotemporal delay period during stem running in terms of short-term memory function.

The 1 s delay was chosen to maintain reliable task performance, as some mice could not perform the task with longer delays. Indeed, one reason the longer-delay condition includes fewer animals is that two mice could not perform reliably with the 3 s delay (one additional mouse was not tested in this condition). Delays on this timescale have also been used in rodent cued delayed-response tasks, including a 0.5 s delay in Kopec et al. (2015), a 1.3 s delay in Guo et al. (2014), and a 1.2 s delay in Inagaki et al. (2019). Like these tasks, our paradigm requires mice to remember an externally presented cue specifying the upcoming response, rather than their own previous arm choice as in spatial alternation. It therefore combines spatial navigation with a cued delayed-response requirement, and the delay durations tolerated in alternation tasks are not necessarily directly comparable. We will clarify this rationale in the manuscript.

We agree that the stationary delay and the subsequent run both require retention of information after cue offset. Our experiments distinguish these behavioral epochs, but do not establish that they involve separate short-term memory processes. The different effects of perturbation suggest that the contribution of these regions changes as the animal moves from waiting to navigating. Determining what accounts for this change is an important direction for future work.

The choice of time windows for inactivation needs to be better justified, which currently appears to be rather random (2s initial running period, run after 0.8s, run after 1.6s; for an average reported running period of ~2.4-2.5s).

We sought to target different portions of the central-arm run. Given the typical traversal time of approximately 2.4–2.5 s, stimulation onsets at 0, 0.8, and 1.6 s sampled the beginning, middle, and later portions of the run. Our setup allowed precise control of stimulation timing, and, as shown in Figure 4b, these onset times correspond approximately to the start, middle, and end of the central arm. Each condition used a nominal 2 s stimulation window, truncated if the mouse reached the choice point sooner. The windows therefore overlap, with the later-onset condition generally producing shorter stimulation. We will clarify this rationale and the distinction between stimulation onset and duration in the revised manuscript.

The mixture of PV-Cre animals (5 animals), Dlx targeting (2 animals), and one WT animal is also suggestive of a fragmented approach, and inactivation efficacy cannot be assumed to be similar for different animals. Importantly, there is no physiological evidence for confirmation of suppression in the optogenetic experiments, even in exemplar animals.

The Dlx animals were included to improve regional specificity through local viral expression and to test whether the behavioral effects were consistent across targeting approaches. Both approaches produced comparable impairments during running, supporting their inclusion in the same analysis. We will clarify this rationale in the manuscript.

Optogenetic activation of inhibitory interneurons is an established approach for suppressing local principal-cell activity, with physiological validation in previous studies (Guo et al., 2014; Li et al., 2019, Zutshi et al., 2022). In our experiments, running-period stimulation produced robust behavioral impairments that were consistent across animals and targeting approaches. Furthermore, comparisons across epochs were performed within animals, using the same preparation and stimulation parameters. Differences in efficacy between animals therefore cannot readily account for the observed epoch dependence. Although direct recordings would establish the magnitude and spatial extent of suppression in our preparation, the central behavioral finding is supported by these within-animal comparisons.

Reviewer #3 (Public review):

The findings are potentially important because they challenge the common assumption that hippocampal and prefrontal contributions to delayed-response tasks are centered on delay-period maintenance.

We thank the reviewer for describing our findings as “potentially important” and for highlighting their implications for how hippocampal and prefrontal contributions to delayed-response tasks are understood. We appreciate the constructive suggestions and address the public comments below.

Most notably, the study lacks a non-memory control task, such as a visually guided version of the maze, making it difficult to determine whether the observed deficits specifically reflect disruption of memory-guided behavior or more general impairments in action selection, behavioral flexibility, or movement planning. The observed increase in perseverative responding and delayed commitment to a turn are consistent with either interpretation.

We agree that leaving the cue on throughout the trial would provide an important control for distinguishing memory-specific effects from broader effects on action selection or movement planning. The senior author is currently setting up a new laboratory, so implementing this control may take some time. We hope to include it in the revised manuscript.

The running-period deficit indicates a disruption of processes that enable the animal to act on a remembered cue. Whether this reflects disruption of memory itself, movement planning, or another component of translating the cue into a choice requires further clarification but does not detract from the observed dependence on task epoch. Uncertainty about the mechanism of the running-period deficit also does not change the observation that the same manipulation produced no detectable impairment during the stationary delay, when the cue was absent and still had to be remembered. This will be clearly discussed in the revision.

In addition, several experimental conditions rely on relatively small numbers of animals, limiting confidence in some negative findings, particularly for the longer-delay and later-run manipulations.

We agree that small sample sizes limit the interpretation of some negative findings. We now report animal-level effect estimates and 95% confidence intervals for each condition (Author response image 2b–c; Author response table 1).

Of the nine conditions with no detectable impairment and more than one mouse, seven had confidence intervals that excluded effects as large as the observed mean early-running impairment in the same region. This included the hippocampal long-delay condition, despite its smaller sample. These results argue against similarly large impairments in these conditions, although smaller effects remain possible. The two later-run conditions remained too uncertain to exclude such impairments. These and the two single-animal conditions are marked in Author response table 1 and will be interpreted cautiously.

Author response table 1.

Animal-level impairment estimates and uncertainty

Finally, while the Discussion proposes that hippocampal-prefrontal circuits become engaged during the transformation of stored information into action, this mechanistic interpretation remains speculative because no neural recordings accompany the causal manipulations.

We will clarify in the Discussion that the proposed transformation of stored information into action remains speculative. Nevertheless, we believe this is an exciting possibility raised by our findings that warrants further investigation. Neural recordings would help test this interpretation but are beyond the scope of the current paper. We plan to explore this question in future work.

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eLife Assessment

Using sci-L3-Strand-seq, this study shows genome-wide, single-cell evidence that DSBs triggered by CRSIPR/Cas9 are frequently resolved through sister chromatid exchange (SCE), which is undetectable with conventional whole genome sequencing approaches. This important work provides helpful metrics quantifying the occurrence of SCE events at targeted and repetitive genomic loci that are of particular interest to those working in gene editing, DNA repair, genome instability, or repetitive genomic loci. The analysis of reciprocal daughter-cell pairs provides compelling evidence for SCE events, providing evidence consistent with CDK1-TTF2-TRAIP mediated cell-cycle regulated CMG helicase disassembly and fork cleavage at unreplicated regions.

Reviewer #1 (Public review):

[Editors' note: this version has been assessed by the Reviewing Editor without further input from the original reviewers. The authors have addressed the comments raised in the previous round of review.]

Summary:

This manuscript uses sci-L3-Strand-seq to map sister chromatid exchange events following CRISPR/Cas9-induced DNA damage. Because exchanges between identical sister chromatids are largely invisible to conventional sequencing, the study addresses an important blind spot in the assessment of genome editing outcomes. The authors compare single-locus Cas9 cleavage, simultaneous targeting of 237 repetitive genomic sites, and Cas9 nickase variants. They further use reciprocal daughter-cell pair analysis to ask whether Cas9-associated SCEs are copy-neutral or linked to larger structural alterations. Overall, this is a valuable study that introduces an important additional layer to the analysis of CRISPR/Cas9 repair outcomes. The central finding that Cas9-induced DSBs can trigger frequent local SCE is well supported and likely to be of broad interest.

Strengths:

The major strength of the manuscript is the application of a strand-resolved, single-cell method to a question that is difficult to address with standard genome sequencing. The evidence that a single Cas9-induced DSB can trigger strong local SCE is compelling in concept and supported by multiple guide RNAs targeting distinct loci. The reported on-target SCE frequencies, reaching up to 41%, suggest that inter-sister exchange is a substantial and underappreciated outcome of Cas9 cleavage.

Of particular interest is the comparison between single-site and multi-site targeting. The finding that 237 programmed Cas9 targets produce only mild bulk enrichment of on-target SCE but stronger enrichment in a subpopulation of cells with elevated SCE burden is interesting and may have wider biological implications, particularly if the findings extend beyond Cas9-induced SCE to spontaneous SCEs.

The reciprocal daughter-cell pair analysis is another notable feature of the study. The observation that some Cas9-associated SCEs are accompanied by structural alterations could challenge the assumption that SCE after a programmed break reflects error-free homologous recombination.

Reviewer #2 (Public review):

Summary:

In this short paper, a clever single-cell Strand-seq method was used to study the number and location of sister chromatid exchange events (SCEs) in cells after CRISPR/Cas9-induced DNA double-strand breaks (DSBs). Unique as well as multiple genomic loci were targeted. Cas9-induced cuts at unique genomic locations led to statistical enrichment of SCEs at the target site, whereas Cas9 targeted at repetitive targets revealed only mild enrichment of on-target SCEs unless analysis was restricted to a subset of cells with >8 SCEs per cell. Interestingly, reciprocal daughter-cell pair analysis revealed large-scale structural alterations on some chromosomes. Whereas disruption of DNA repair genes, including LIG3, LIG4, XRCC1, and XRCC4, did not measurably alter SCE frequency per cell within 24 hrs, consistent with delayed functional loss following editing and selection against essential genes. Together, these findings demonstrate that Cas9-induced DSBs are potent local triggers of SCE at unique loci and can be associated with structural alterations, highlighting the influence of lesion type and genomic context on recombination outcomes during genome editing.

Strengths:

The data in this paper represent a very rich resource of how parental DNA template strands are distributed in paired daughter cells after various treatments. Abnormalities observed in only one of such paired daughter cells provide a novel and exciting approach to study mechanisms of DNA instability and DNA repair at a genome-wide level in general and following Cas9-induced DSB in particular.

Weaknesses:

The effect of Cas9-induced DSBs in the cells that are used will depend on the cell cycle stage of the cells that are targeted, as well as the number of times cuts are made. The latter could happen before, during, and after DNA repair reactions on one or both alleles in a diploid cell. As a result, it is very difficult to extrapolate the mechanisms of DNA instability and DNA repair from the observed genomic rearrangements. Novel approaches are needed to limit the number and timing of Cas9-induced breaks to overcome some of these limitations.

Reviewer #3 (Public review):

Chovanec and Yin used their newly developed sci-L3-Strand-seq powerful method to characterize SCE after Cas9 cleavage in a human cell line, using either a single target site or an element repeated 237 times in the genome. SCE are often neglected in DNA repair analyses since they are « genetically silent ». Interestingly, the authors found enrichment of SCE at unique Cas9 sites, but only a modest enrichment of SCE when Cas9 targets 237 sites in the genome. The genetic control of SCE formation at Cas9 sites is not deliberately addressed in this paper. However, the authors found that targeted SCE seem to be enriched in a subpopulation of cells, particularly « permissive » for SCE, but the determinants of such a population are unknown. Finally, the power of the sci-L3-Strand-seq allowed the authors to characterize a specific type of SCE based on the analysis of reciprocal daughter-cell pairs' genomes that is associated with a specific type of chromosomal rearrangement compatible with the ones observed in HR defective BRCA1/2 deficient cells.

Author response:

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

eLife Assessment

Using sci-L3-Strand-seq, this study shows genome-wide, single-cell evidence that DSBs triggered by CRISPR/Cas9 are frequently resolved through sister chromatid exchange (SCE), which is undetectable with conventional whole-genome sequencing approaches. This important work provides helpful metrics quantifying the occurrence of SCE events at targeted and repetitive genomic loci that are of particular interest to those working in gene editing, DNA repair, genome instability, or repetitive genomic loci. However, the evidence supporting the proposed involvement of under-replicated region/replication termination-zone resolution and TRAIP/URR-like pathways is currently incomplete and could be strengthened with an increased number of reciprocal daughter-cell pairs and by genetic or molecular perturbation, or alternatively, this can be addressed by changing the discussion.

We appreciate the editor’s and the reviewers’ recognition of Cas9-induced SCE as an important previously invisible repair outcome and of RDCP analysis as a notable feature of the study. As proposed, we incorporated the two recent Science studies and now tone down the Discussion of our RDCP observations as consistent with, rather than definitive evidence for, the TRAIP-dependent pathway. We also detail how our single-cell genomic observations complement and extend these two studies in terms of the biological significance of the CDK1-TTF2-TRAIP axis.

Specifically, these changes are in:

Discussion. We changed

“Two recent studies revealed how the CDK1-TTF2-TRAIP axis is cell-cycle regulated to trigger mitotic CMG helicase disassembly and fork cleavage: one study showed a two-fold SCE reduction in mouse ES cells (Fujisawa and Labib, 2026), while the other showed that disrupting the TRAIP-TTF2 interaction reduced common fragile site deletions (Can et al., 2026). Our observation of the "WWC-or-WCC/deletion pair" signature in wild-type cells provides, to our knowledge, the first genetic evidence of linking a deletion with SCE and revealing both W and C unreplicated template strands present in the reciprocal daughter cell, consistent with this mechanism at single-cell genomic resolution (illustrated in Fig.3), although this is limited by the observation of only one RDCP.”

While each study highlights the biological significance of the CDK1-TTF2-TRAIP axis individually for SCE and deletions, we show the coupling relationship (and further evidence of unreplicated template strands) in reciprocal daughter cells.

Fig.3. Title and legends. We changed

“Haplotype-aware analysis of observed RDCP (Pair 4, chr1) shows SV patterns at the SCE junctions consistent with the predicted RDCP signature of SCE mediated by URRs or replication termination zones (green shaded area), although the lagging strands, rather than the leading strands, must be resolved to generate these mitotic breaks.”

Reviewer #1 (Public review):

Summary:

This manuscript uses sci-L3-Strand-seq to map sister chromatid exchange events following CRISPR/Cas9-induced DNA damage. Because exchanges between identical sister chromatids are largely invisible to conventional sequencing, the study addresses an important blind spot in the assessment of genome editing outcomes. The authors compare single-locus Cas9 cleavage, simultaneous targeting of 237 repetitive genomic sites, and Cas9 nickase variants. They further use reciprocal daughter-cell pair analysis to ask whether Cas9-associated SCEs are copy-neutral or linked to larger structural alterations. Overall, this is a valuable study that introduces an important additional layer to the analysis of CRISPR/Cas9 repair outcomes. The central finding that Cas9-induced DSBs can trigger frequent local SCE is well supported and likely to be of broad interest. The evidence for structural complexity associated with some induced SCEs is intriguing, but the mechanistic interpretation should either be tested directly or presented more cautiously.

Strengths:

The major strength of the manuscript is the application of a strand-resolved, single-cell method to a question that is difficult to address with standard genome sequencing. The evidence that a single Cas9induced DSB can trigger strong local SCE is compelling in concept and supported by multiple guide RNAs targeting distinct loci. The reported on-target SCE frequencies, reaching up to 41%, suggest that inter-sister exchange is a substantial and underappreciated outcome of Cas9 cleavage.

Of particular interest is the comparison between single-site and multi-site targeting. The finding that 237 programmed Cas9 targets produce only mild bulk enrichment of on-target SCE but stronger enrichment in a subpopulation of cells with elevated SCE burden is interesting and may have wider biological implications, particularly if the findings extend beyond Cas9-induced SCE to spontaneous SCEs. Given that potential, the current manuscript would benefit greatly from any experiments characterizing this sub-population: are these cells in a particular cell cycle state, experiencing changes in gene expression, or do they have other unique biological properties?

The reciprocal daughter-cell pair analysis is another notable feature of the study. The observation that some Cas9-associated SCEs are accompanied by structural alterations could challenge the assumption that SCE after a programmed break reflects error-free homologous recombination.

Thank you very much for this assessment.

Weaknesses:

The number of informative RDCPs is limited, and the mechanistic interpretation of the "WWC-orWCC/deletion" signature is more suggestive than definitive. In particular, the manuscript invokes (even though only in the Discussion section) URR or replication-termination-zone resolution and discusses TRAIP-dependent CMG unloading, nuclease cleavage, and polymerase theta-mediated joining, but these pathway components are not directly tested herein. A more conservative conclusion that some Cas9-associated SCEs coincide with structural alterations is more appropriate, particularly in the Discussion and Conclusion. For example, the statement that this work provides "direct genetic evidence" for a URR-type mechanism is overstated unless supported by additional experiments or a more extensive analysis of alternative models. Similarly, while the authors explain the limitations of acute Cas9 disruption of LIG3, LIG4, XRCC1, and XRCC4, the manuscript should clarify what biological questions this experiment can and cannot answer.

Please see response to the eLife Assessment as this is a common point raised by multiple reviewers.

Additionally, we clarified what the DNA repair gene targeting experiment can and cannot answer (delayed protein loss, essential-gene selection) by adding the following text in the “Disruption of DNA repair genes at the cut site did not measurably alter SCE frequency per cell” section:

“One additional complication is that, although Cas9 RNP achieves >90% knockout efficiency in bulk assays and is therefore used as a substitute for siRNA, sorting BrdU-labeled cells in the subsequent G1 enriches for cells that escaped frameshift editing, particularly for essential genes; thus, 100% knockout in 90% of cells is not equivalent to 90% knockdown in every cell, representing a unique challenge for single-cell assays.”

Reviewer #1 (Recommendations for the authors):

(1) Temper the mechanistic claims about URR/TRAIP-type resolution.

The RDCP data support the conclusion that some Cas9-associated SCEs are accompanied by structural alterations and may arise through non-classical mechanisms. However, claims about TRAIPdependent CMG unloading, URR resolution, or polymerase theta-mediated joining should be framed as a model unless directly tested.

We cited mechanistic dissection of the CDK1-TTF-2-TRAIP axis, which was published since the review of the paper. While each study highlights the biological significance of the CDK1-TTF2-TRAIP axis individually for SCE and deletions, we show the coupling relationship (and further evidence of unreplicated template strands) in reciprocal daughter cells but qualified that this observation is in only one RDCP. We further tempered our claims by changing “direct evidence” to “consistent with” as we did not perturb genes involved in these processes.

(2) Clarify the impact of the small RDCP sample size.

The manuscript would be strengthened by explicitly stating how many total RDCPs were analyzed, how many SCE events were informative, and how much confidence can be placed in the estimated fraction of SCEs associated with SVs. A short table summarizing RDCP counts, SCE counts, copy-neutral events, and SV-associated events would be helpful.

A total of 15 RDCPs were recovered from close to 4,000 single cells analyzed across all conditions. We added Tab.S3 detailing SCEs in all 15 RDCPs in addition to SCE and SV breakdown in Tab.S2 (originally Tab.S1). The new Tab.S3 is cited in the “RDCP analysis reveals large-scale SVs on chromosomes with induced SCE, as well as structural alterations at Cas9-induced SCE junctions” section.

(3) Provide more detail on the "rescued" SCE calls.

Because the central conclusions rely on SCE detection, the criteria for breakpoint R-based calls versus rescued calls should be explained clearly in the main text or methods. It would be useful to know how sensitive the main conclusions are to the inclusion or exclusion of rescued calls. Is this laid out in greater detail in an additional manuscript?

We previously included an “On-target SCE identification” section in the Methods, where we described in detail the rescue of on-target SCEs missed by the initial breakpoint R calls. We also depicted calls and calls+rescues for all the conditions in Fig.S1B.

We agree with the reviewer and now expanded the description of rescued SCE calls in the main text (under the “A single Cas9 DSB induces potent local SCE” section). In brief, 50-92% of SCEs (typically >70%) across the four single-targeting sites were directly called rather than rescued, with the exception of LIG4, where only 30% were direct calls. This is because LIG4 is located only 6 Mb from the telomere and is therefore particularly prone to missed breakpointR calls in low-coverage cells. On-target rescue at individual sites is self-contained in this manuscript because our lab primarily focuses on spontaneous SCE, for which there are no expected SCE sites. However, the rescue methodology was previously implemented in the original development of sci-L3-Strand-seq to identify SCEs at centromeres.

(4) Clarify the biological interpretation of the repetitive-target enrichment.

The high-SCE subset analysis is interesting, but the manuscript should explain whether these cells have evidence of higher RNP uptake, altered cell-cycle state, greater DNA damage, or lower sequencing quality. If these possibilities cannot be distinguished, the text should state this clearly.

We agree with the reviewer. The high SCE subset does not have lower sequencing quality by coverage or background (0.3% coverage for high-SCE vs. 0.28% coverage overall, and 3% background for both high-SCE and overall). However, our current data do not allow us to distinguish among biological explanations for the elevated SCE. The original manuscript acknowledged this limitation (“Whether this reflects a cell-cycle state more permissive to both cutting and recombination, or stochastic variation in RNP uptake coupled with a recombination-prone chromatin environment, remains to be determined.”). To make this limitation more explicit and to address the possibility of sequencing quality raised by the reviewer, we have revised the text as follows: “The high-SCE subset did not show evidence of lower sequencing quality, based on either sequencing coverage (p=0.17) or background SCE levels (p=0.13). However, we cannot distinguish whether the elevated on-target SCE reflects a cell-cycle state more permissive to both cutting and recombination, or stochastic variation in RNP uptake coupled with a recombination-prone chromatin environment.”

This question may be better explored by future co-assays with sci-L3-Strand-seq; currently we cannot enrich for cells with high SCEs to characterize the molecular features of this subset of the cells using other omics approaches.

(5) Reconsider the framing of the DNA repair gene targeting experiment.

The current data do not strongly test whether LIG3, LIG4, XRCC1, or XRCC4 regulate Cas9-induced SCE, because functional protein loss is delayed and essential-gene targeting introduces selection. This section may be better framed as a negative/control observation rather than as a pathway analysis.

We agree and please refer to Public Reviews for a single-cell assay-specific explanation.

(6) Consider including some additional control experiments, for example, Cas9 without sgRNA, nontargeting sgRNA, or mock-transfected cells to make sure that some phenotypes (for example, cell-cycle arrest) directly result from DNA cleavage rather than from the transfection procedure.

We thank the reviewer for this suggestion. We have carefully considered these additional controls but have chosen not to add further experiments. Our existing Cas9 nickase experiments provide a control that directly addresses whether the observed arrest is attributable to DSB formation rather than RNP delivery/transfection. Both the D10A and H840A Cas9 nickases were delivered under the same experimental conditions as wild-type Cas9, but neither produced the cell-cycle arrest observed following DSB induction by wild-type Cas9. Thus, these experiments control for Cas9 RNP delivery while altering the nature of the DNA lesion and support the interpretation that the observed arrest is associated specifically with Cas9-induced DSBs rather than the transfection procedure itself.

(7) Figure 1: the fonts should be increased. The majority of the labels are impossible to read in a printed copy of this manuscript.

We thank the review for pointing this out. We enlarged Fig.1 fonts.

(8) Figure 1C. The pileup plots should be described and interpreted in a clear way. In its present form, it is unclear how the interpretations and conclusions are made.

We added explanation of the pileup analysis immediately following mentioning the Fig.1C pileup: “We next examined … SCEs using genome-wide pileup analysis (Fig.1C, Fig.S1B), in which we plot the total number of SCEs detected across all single cells within each 1 Mb window.”

Reviewer #2 (Public review):

Summary:

In this short paper, a clever single-cell Strand-seq method was used to study the number and location of sister chromatid exchange events (SCEs) in cells after CRISPR/Cas9-induced DNA double-strand breaks (DSBs). Unique as well as multiple genomic loci were targeted. Cas9-induced cuts at unique genomic locations led to statistical enrichment of SCEs at the target site, whereas Cas9 targeted at repetitive targets revealed only mild enrichment of on-target SCEs unless analysis was restricted to a subset of cells with >8 SCEs per cell. Interestingly, reciprocal daughter-cell pair analysis revealed largescale structural alterations on some chromosomes. Whereas disruption of DNA repair genes, including LIG3, LIG4, XRCC1, and XRCC4, did not measurably alter SCE frequency per cell within 24 hrs, consistent with delayed functional loss following editing and selection against essential genes. Together, these findings demonstrate that Cas9-induced DSBs are potent local triggers of SCE at unique loci and can be associated with structural alterations, highlighting the influence of lesion type and genomic context on recombination outcomes during genome editing.

Strengths:

The data in this paper represent a very rich resource of how parental DNA template strands are distributed in paired daughter cells after various treatments. Abnormalities observed in only one of such paired daughter cells provide a novel and exciting approach to study mechanisms of DNA instability and DNA repair at a genome-wide level in general and following Cas9-induced DSB in particular.

Thank you very much for this assessment.

Weaknesses:

The effect of Cas9-induced DSBs in the cells that are used will depend on the cell cycle stage of the cells that are targeted, as well as the number of times cuts are made. The latter could happen before, during, and after DNA repair reactions on one or both alleles in a diploid cell. As a result, it is very difficult to extrapolate the mechanisms of DNA instability and DNA repair from the observed genomic rearrangements. Novel approaches are needed to limit the number and timing of Cas9-induced breaks to overcome some of these limitations. The language and logic in the paper can be improved, and some of the claims seem incorrect. For example, the abstract reads "A single Cas9 cut at a unique genomic locus led to strong local enrichment of SCE at the break site, reaching up to 41% in the same cell cycle and 17% in the subsequent division, indicating that DSB repair frequently engages non-local inter-sister repair." The evidence that only a single Cas9 cut was made is lacking (see my earlier comment); it is not clear how local enrichment or non-local inter-sister repair are defined.

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 also agree that novel approaches are needed to limit the number and timing of Cas9-induced breaks to overcome these limitations, perhaps by using vfCas9 but more importantly, if new approaches to turn off Cas9 are developed. We have added a brief discussion on this limitation (in the Limitation section) and the resulting constraints on extrapolating mechanisms of DNA instability and repair from the observed genomic rearrangements. We thank the reviewer for pointing out the distinction between “a single Cas9 cut” vs. "Cas9 targeting of a single genomic locus." We went through the manuscript and revised where cutting only once was implied. We also explicitly acknowledge the possibility of multiple rounds of cutting at the same sites.

We thank the reviewer for pointing out that “non-local repair” is a non-standard term. We use it operationally to distinguish repair confined to the broken chromatid (e.g., fill-in synthesis or end joining in cis) from repair involving exchange between sister chromatids. We have added a schematic (Fig. S1A) illustrating this distinction and cited this figure immediately before where we operationally defined SCE as a “reciprocal strand switch between sister chromatids, without implying a single mechanistic pathway.” This distinction is important because, particularly for two-ended Cas9 DSBs, an SCE-like outcome could potentially arise through either HR-mediated crossover or NHEJ of DNA ends across sister chromatids; the latter may involve different genetic requirements from classical NHEJ at least in end-tethering. We have revised the manuscript to define “non-local repair” explicitly at its first use.

Reviewer #2 (Recommendations for the authors):

References to relevant earlier studies using Strand-seq to study SCEs are missing (PMID: 27185886 and PMID: 29348659).

We thank the reviewer for pointing this out. We added these references in the 3rd paragraph of the Introduction where we briefly review Strand-seq methods.

Reviewer #3 (Public review):

Summary:

Chovanec and Yin used their newly developed sci-L3-Strand-seq powerful method to characterize SCE after Cas9 cleavage in a human cell line, using either a single target site or an element repeated 237 times in the genome. SCE are often neglected in DNA repair analyses since they are « genetically silent ». Interestingly, the authors found enrichment of SCE at unique Cas9 sites, but only a modest enrichment of SCE when Cas9 targets 237 sites in the genome. The genetic control of SCE formation at Cas9 sites is not deliberately addressed in this paper. However, the authors found that targeted SCE seem to be enriched in a subpopulation of cells, particularly « permissive » for SCE, but the determinants of such a population are unknown. Finally, the power of the sci-L3-Strand-seq allowed the authors to characterize a specific type of SCE based on the analysis of reciprocal daughter-cell pairs' genomes that is associated with a specific type of chromosomal rearrangement compatible with the ones observed in HR defective BRCA1/2 deficient cells.

Strengths:

This is an interesting paper that molecularly explores sister chromatid exchanges, which represent an important challenge in molecular biology since they are genetically silent.

Thank you very much for this assessment.

Weaknesses:

A complexity of the current paper is that it heavily relies on a recently published paper (Chovanec et al 2026, NAR) describing the powerful but complex technique sci-L3-Strand-seq. Knowledge of this paper is a prerequisite to understanding the current manuscript because no reminder is provided. In addition, the current manuscript presents the use of the sci-L3-Strand-seq technique in the study of SCE after Cas9-induced DSBs, while a companion study is referred to several times for containing results about SCE in XRCC1 KO. At some point, one questions the relevance of splitting the use of sci-L3-Strandseq in different papers instead of making a single integrated one.

We appreciate this concern. The original sci-L3-Strand-seq study is an extensive methodology paper that establishes and validates various computational framework, whereas the companion study focuses on the genetic regulation of spontaneous SCE. The experimental designs and biological questions of the companion study and the present work are therefore distinct, although we draw on selected results from the companion study where they provide useful comparisons and contrasts between spontaneous and Cas9-induced SCE. The present study addresses a distinct biological question, the response to Cas9-induced DSBs, and we therefore believe that combining these studies would make the resulting manuscript unnecessarily broad and obscure their different biological questions.

We nevertheless agree that the present manuscript should be understandable without requiring detailed knowledge of either paper. We have therefore added a brief description of the sci-L3-Strandseq approach (3rd paragraph of Introduction, Fig.S1A legends, and Fig.1B legends) and clarified the relevant methodological concepts where they are first introduced. We hope to 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.

Reviewer #3 (Recommendations for the authors):

(1) Abstract

"Identical sisters ": redundant

"non-local" inter-sister repair: the meaning is not clear. Do the authors refer only to "inter-sister" and therefore "non-local" is redundant, or do they imply something specific by "non-local", in which case it needs to be clarified?

"237 repetitive targets": at least a slight description of this target is needed. Is it a "random" repeat, a satellite sequence, a sequence related to a transposable element ?...

We agree with the reviewer that “identical sisters” is technically redundant. However, we have retained “identical” here to emphasize the distinction between sister chromatids vs. homolog, as SCE is sometimes misconstrued as exchange between homologs and as potentially causing loss of heterozygosity. We prefer the slight redundancy here for conceptual clarity.

We thank the reviewer for pointing out that the meaning of “non-local” was unclear. As discussed in our response to Reviewer #2, we use “non-local repair” operationally to distinguish repair confined to the broken chromatid in cis from repair involving exchange between sister chromatids. We have added a schematic (Fig.S1A) illustrating this distinction and explicitly define the term at its first use in the revised manuscript. Please see our response to Reviewer #2 above for the detailed rationale.

We thank the reviewer for asking us to clarify the nature of the 237 repetitive targets. The sgRNA targets an Alu sequence and was selected from a larger screen of >20,000 sgRNAs targeting repetitive sequences occurring at >200 genomic sites. In that screen, cellular toxicity did not simply scale with the number of predicted target sites; we therefore selected this sgRNA because its intermediate phenotype allowed us to introduce a large number of programmed DSBs without either minimal perturbation or excessive loss of cells. Thus, the 237-site guide was not an arbitrarily selected Alu-targeting sgRNA. The full repetitive-element screen is beyond the scope of the present study, but we have clarified in the Abstract that these 237 sites are Alu targets and added a brief description of the guide selection in the Methods.

(2) Introduction:

"non-local outcome / non-local repair processes": The use of "non-local" is not standard and is obscure for the reader. Specify if it has any meaning or remove it.

Please see our response above to both Reviewers #2 and #3 regarding our definition and use of “nonlocal repair”.

The authors mention that replication through a DSB generates four broken ends. However, in case the DSB is reached by one replication fork before the converging one, there are only three broken ends for at least the time required for the converging fork to reach the DSB from the other side. This may influence the repair outcome.

We agree with the reviewer. If one replication fork encounters the DSB before the converging fork, a transient three-ended intermediate can exist before the second fork reaches the break. This temporal asymmetry could influence repair pathway choice, including engagement of HR, end joining, or BIR-like repair. Our assay captures the resulting SCE outcome but cannot distinguish the order in which replication forks encounter the DSB or the repair pathway engaged at these intermediate stages. We have revised the text (2nd paragraph of the Introduction) to clarify that four broken ends represent the eventual configuration after replication through the DSB, rather than necessarily a simultaneous intermediate.

(3) Results

Cell cycle arrest experiment: it seems that a control condition with no Cas9 is missing to conclude better about what looks like a G2-M arrest, but that is not clearly mentioned.

Please see our response to Reviewer #1, Recommendation 6, regarding additional controls for the cell-cycle arrest experiment. Briefly, the D10A and H840A Cas9 nickases were delivered under the same experimental conditions as wild-type Cas9 but did not produce the cell-cycle arrest observed following DSB induction, providing an internal control for RNP delivery/transfection and supporting the association of the arrest with Cas9-induced DSBs. We would also like to clarify that the observed cell-cycle arrest is primarily a G1/S, rather than G2/M, basing on the FACS signal (see revised Fig.1B legend). This is consistent with the strong G1/S checkpoint in mammalian cells and the predominantly G1 cell-cycle distribution of BJ-5ta cells.

Note that the font size in Figure 1 is too small for readability.

We have enlarged the font sizes throughout Figure 1 to improve readability.

Figure 1B, D10A and H840A conditions:

The authors mention that nicks can be converted into DSBs through the passage of the replication fork, but do not see any cell cycle defect in the conditions tested. Is it possible that the absence of effect results from the fact that the analysis is done prior to nicks being converted into DSBs? This remark notably applies to the 237 target sites experiment. It seems that controlling for cell cycle delays for longer times is needed to conclude clearly about this aspect. In case a clear absence of cell cycle delay is observed in the 237 target sites in the Cas9 nicking condition, this would suggest that replication born DSBs behave differently from "classical" two-ended DSBs and do not trigger cell cycle arrest.

We agree that the timing of nick conversion during replication could contribute to the absence of a detectable cell-cycle delay under the conditions examined. However, extending the duration of Cas9 nickase treatment or labeling would not necessarily resolve this question, because persistent Cas9 activity permits repeated rounds of nicking across successive cell cycles, making it difficult to relate a later cell-cycle phenotype to a defined replication-born lesion. More generally, we believe that the relationship between replication-associated nicks, SCE formation, and cell-cycle progression is better addressed in the context of spontaneous SCE, which is the focus of our companion study. The present study is focused on SCE following programmed Cas9-induced DSBs, and analysis of replication-born nick lesions would require precise temporal control (ideally vfCas9 nickases that can be turned off) of individual nicking events relative to replication, for which an appropriate experimental system is not currently available to us.

Figure 1C should mention somewhere the genomic location of the four targets to clearly show that they correspond to the four major SCE peaks. In addition, there is no legend for the vertical pink stripes. Finally, it might be wise to keep the same y-axis scale for better comparisons.

Figure 1 overall: it might be wise to clearly show a no Cas9 condition to clearly set the SCE baseline and show that it is independent of Cas9 induction. As of now, it is not clear whether the non-targeted SCE comes from a specific cleavage of Cas9 or not. Such an aspect could benefit from putting Figure S1C in the main Figure 1. Alternatively, results from Chovanec et al 2026 (NAR) should be better restated because the reader does not necessarily have them in mind.

We thank the reviewer for these suggestions. The expected Cas9 target positions were already indicated by vertical bars in Fig. 1C; however, we agree that this was not sufficiently clear. We have therefore revised the figure legend to explain that the vertical bars indicate the expected Cas9 target positions. The Chovanec et al. (2026, NAR) study focused entirely on spontaneous SCE, which we simultaneously map here as the background signal, rather than the on-target SCEs induced by Cas9. We hope that explicitly identifying the target locations in the revised legend makes this distinction clear and ensures that prior knowledge of the NAR study is not necessary to interpret Fig. 1C.

We have retained the individual y-axis scales because the magnitude of SCE enrichment differs substantially among conditions. Using a common y-axis scale would make several of the on-target SCE peaks difficult to visualize.

The section « Disruption of DNA repair genes at the cut site did not measurably alter SCE frequency per cell » is questionable in the results section for the following reasons:

(i) The DNA repair genes are used here as target sites for Cas9 cleavage, but are not the object of the study, but may be the object of a companion paper. This aspect is slightly misleading.

(ii) As first mentioned in this section, there is evidence strongly suggesting that inactivating DNA repair genes will not affect SCE, and this is what the authors observed.

(iii) As an alternative, one could put the emphasis on the fact that the effect of Cas9-mediated inactivation of DNA repair genes (ie LIG3) starts to be detectable only in the washout condition ie after at least one cell cycle. But in this case, this is addressing the role of DNA repair genes in Cas9-induced SCE, which is not the point of the current paper.

We thank the reviewer for this comment and agree that the original framing of this section could give the impression that these experiments were intended to test the functions of the targeted DNA repair genes in SCE. This was not our intent. Rather, these genes provided defined genomic target sites for Cas9 cleavage, and the primary purpose of the experiment was to characterize SCE associated with Cas9-induced DSBs at these loci.

As discussed in our response to the Editor Assessment, there are important limitations to using these experiments to infer the consequences of loss of the targeted proteins, including the delay between Cas9 cleavage and depletion of pre-existing protein and, and particularly in the single-cell assay, selection for cells that escape disruptive editing at essential genes. We have added text to the Results explicitly describing these limitations.

We therefore agree with the reviewer that the delayed effects observed under the washout condition should not be interpreted here as establishing a role for individual DNA repair genes in Cas9-induced SCE. We have revised the section title to “Cas9 targeting of DNA repair gene loci did not immediately alter overall SCE frequency per cell” to clarify the scope of this experiment and to avoid implying that testing the functions of the targeted DNA repair genes is a major objective of the present study.

The conditions in Table 1 need to be homogenized and better explained:

- 237 sites and 237 cuts are used: homogenize?

We thank the reviewer for spotting this. We revised both to be “237 sites”.

- May explain better the rationale for putting BrdU simultaneously with Cas9 or after 24 h and a wash.

For the single-targeting sites, we observed more SCE when BrdU was added simultaneously with the Cas9 for the same 24 hours, compared to adding BrdU in the subsequent division after a wash. Therefore, for the 237 sites, we analyzed both conditions.

- Typo in the text: 237cuts_24ws_40BrdU instead of 237cuts_24ws_BrdU

We apologize for the lack of clarity in these labels and have substantially revised the Table 1 legend. In brief, the “40” is not a typo. In the 237 sites experiments, wild-type Cas9 considerably prolonged the cell cycle. Therefore, rather than labeling with BrdU for 24 hours as in the other conditions, we extended BrdU labelling to 40 hours in the last two conditions to allow more cells to progress into the subsequent G1 for successful Strand-seq analysis. We clarified that “237 sites 24 + 16hrs BrdU” refers to the condition in which Cas9 RNP and BrdU were added simultaneously. After 24 hours of Cas9 RNP treatment, BrdU labeling was continued for an additional 16 hours (a total of 40 hours of BrdU). The “237sites 24ws40BrdU” condition is the corresponding washout condition, in which Cas9 RNP was removed after 24 hours and cells were then labeled with BrdU for 40 hours post-washout.

- 237 cuts: Are some sites more enriched in SCE than others?

Yes, some sites showed greater SCE enrichment than others. We tested whether this variation correlated with chromatin accessibility but found no significant association. This was not unexpected, as the sgRNAs predominantly target Alu elements.

- Table 1: There is a difference between 237 sites 24ws24BrdU and 237cuts24ws40BrdU, with a significant enrichment of on-target SCE for the latter condition only. Could the increase in SCE rise even more with longer BrdU exposure? In other words, does the low enrichment in SCE at target sites in the 237 sites experiment result from a non-optimal timing for the analysis?

Yes, this is possible. We did not systematically test additional treatment or labeling durations. A 24-hour Cas9 RNP treatment is typically used for Cas9 RNP-mediated knockout experiments, and we therefore initially used this duration to assess gene-editing outcomes. For Strand-seq, BrdU labeling is ideally limited to approximately one cell division. Because BJ-5ta cells have an approximately 24-hour cell cycle, extending BrdU labeling substantially beyond 40 hours could allow some cells to undergo a second round of replication and become double-labelled. We therefore did not extend BrdU labeling beyond 40 hours. Thus, the lower enrichment in the 24ws24BrdU condition may in part reflect the timing of the assay.

- Figure 2 / RDCP analysis:

Interpretation of this figure relies exclusively on the 2026 NAR paper from the authors. This, at least, should be mentioned to help the reader understand it. Once the legend restates, this figure misses clear identification of the SCE and other genomic rearrangements. For readability, maybe the full genome should be kept for the supplementary data, and only the rearranged chromosomes should be kept in the main figure so that the rearrangements are clearly visible and annotated.

We thank the reviewer for this suggestion. To make the Strand-seq plots interpretable without relying on our 2026 NAR paper, we have added an explanation of Strand-seq orientation in the third paragraph of the Introduction and in Fig.S1A. We have revised Fig.2 legends to improve readability. We have retained the whole-genome view because Strand-seq data are conventionally presented in this format and it provides important genome-wide context for interpreting the observed events. The rearranged chromosomes and events were annotated in Fig.S3.

(4) Discussion

- Most DSB never formed or did not produce SCE: how to understand this better? What would be the argument in favor of one or the other possibility?

We agree that these are two possible explanations that cannot be distinguished by the current experiment. The absence of an SCE at a targeted site could reflect either inefficient DSB formation or repair of a DSB through a pathway that does not generate an SCE. Distinguishing these possibilities would require direct measurement of cutting efficiency at individual target sites, which was beyond the scope of this study.

- The conclusion about the effect of the Cas9 nickases needs to be toned down as long as the proper timing for SCE analysis has not been performed (see comment above).

We agree and have toned down this conclusion by specifying that no significant on-target SCE enrichment was detected under the conditions tested and acknowledging that we cannot exclude SCE formation at other time points (Discuss, first paragraph).

- As much as possible, avoid the use of non-conventional acronyms like URR.

We agree and have reduced the use of non-conventional acronyms where possible. We have retained URR (under-replicated region), as the term appears seven times throughout the manuscript, but have ensured that it is clearly defined at first use.

- The discussion about the RDCP analysis in the second paragraph of the discussion should refer to Figure 3.

Thank you for pointing this out. We added this reference to Fig.3

eLife Assessment

This study presents a valuable tool for comparing immune receptor data across multiple samples while properly accounting for statistical uncertainty and receptor similarity. The evidence supporting the tool is solid overall. However, some key concerns regarding potential sequencing artifacts in one of the validation datasets and an unclear strategy for false discovery rate control in the proposed framework remain to be addressed.

Reviewer #1 (Public review):

In this manuscript, the authors present ClustIRR, a computational tool that analyzes multiple TCR repertoires together, instead of one at a time. It builds one shared similarity graph across all the repertoires, then finds communities (CJs) on that graph that can be compared across samples. Building one shared graph across repertoires, rather than clustering each repertoire on its own, is a real improvement over existing tools. However, there are a few concerns that need to be addressed.

(1) The Introduction motivates ClustIRR by contrasting it with beta-binomial regression, Fisher's exact test, and scCODA/tascCODA (lines 62-77), but none of these are actually run on the same data in the Results. Could the authors include a direct comparison, e.g., applying a standard beta-binomial or Fisher's exact test to the Dataset 1 CJ occupancy matrix, to show the Bayesian model gives a lower false-positive rate or better-calibrated intervals than the alternatives it's positioned against?

(2) Prior predictive and posterior predictive checks are both reported as "(data not shown)" (lines 644, 728). Since the manuscript's central claim is rigorous, uncertainty-aware inference, it would help to include these diagnostic plots, along with Rhat and ESS values, in the supplement rather than stating they were checked.

(3) With 7,505 CJs tested simultaneously for differential occupancy in Dataset 1 alone (Figure 1 legend), what is the expected false discovery rate under the non-overlapping-HDI criterion used throughout? A short discussion of multiple-comparisons correction, or an argument for why it isn't needed under this framework, would strengthen the statistical claims.

(4) Line 115 states the Dataset 1 joint graph produced 10,301 CJs, of which 3,038 were singletons, leaving 7,263 non-singleton CJs. The Figure 1 legend reports 7,505 CJs used for the β modeling. Could the authors clarify how these two numbers relate - whether some singletons were included in the model, or a filtering step was applied that isn't described in Methods?

(5) The Methods section states that archival pretreatment tumor tissue was available for four patients (Pt4, Pt32, Pt36, Pt38; line 531), but the T+/T- DCJ analysis in Fig. 3B-C is only shown for Pt4. Was this analysis attempted in the other three patients? Extending it, even partially, would substantially strengthen the claim that contracting DCJs are enriched for tumor-infiltrating TCRs, which is currently based on a single patient.

(6) Dataset 1 was generated by deliberately stimulating T cells with EBV or MART1 antigen, so recovering EBV/MART1-annotated CJs from VDJdb is closer to a positive control than a blinded validation. Do the authors have, or could they obtain, any independent confirmation (e.g., tetramer data or an orthogonal cohort) for the CJs with large β that lack VDJdb annotation (orange dots, Figures 1B-C)?

Reviewer #2 (Public review):

Summary:

The study confronts a major obstacle in repertoire analysis. Given that individual TCR sequences are diverse and sparsely detected across repertoires, identifying sample-specific enrichment of TCRs based on sample-to-sample comparison of exact clonotype sequences can be intractable. This paper attempts to build on insights that sequence-similar TCRs can share antigen recognition, such that aggregating similar sequences derived from multi-sample joint-graph communities (i.e. clusters of tightly connected nodes) could reduce sparsity and boost signal.

Strengths:

The study is a well-motivated effort to address a need in the field. The paper takes a unique approach. The core method is modeling community occupancy with a hierarchical Dirichlet-Multinomial model that attempts to account for the high level of overdispersion present in repertoire sampling, a technique that has been previously applied to compositional microbiome data.

The authors apply this framework to both single-cell paired-chain and bulk single-chain TCR data. They develop a set of examples from public and synthetic data, with the most promising real-world application shown in reanalysis of longitudinal data during treatment of cancer patients with checkpoint inhibitors.

The manuscript is well structured and cogent. The authors are to be commended for contributing a well-documented, open-source R/Bioconductor package and for providing the underlying analysis datasets in a well-organized repository. In the joint graph construction step, the authors opt to use an existing implementation of the BLAST algorithm on CDR3 sequences, which is a slightly odd choice since it ignores potential contributions of other V-gene germline-encoded CDRs, but the authors also envision that their statistical package could be extended to include community graphs developed with other established TCR clustering tools. This will allow others to potentially explore the utility of Bayesian hierarchical Dirichlet-Multinomial models for differential occupancy analysis of immune receptors under varied clustering criteria.

The methods described here were demonstrated on relatively small datasets from 2-5 samples, and future work is likely needed to extend the joint graph differential occupancy concept to larger datasets. The authors are transparent about this and some of the other limitations in their current tool, most notably the computational cost of graph construction based on an all-versus-all sequence alignment to construct a joint sequence graph and the challenge of Bayesian parameter estimation as the number of subgraph entities scales with input data size. Since efficient approximate methods exist to find edges between similar text strings, the underlying idea of applying uncertainty-aware statistical inference to subgraph communities is promising, and the paper advances its primary goal.

Weaknesses:

The paper proposes the utility of the joint-graph community occupancy framework through three examples. I discuss potential weaknesses apparent in each separate example in turn.

(1) Weaknesses in Example 1

A broad weakness of the first results section ("Detecting EBV- and MART1-antigen reactive T cell communities from single cell datasets") is its reliance on a single vendor-generated dataset generated by the company ParseBio with no published experimental protocols and limited, if any, prior peer review. For reasons I will explore in greater detail below, the EBV-sample data may be particularly prone to chimeric pairings that confound the authors' primary analysis goals, and, at the very least, may not reflect physiologically realistic conditions for identifying antigen-reactive TCRs in other contexts.

Let us first consider Dataset 1 in more detail. The authors compare 2 antigen-stimulated repertoires with 3 unstimulated controls. To improve on single clonotype-level comparisons, the authors propose comparing the cell count aggregated across cells within joint graph communities constructed from paired CDR3 sequences across all the samples. Thus, one of the most relevant questions one hopes the authors answer in this section is whether the resolved graph communities are made up of many distinct clonotypes (i.e., are they polyclonal), allowing the method to function as intended by aggregating across multiple clones with putative shared antigen-reactivity.

Supplementary Figure 1B shows the size of all the communities with callouts for the putative EBV-expanded communities. The authors listed communities strongly enriched in the EBV-stimulated sample as e1, e2, e3, and e5. Each contains {greater than or equal to}100 clonotypes, and the authors note they contain at least one clonotype with a CDR3 sequence matching an EBV-annotated clone in VDJdb - a database of TCRs with some experimental evidence of epitope-reactivity. Community "e2" is notable for its remarkable size, including 1,339 unique clonotypes. At first glance, this seems promising for a method attempting to boost signal through community detection. However, it is worth re-investigating the individual clone sizes and sequences within this extraordinary community.

In the EBV-associated community "e2", a look at the data provided by the authors on the paper's GitHub repository suggests a single clonotype (clonotype_9; TRAV12-3 CATQGSNDYKLSF / TRBV9 CASSTGQVATNEKLFF) comprises 26,917 cells. As such, it makes up 29% of the sample with a total of 90,588 cells. If one clone supplies most of a graph community's cell counts, the community-level posterior estimate of β (Figure 1B) effectively tracks a single-clone estimate, and the premise of borrowing statistical power across a polyclonal expansion in this example is hard to assess.

There is also considerable evidence to believe that the apparent mega-polyclonality of cluster e2 may be partially an illusion, stemming from an artifact of this hyper-expanded clone's massive size and the experimental method used to assign TCRα-TCRβ chain pairings. In fact, the same α-chain CDR3 (CATQGSNDYKLSF) appears in ~1,219 clonotypes paired to distinct β chains, generating much of e2's remarkable 1,339-clonotype count. I believe two features warrant caution here. First, a single clonotype making up ~29% of total T cells in the sample is highly unexpected in ex vivo repertoires, suggesting intense non-physiological expansion conditions unlikely to generalize to other settings. That is, one would almost never expect to see a signal this strong.

Second, one TCR-α chain paired to ~1,220 distinct and diverse β chains in one sample is also biologically unexpected given what we know of the best-characterized epitope-specific responses for EBV, including to the well-known HLA-A*02 EBV BMLF-1 epitope, which recruits a tetramer-stained repertoire with conserved CDR3 motifs in both chains and at least some constraint on favored V-gene/α-β pairing (See Extended Data Figure 5 in Dash et al., Nature 2017). This raises the concerning possibility of barcode collision and mispairing against a hyperexpanded clone in the ParseBio split-pool method, unlikely to be robust to a clone occupying a third of the sample. Most of the ~1,219 β chains paired to the dominant α have a cell count of 1, further raising the concern of artifactual pairing versus genuine convergence. The second largest community "e1" also seems to suffer from the same issue, with a TCRβ sequence from one super clone making up 7% of the sample potentially being artifactually over-paired to >500 rare single-cell-count TCR α chains.

Taken together, these observations suggest that the authors' first positive control example passes but probably for the wrong reason since at least some of the "antigen-specific communities" are strongly anchored by a single hyper-clone. This could be remedied by repeating the same type of analysis on an ex vivo single-cell repertoire following more modest stimulation or natural infection (e.g., yellow-fever vaccine, influenza, or SARS-CoV-2 single-cell TCR datasets). I would advise future work using an alternative data source with better-documented experimental protocols, given the concerns above.

(2) Weaknesses in Example 2

Example 2 explores the application of Bayesian methods for identifying sample-enriched joint graph communities found in longitudinal data from many participants at two time points and longitudinal data from 1 person (Pt4) at 5 time points. A potential weakness of Case Study 2 is that it yields limited additional biological insight compared to what was previously shown by the authors of the underlying input data. Previously, Formenti et al. 2018 showed that the number of expanded clones after treatment strongly reflects responder status in this cohort, greater in patients with CR/PR versus SD or PD (See Figure 2b of the study). This 2018 primary analysis showed that tracking individual clonotypes was sufficient to reveal biological insight without the need for the computational demands of constructing a massive sequence similarity graph, finding communities on joint graphs, or Bayesian statistical inference. Thus, the impact of Case Study 2 in proving the unique utility of ClustIRR is somewhat diminished.

It is not clear how this study's result is more "robust" than the original analysis. Perhaps the authors could further clarify what is learned from the uncertainty-aware approach that could not be learned from exact clone tracking in time series.

Thus, example 2 shows that a complex method recapitulated the finding of a much simpler method for analyzing longitudinal TCR data where a strong signal of expansion was already present at the single-clonotype level. Since the Dirichlet method is sensitive to absolute counts, the large expanding clone in each community at 22 days may alone have carried most of the signal, which is not fully explored.

In this section, the authors make an interesting observation that CDR3β detected in both PBMC and patient-matched tumor samples were enriched in contracting communities (7/14) versus expanded communities (1/41). The authors do not indicate whether a similar enrichment of tumor-infiltrating lymphocytes (TILs) matched Day 0-22 contracting communities in the other 4 patients with tumor-matched samples, which, if consistent, would strengthen their finding.

(3) Weaknesses in Example 3

The final example explores "convergent repertoire differences between species." This is intriguing in principle but less informative due to the use of synthetic data with somewhat predictable properties that some may reasonably consider baked in by the data-generating process. That is, some of the results might be guaranteed by the way the data is constructed using the OLGA/IGoR generative model. For instance, the authors observe a positive correlation between CJ community size and Pgen of constituent clonotypes, stating: "This indicates that CDR3 sequences with high Pgen are statistically more likely to be generated, leading to convergence of similar sequences into public CJs." I may be mistaken, but this conclusion is almost guaranteed by the way the data-generating OLGA model outputs more similar high-Pgen sequences and fewer lower-Pgen sequences.

An interesting finding in this section is shown in Figure 4B, where community-level aggregation allowed for discrete clustering of human samples away from mouse samples that was not possible by comparing cosine similarity of a sparse clonotype occurrence matrix, a result that would be higher impact if it could be shown to separate real repertoire samples from humans with differential serology, vaccination status, or HLA backgrounds.

(4) Weaknesses in General

More generally, one aspect of the method that seems under-emphasized is the fact that many of the nodes in a multi-sample joint sequence similarity graph may have no edges. These zero-degree nodes would probably frequently occur in only one sample but be absent in other samples. It is not strongly emphasized in the paper how the model would infer whether such a singleton found in only one sample in the graph could be reliably inferred to be sample-specific enriched (see, for example, the large single node in Figure 3D, the orange node labeled "GQYF" in the far-right position of the lowest row in panel D). Presumably the number of cell counts represented in this single-sequence node is so great at sampled timepoint Day 22 as to yield a statistically strong signal in the multinomial model; however, the authors may wish to comment on how, for such singleton sequences, the power to detect sample-specific enrichment differs from prior single-clonotype-based methods.

With any large effort to find statistically significant features from a large candidate set examined all at once, a reader might be concerned with the potential for false discovery. Throughout, the authors seem to assign statistical significance when the 95% high-density interval (HDI) of the posterior estimate excludes zero or when the 95% HDIs of two features do not overlap. There is little discussion of how this implicitly handles multiplicity adjustment via shrinkage, which the authors could address more directly and explain more clearly to a broad audience, including many non-statisticians, who will read this paper.

Reviewer #3 (Public review):

Summary:

Analysis of immune receptor repertoires (IRR) needs to take into account the underlying diversity of the repertoires analysed, and the limitations inherent to the technologies used to measure IRRs: limited sampling depth relative to total number of cells and clonotypes, and experimental noise. In this work, Kitanovski and colleagues present ClustIRR. ClustIRR proposes to improve the analysis of immune receptor repertoires, specifically TCRs in the presented applications, by performing two steps: (1) consistent and comparable sequence clustering across repertoires, to account for sparsity of sampling, and (2) estimation of sequence clusters of interest using a Bayesian approach. They showcase ClustIRR performance in 3 scenarios: detection of antigen-specific T cells in a peptide-stimulation, detection of T cells responding to immunotherapy in the context of lung cancer, and analysis of mouse and human T cell repertoires.

Strengths:

(1) The cluster occupancy calculation presents an important conceptual framework which would be of interest and useful to the TCR repertoire field as it smoothly integrates information over a set of experimental conditions or time points. The application to longitudinal TCR sequencing datasets is particularly interesting, and could easily be extended to BCR sequencing datasets. Moreover, the calculation can be performed with any user-defined grouping of TCR clones, which allows for usage of other existing methods as the user wishes.

(2) The results of the human and mouse repertoires provide a very insightful argument for the use of metaclones as opposed to single clones for analysis of repertoires compared to single clones.

Weaknesses:

(1) While ClustIRR provides an interesting framework to analyse TCR sequencing datasets, it is not clear whether ClustIRR can perform more informative sequence clustering than state-of-the-art methods. A comparison of obtained clusters with existing methods would provide a useful benchmark. Moreover, computation time scales quite fast with the number of sequences included. This is a major limitation, as the authors state that a time of 2.5 hours is required for clustering of ~100,000 sequences, a number of clones that can easily be reached when analysing multiple samples together.

(2) The authors claim in the abstract that ClustIRR is integrated with gene expression data. However, in the results presented, the gene expression and TCR sequencing data are analysed separately, and the results are simply correlated. No real integration in the analysis exists for these two data types. The claim should be removed from the abstract. Moreover, the differential gene expression section, while it presents interesting results, lacks clarity and transparency. Presentation of the data in more transparent ways (such as showing violin plots or clustering on the UMAP) would increase the strength of the claims.

(3) The score calculation does not seem to be normalized to take into account the underlying diversities of CDR3a and CDR3b. While still a useful metric for sequence clustering, I worry about the impact of the lack of normalisation on the conclusion that the "alpha chain drives functional convergence through germline bias". The observation that clustering is mostly driven by the J gene is known and expected (https://pmc.ncbi.nlm.nih.gov/articles/PMC5553937/), as the J gene has lower diversity and greater overlap with the definition of CDR3. Because CDR3a is lower diversity generally from CDR3b, it will likely dominate the sequence similarity signal. Thus, it will appear that Ja drives the signal. The authors do try to address this by looking at clusters driven by CDR3b similarity. However, a low number of CDR3b-driven clusters is consistent with the similarity definition. I wonder if instead the appropriate control for this analysis would be to run the same analysis disregarding CDR3a sequence altogether, and quantify whether similar species-specific DCJ are identified when only CDR3b similarity is used? Absence or reduction of species-specific clustering would confirm that the effect is driven by the CDR3a sequence.

eLife Assessment

This meta-analysis provides a valuable contribution by integrating findings from dozens of macaque electrophysiology studies to reconcile discrepancies in choice probability and identify factors that robustly influence choice signals in the visual cortex. Such systematic synthesis across studies is rare in this field, and the analysis provides solid evidence for several conclusions, including the cross-study consistency of the relationship between choice probability and sensitivity and the distinctiveness of V1.

Reviewer #1 (Public review):

This meta-analysis addresses long-standing questions about the reliability and interpretation of choice probability in macaque visual areas, and provides some important findings (e.g., the cross-study consistency of the CP-sensitivity relationship, V1 distinctiveness). However, the evidence for several claims is incomplete: the analysis does not consider the statistical dependence of data points from the same studies and monkeys, and both the bistable-stimulus effect and the stimulus-duration effect rely on interpretive assumptions.

Strengths:

The paper's transparency about its own limitations is a genuine strength. Several sections of the paper and the supplement report null results (task exposure, lapse rate, eccentricity) rather than omitting them. This kind of self-scrutiny is uncommon in meta-analyses and substantially increases confidence in the parts of the analysis that do hold up.

Weaknesses:

(1) No mixed/hierarchical statistical models for nested data. The paper considers 150 data points from 59 studies and treats them as independent samples, though many share monkeys and brain areas. This reduces the confidence in the reported p-values. A standard way of dealing with this would be to use mixed-effect models with random intercepts rather than OLS.

(2) Evidence for one of the main findings in the abstract ("First, CPs were higher in tasks involving bistable percepts, reinforcing the link between CP magnitude and subjective perception.") is weak. This effect relies entirely on studies using bistable rotating cylinder stimuli performed in a single lab (lines 702 - 711). I would suggest making this more explicit in the abstract / discussion and in Figure 8b,c.

(3) The interpretation of main drivers of CP is unclear. The discussion summarizes the 4 main drivers of CP as "four systematic drivers of this variability: neuronal sensi758tivity, brain area, stimulus duration, and task type." The independent contribution of task type is however, questionable. In line 623, it is stated that the difference between coarse and fine discrimination can be entirely explained by the difference in sensitivity (explained possibly by differences in optimizing the stimuli). Again, detection tasks (line 658) show a trend for higher CP because most studies used tailored stimuli from single-recording experiments. Bistable task: see point 2. Thus, all "task effects" can be attributed to confounds, and the claim of the "four drivers of CP" should be revised.

(4) The paper could be improved by a Discussion that synthesizes the results in a concise manner. Now it seems more like a re-iteration of the results. Overall, I appreciate that the paper is thorough and discusses many of the caveats. However, those are somewhat buried in the long subsections, and I fear that the quick reader may walk away with a stronger impression of "four robust independent drivers" than the text, read carefully, actually supports.

(5) Datapoints are not weighted according to their standard error (common practice in meta-analysis is inverse-variance weighting). The concern is that underpowered studies with high variance (e.g., due to a low number of recorded neurons) have the same impact as well-powered studies, and this may change some of the estimates. For example, Supplementary Figure 4 shows that mean CP values decrease with statistical power of the study, consistent with the concern. If SEMs are not available, could the authors show the robustness of the results by weighting by sample size as a partial check?

(6) Interpretation of feed-forward vs. feedback origin of CP [Disclosure: I am an author of Wimmer et al. 2015.]. This paper presents a mechanistic network model of area MT and a decision area that decomposes CP into two components with distinct time courses, and, directly relevant to Section 2.6, shows how a combination of an early feedforward and a late feedback component can produce a roughly time-invariant (flat) CP. This is a specific, quantitative instance of the "sustained plateau" pattern the authors themselves note is inconsistent across studies (lines 480-486) but don't develop further. Engaging with this model in Section 2.1/2.6 would let the authors contrast their duration-effect interpretation against an explicit dynamical model rather than the generic feedforward/feedback dichotomy in Figure 7a.

(7) Reaction-time experiments. I am worried that differences in CP in RT vs. fixed duration tasks (Supplementary Figure 12) could have an influence on the main regression analysis (because RT experiments are mostly from detection tasks, and because RT experiments presumably include less of a post-decision period). Could this factor be included in the main analysis?

Reviewer #2 (Public review):

Summary:

This manuscript by Pletenev et al. provides a meta-analysis of 59 published studies on decision-related activity in the macaque visual cortex. The work does not contain original research material, but by conducting extensive analyses and compilations of previously published data, it provides several new insights not already conveyed in recent reviews on this topic.

Strengths:

The work is scholarly and helps organize and integrate a broad set of findings. A difficulty in such an undertaking is making sure that the original studies are accurately characterized and tabulated. The lead authors should be commended for the rigorous approach they've taken; the inclusion of many of the authors of the original studies as co-authors provides additional reassurance that trends visible across studies reflect an accurate quantification of what each study has shown.

Weaknesses:

My sole scientific concern is on the 'duration' section (lines 487 to 536). Specifically, the authors relate the dependence of choice probability (CP) on time to two competing (but not mutually exclusive) views of how CPs arise-the 'feedforward' vs 'feedback' views. The basis for the predictions in this section was not clear to me. In particular, it was not obvious that the predictions fully considered all the relevant factors. For instance, did the feedforward predictions consider how the response covariance depends on duration and how this would affect CP values (Equation 1)? (See for example Figure 4 of Kang and Maunsell, 2012, JNP.)

I would suggest either explaining the basis of the predictions much more carefully or moving the predictions to a supplementary section where they can be presented in more detail (i.e., more convincingly). Alternatively, since the section is inconclusive in the end (there is not strong evidence in favor of FF or FB), the authors could mention the theoretical predictions in passing only, i.e., much more briefly, just to make the reader aware that the different theories can provide predictions about the duration dependence.

Reviewer #3 (Public review):

Summary:

This study presents a comprehensive meta-analysis of choice probability (CP), a classic metric of the relationship between single-neuron responses and an animal's perceptual judgment. The authors compiled data from 59 macaque electrophysiology studies and identified several factors that consistently influence CP magnitude, including neuronal sensitivity, brain area, stimulus duration, and task type. These results provide evidence that helps settle several long-standing debates about how CP should be interpreted.

Strengths:

This work is a rare example of meta-analysis in macaque electrophysiology, focusing on an important and long-debated metric, choice probability (CP), in the study of sensory and decision-making mechanisms. CP has been measured across many studies, but its interpretation remains contentious because it depends on numerous task and recording factors in addition to sensory and decision-making mechanisms. Individual macaque studies also typically include few subjects, and CP effects are generally small, which prevents any single study from drawing strong conclusions about general patterns. The authors identified an ideal use case for meta-analysis and combined fragmented findings from individual primate studies into a coherent picture of which factors matter most for CP and which do not. This work can also serve as a guide for future meta-analyses of macaque electrophysiology data.

Weaknesses:

While the survey and discussion of CP's interpretation are comprehensive, the paper would benefit from a clearer conclusion on why measuring CP remains important and what future directions could make CP more useful for revealing sensory and decision-making mechanisms.

Author response:

We thank the Editors and Reviewers for their encouraging evaluation and constructive feedback. We are glad that they recognized the value of this systematic synthesis in reconciling disparate findings across many studies on an important question, and in providing new insights that help address long-standing debates around the interpretation of CP values. They also acknowledged our rigorous data curation involving many original study authors, and our transparency in reporting limitations and null results.

To address their constructive recommendations, we will provide additional hierarchical regression analyses where possible, state some limitations more explicitly, and condense the Discussion section to improve focus and readability.

Regarding the hierarchical nature of the data, we distinguish three potential hierarchical levels: studies, monkeys, and neuronal samples. Because individual monkeys contribute roughly one observation per study and cannot be tracked across publications, animal-level random effects are statistically unidentifiable. We will address the rare cases where identical neuronal pools were evaluated across multiple task conditions by providing a sensitivity analysis restricted to one data point per unique neuronal sample. At the study level (median 2, range 1–7 observations per study), we will present linear mixed-effects models with random study intercepts.

On the bistability findings, we agree with Reviewer 1's concern about the limited number of studies. We noted in the Results and Discussion that this effect currently relies on rotating-cylinder paradigms and emphasized the need for CP to be quantified with other forms of bistable stimuli. We will make this limitation explicit in the Abstract and Figure 8 caption. We will revise the Discussion to emphasize the three primary drivers (neuronal sensitivity, brain area, and stimulus duration) and treat the bistable stimulus effect separately as a distinct finding.

Regarding Reviewer 1's concern about reaction-time experiments: because reaction-time (RT) paradigms are heavily confounded with detection tasks in the existing literature (89% of detection tasks are RT tasks, and 67% of RT tasks are detection ones), including RT as a separate factor introduces near-complete collinearity. We will make this constraint and the inability to statistically disentangle them explicit in the main text.

Addressing Reviewer 2's concern regarding the CP–duration predictions, we agree that they depend on specific modeling assumptions. While our predictions—for the feedforward framework in particular—reflect standard models from the literature, we will explicitly acknowledge that alternative feedforward assumptions—such as duration-dependent response covariance—could alter the expected relationship.

In response to Reviewer 3’s comments on the rationale and future utility of measuring CP, we will revise the Discussion to emphasize that while the interpretation of CP has evolved from feedforward readout to include feedback mechanisms, our results confirm that CP remains a robust neural correlate of subjective perception. Although the exact mechanisms linking CP to perception remain unresolved, this ambiguity does not justify abandoning the metric; rather, CP remains an indispensable tool, provided it is supplemented with additional analyses as outlined in our recommendations.

eLife Assessment

This important study provides convincing evidence that somatosensory relay nuclei remain engaged during attempted hand movements following chronic cervical spinal cord injury, including in individuals with severe motor impairment. The combination of functional and quantitative MRI with physiological controls supports the main findings and may have implications that are of importance in understanding sensorimotor processing after spinal cord injury. However, the interpretation of this activity as specifically reflecting top-down, and particularly corticocuneate, signaling may be overstated. The origin and anatomical route of the observed activity appears to remain less firmly established.

Reviewer #1 (Public review):

Summary:

The authors investigated somatosensory processing along the afferent somatosensory pathway (cuneate nucleus, thalamus, S1) in a group of spinal cord injury patients and a group of controls. They propose that reduced motor function in SCI patients would reduce bottom-up activity; thus, recorded activity in SCI patients would reflect top-down modulation of overt or attempted movements.

Strengths:

(1) Strong methods.

(2) Experimental and control groups.

(3) Strong writing.

(4) Results well presented.

(5) Appropriate statistics.

Weaknesses:

Some results (or lack of) cast doubt about the ability of the used technique (3T fMRI) to detect the desired effects (bottom-up vs top-down activity).

Reviewer #2 (Public review):

Summary:

This study addresses a question that has been essentially inaccessible in humans: whether the early somatosensory relay nuclei are engaged by anything other than peripheral drive. Using functional and quantitative MRI in individuals with chronic cervical spinal cord injury, the authors show that the cuneate nucleus and VPL are robustly engaged during overt or attempted hand movement, and that this engagement persists in a participant with complete hand paralysis and no detectable muscle activity. They further report structural degeneration of the cuneate nucleus that is unrelated to the preserved task-evoked activity, and interpret the residual activity as reflecting top-down corticocuneate signalling.

Strengths:

The work is well conceived and clearly written, and the demonstration that the cuneate nucleus and VPL are robustly engaged during (attempted) hand movement after chronic cervical spinal cord injury is, to my knowledge, novel at this level of anatomical resolution. The finding is convincing. The dissociation between preserved task-evoked activity and marked structural degeneration of the cuneate nucleus is a highly interesting result with clear implications for rehabilitation. The manuscript is straightforward to follow, and the imaging protocol is carefully executed.

Weaknesses:

My main reservation concerns the inferential step from "not peripheral" to "corticocuneate". The data establish the former convincingly; the latter may not.

(1) Attribution of the observed activity to corticocuneate projections.

The central claim rests on an argument by elimination: because bottom-up drive is excluded in PT01, the residual activity must be top-down and, by extension, corticocuneate. Two distinct gaps should be addressed. First, "top-down" is not equivalent to "direct corticocuneate". Descending influence could reach the cuneate nucleus through multiple indirect pathways. Second, the activity observed at the three levels (cuneate, VPL, S1) need not be serially propagated, since layer 6 corticothalamic projections, for example, could drive VPL independently of any cuneate contribution. I would ask the authors to either provide evidence bearing on the routing, or to consistently use a route-neutral term (e.g. "descending" or "top-down") and reserve "corticocuneate" for the discussion of candidate mechanisms.

(2) Afferent input arising above the lesion level.

The EMG control in PT01 was restricted to hand and forearm muscles. Musculature innervated above C4 (cervical paraspinals, trapezius, and to a variable extent the shoulder girdle) remained available to this participant, and attempted hand movement is frequently accompanied by increased proximal co-contraction, postural stabilization, and altered respiratory effort. Afferent to the upper cervical cord is known to project to the ipsilateral cuneate nucleus, and its activity would produce lateralized, ipsilaterally dominant cuneate input - that is, precisely the pattern reported. This alternative is not excluded by the present control and should be addressed directly, ideally with proximal EMG in PT01 (and, if possible, in the other participants), or at minimum with an explicit discussion. Relatedly, the authors recorded respiratory and cardiac signals: please report whether respiratory volume or heart rate differed between movement and rest blocks, and between groups, since the dorsal medulla lies adjacent to cardiorespiratory nuclei.

(3) Functional significance of the preserved top-down signal.

The discussion establishes that top-down input persists but says relatively little about why it should. If the principal role of descending input to the cuneate nucleus is the gating of incoming afferent traffic, then in the absence of afferents there is nothing left to gate, and one might have expected the signal to be lost. Its persistence is the most interesting aspect of the finding and deserves fuller discussion. Candidate accounts the authors may wish to consider include: an efference copy or predictive signal delivered to a comparator that no longer receives its input, in the framework the authors already invoke (references 27, 28); engagement of the non-lemniscal outputs of the dorsal column nuclei (e.g., cuneocerebellar, cuneo-olivary projections); attempted movement engages motor imagery and attention, in which case the relevant question becomes what distinguishes these from movement-related gating. A related interpretational point: in behaving primates, movement-related modulation of cuneate transmission is bidirectional and includes prominent suppression (refs. 7/12). Note also that BOLD increases are compatible with increased inhibition, so they do not indicate facilitated throughput.

Author response:

Reviewer #1:

Some results (or lack of) cast doubt about the ability of the used technique (3T fMRI) to detect the desired effects (bottom-up vs top-down activity). 

As the reviewer notes, 3 T MRI alone cannot partition the relative contributions of bottom-up and top-down signals, since both are present during movement in an intact system. This reflects the premise of our study design but is also an important caveat when interpreting the group-level results, which characterise the net task-related response. Our central inference therefore focuses on the persistence of activation in PT01, in whom hand movement was absent. PT01 therefore lacks bottom-up signals, and any observed activity must be driven by top-down processes. In the revised manuscript, we provide measures of signal quality and activation magnitude to better characterise the sensitivity of these measurements and will draw on existing evidence that our approach resolves task-specific responses within these nuclei.

Reviewer #2:

(1) Attribution of the observed activity to corticocuneate projections: My main reservation concerns the inferential step from "not peripheral" to "corticocuneate". The data establish the former convincingly; the latter may not. The central claim rests on an argument by elimination: because bottom-up drive is excluded in PT01, the residual activity must be top-down and, by extension, corticocuneate. Two distinct gaps should be addressed. First, "top-down" is not equivalent to "direct corticocuneate". Descending influence could reach the cuneate nucleus through multiple indirect pathways. Second, the activity observed at the three levels (cuneate, VPL, S1) need not be serially propagated, since layer 6 corticothalamic projections, for example, could drive VPL independently of any cuneate contribution. I would ask the authors to either provide evidence bearing on the routing, or to consistently use a route-neutral term (e.g. "descending" or "top-down") and reserve "corticocuneate" for the discussion of candidate mechanisms. 

We agree with the reviewer that our previous attribution of the observed brainstem effects to corticocuneate processing was speculative and should have been presented as such. Our findings support a non-peripheral, top-down contribution but do not allow us to attribute this descending influence to a specific anatomical route. We have therefore revised the manuscript throughout to use “top-down” processing as a more route-neutral term, reserving the corticocuneate pathway for discussion of possible candidate mechanisms. We have also clarified in the revised discussion that activity observed across the cuneate nucleus, VPL, and S1 does not necessarily imply serial propagation through these structures.

(2) Afferent input arising above the lesion level: The EMG control in PT01 was restricted to hand and forearm muscles. Musculature innervated above C4 (cervical paraspinals, trapezius, and to a variable extent the shoulder girdle) remained available to this participant, and attempted hand movement is frequently accompanied by increased proximal co-contraction, postural stabilization, and altered respiratory effort. Afferent to the upper cervical cord is known to project to the ipsilateral cuneate nucleus, and its activity would produce lateralized, ipsilaterally dominant cuneate input - that is, precisely the pattern reported. This alternative is not excluded by the present control and should be addressed directly, ideally with proximal EMG in PT01 (and, if possible, in the other participants), or at minimum with an explicit discussion. Relatedly, the authors recorded respiratory and cardiac signals: please report whether respiratory volume or heart rate differed between movement and rest blocks, and between groups, since the dorsal medulla lies adjacent to cardiorespiratory nuclei.

The reviewer raises an important point. To test whether proximal muscle activity could account for the cuneate response in PT01, we collected additional EMG data during attempted hand movements, focusing on muscles innervated above the lesion level. These included the anterior (AD) and middle deltoid (MD), upper (UT) and middle trapezius (MT), and cervical paraspinals (CP), along with two of the original distal recordings (thenar eminence, TE; extensor digitorum, ED). Nonetheless, we found no significant difference in EMG activity in any recorded muscle during attempted left- or right-hand movement versus rest (Supplementary Figure 3A and 3B). To confirm that the chosen electrode montage could detect proximal muscle activity, we further instructed the participant to perform left or right shoulder shrugs during the same session. This produced a clear increase in activity during movement across the trapezius, cervical paraspinal and middle deltoid recordings (Supplementary Figure 3C and 3D).

In addition, we analysed the cardiac and respiratory recordings acquired during fMRI to determine whether movement-related physiological changes could explain the observed brainstem activity. Importantly, any physiological change in heart rate during movement is global and therefore cannot explain the hand-dependent lateralisation of the cuneate response. Furthermore, cardiac and respiratory nuisance regressors were included in all first-level models. Heart rate showed a small but significant increase during movement compared with rest (controls: +0.31 bpm; SCI: +0.69 bpm; main effect of condition F(1,33) = 10.22, p = 0.003, η²</sub>p</sub> = 0.24, BF₁₀ = 8.44), whereas respiratory volume per time (RVT) did not differ between conditions (F(1,33) = 0.35, p = 0.56, η²</sub>p</sub> = 0.01, BF₁₀ = 0.24). Given the autonomic consequences of cervical injury, we also tested whether these changes differed between groups. Neither measure showed a Group × Condition interaction (heart rate: F(1,33) = 1.41, p = 0.24, BF₁₀ = 0.56; RVT: F(1,33) = 1.60, p = 0.22, BF₁₀ = 0.61), suggesting that they cannot account for the group differences we report.

We have added the additional EMG control and the cardiorespiratory analyses to the Supplementary Material of the revised manuscript. Together, these controls suggest that neither proximal muscular nor cardiorespiratory factors explain our findings.

(3) Functional significance of the preserved top-down signal: The discussion establishes that top-down input persists but says relatively little about why it should. If the principal role of descending input to the cuneate nucleus is the gating of incoming afferent traffic, then in the absence of afferents there is nothing left to gate, and one might have expected the signal to be lost. Its persistence is the most interesting aspect of the finding and deserves fuller discussion. Candidate accounts the authors may wish to consider include: an efference copy or predictive signal delivered to a comparator that no longer receives its input, in the framework the authors already invoke (references 27, 28); engagement of the non-lemniscal outputs of the dorsal column nuclei (e.g., cuneocerebellar, cuneo-olivary projections); attempted movement engages motor imagery and attention, in which case the relevant question becomes what distinguishes these from movement-related gating. A related interpretational point: in behaving primates, movement-related modulation of cuneate transmission is bidirectional and includes prominent suppression (refs. 7/12). Note also that BOLD increases are compatible with increased inhibition, so they do not indicate facilitated throughput. 

We thank the reviewer for their comment and agree that the persistence of this descending signal despite profound loss of peripheral input is a very interesting aspect of the findings, and that our manuscript will benefit from a more extended discussion of this result. We will expand on this and the candidate accounts raised in the revised discussion. We will also clarify that movement-related modulation of cuneate processing may include both facilitation and suppression, and that our finding of increased BOLD activity does not necessarily imply facilitated sensory throughput.

eLife Assessment

This valuable study examines the relationship between simultaneous LC single-unit recordings and pupillometry, both within and across baseline and evoked epochs, finding that cross-epoch relationships are unreliable. The evidence is solid and suggests that care should be taken when interpreting pupil responses as reflecting LC activity. This manuscript will be interesting to basic and clinical researchers working in cognitive and decision neuroscience as well as computational psychiatry.

Reviewer #1 (Public review):

Summary:

This manuscript uses a valuable dataset of simultaneous LC single-unit recordings and pupillometry in awake monkeys to examine one aspect of the relationship between LC activity and pupil diameter: whether baseline LC activity predicts evoked pupil and whether baseline pupil predicts evoked LC. These relationships are largely absent in the present dataset, and the authors conclude that this type of prediction is not reliable.

Strengths:

This is a valuable dataset of simultaneous LC single-unit recordings and pupillometry in awake monkeys, the within-modal and within-epoch analyses are sound. The new results further caution the use of pupil diameter to infer LC activity.

Weaknesses:

There is an obvious rationale for asking whether baseline LC relates to baseline pupil or evoked LC relates to evoked pupil. It is also obvious to ask about the relationship between baseline and evoked LC activity, and between baseline and pupil responses. However, the rationale for the cross-modal and cross-epoch analysis is not clear. Why should one expect baseline LC to predict evoked pupil, or baseline pupil to predict evoked LC? What is the biological importance of such predictions? These analyses simultaneously change the modality and the temporal domain.

Furthermore, some recent studies, which are not referenced in this manuscript, showed variability in the relationship between pupil and LC within the same epoch, and that tonic and phasic pupil responses could be regulated by different inputs to LC. Given that the pupil-LC coupling is readily imperfect and potentially controlled by different cellular and circuit mechanisms, it is not surprising that their cross-epoch relationship is even more variable.

One main analysis that correlated baseline pupil with evoked LC showed statistically different results between the two monkeys, raising the question of to what extent a general claim for the cross-modal cross-epoch analysis can be made.

Reviewer #2 (Public review):

The manuscript by Thompson and Gold reported that, although baseline and evoked LC activity were positively correlated with baseline pupil size and evoked pupil dilation, respectively, there were no reliable cross-epoch relationships between LC activity and pupil size - that is, between baseline LC activity and evoked pupil dilation or between baseline pupil size and evoked LC activity. A major strength of the study is its large dataset, comprising recordings from more than 100 LC single units collected across 83 recording sessions in two monkeys. The authors further strengthened their conclusions by performing several control analyses to rule out potential confounds, including whether the findings were influenced by (1) the use of residuals in the main analyses, (2) the possibility that the auditory stimulus failed to evoke the full dynamic range of LC activity and pupil responses, and (3) nonlinear cross-epoch relationships between LC activity and pupil size.

These findings are important because they remind researchers to exercise caution when assuming that non-illuminance-mediated fluctuations in pupil size can reliably serve as a proxy for LC activity under all experimental conditions

With that being said, I have two suggestions that I believe would further strengthen the manuscript.

(1) Previous studies have suggested that the LC is organized into functionally distinct subpopulations (e.g., PMID 28920933 and PMID 40770025). It is therefore possible that a subset of the LC neurons recorded in this study does not participate in controlling pupil size. I encourage the authors to discuss this possibility in the Discussion. In addition, this possibility could be tested by repeating the cross-epoch relationship analyses using only LC units that exhibit a strong correlation with pupil size (the darker points in the last column of the top two rows of Figure 1?).

(2) The manuscript would benefit from a clearer visualization of the analyses addressing the possibility that the auditory stimulus failed to evoke the full dynamic range of LC activity and pupil responses. A supplemental figure illustrating the distributions or ranges of LC activity and pupil responses, together with the corresponding control analyses, would help readers better understand this important point.

eLife Assessment

This study addresses a key question concerning whether neurofeedback can enhance the neural representation of a selected speaker during competing continuous speech and whether such enhancement translates into behavioral benefits. The solid findings provide important insights into the online modulation of auditory attention and the extent to which selective listening can be voluntarily controlled. Although the observed effects were relatively small and did not consistently persist beyond the feedback period, the study advances understanding in an under-explored area and provides a helpful foundation for future research on sustained learning and behavioral transfer.

Reviewer #1 (Public review):

Summary:

The authors asked whether neurofeedback during competing continuous speech can help to modulate the attention-related N1-component in the temporal response function (TRF), which is an event-related-response-like estimate of the phase-locked EEG activity following the envelope. The research question is relevant because it asks to what degree the strength of attention can be controlled beyond the binary decision to attend or ignore something, and whether this control is beneficial for the behavioral outcome.

Strengths:

(1) Sample size of 56 participants.

(2) Control group with sham feedback.

(3) Novelty: Under-explored field of neurofeedback in selective speech tracking.

(4) Pragmatic and reasonable methodological decisions.

(5) Transparent results not hiding the fact that effect sizes are small.

Weaknesses:

Besides some need for clarification, I could only find one methodological weakness, which the authors discuss anyway:

(1) Overall, speech tracking-based neurofeedback may lead to more robust results, because the N1-extraction does not have to be handcrafted and all components would be taken into account. As the authors state, the P2-component has been related to effort, and this may provide more "room to play" for voluntary modulation.

The following "weaknesses" are related to the impact of the results:

(2) Non-translating effects to post-training trials, neither neurally nor behaviorally.

(3) Neurofeedback-related Modulation of N1

Reviewer #2 (Public review):

Summary

This manuscript investigates whether neurofeedback based on the N1 component of the temporal response function can be used to modulate neural responses during selective attention to continuous speech. Participants listened to two competing audiobooks and were instructed to attend to one of them. In the neurofeedback group, trial-by-trial N1 responses were converted into visual feedback, whereas the sham-feedback group received replayed feedback from other participants. The authors found a significant interaction between group and block for the N1 response to target speech over a small fronto-central cluster, with larger N1 responses during feedback blocks in the genuine neurofeedback group but not in the sham group. No neurofeedback effect was found for the distractor response. The authors also reported exploratory post-training effects and an association between changes in N1 and speech-comprehension performance at right fronto-central electrodes.

Overall, the study is conceptually interesting and novel. The online, trial-by-trial estimation of neural responses from continuous speech is an attractive development for auditory neurofeedback, and the inclusion of a randomised sham-feedback group is an important strength. However, the manuscript provides stronger evidence for modulation of a neural response during feedback than for learning or training of selective attention. Some aspects of the analysis and interpretation also require further consideration/clarification, particularly the use of group-specific N1 time windows, the spatial confound between target and distractor streams, the absence of artefact correction in the signal used for feedback, and the relatively weak behavioural evidence.

Strengths

The main strength of this study is its novel use of neurofeedback during continuous competing speech. Rather than providing feedback based on a general measure of brain activity, the authors targeted a specific neural response associated with selective auditory attention. The online implementation is technically impressive, allowing neural responses to be estimated from 22-second speech segments and converted rapidly into feedback. The inclusion of a sham-feedback group is another important strength, as it helps distinguish effects of genuine neurofeedback from nonspecific effects such as task engagement or motivation. The relatively large sample for a neurofeedback study and the use of natural continuous speech also increase the robustness and ecological relevance of the work.

Weaknesses

(1) The effect was present during the feedback blocks but did not increase across training blocks, and the post-training effect was not found at the same electrodes used for feedback. The evidence therefore supports online modulation more strongly than learning or lasting self-regulation, and claims about successful training or persistent learning should be interpreted cautiously.

(2) The offline analysis used different N1 time windows for the neurofeedback and sham groups. This introduces a potential bias in the group comparison because the dependent measure was defined differently between groups. Confirmation of the main result using a common, independently defined N1 window would strengthen the evidence.

(3) The target speech was always presented from the front and the distractor from behind. Differences between target and distractor responses therefore cannot be attributed entirely to attention because spatial location is also different. This limits the interpretation of target-versus-distractor differences and may also contribute to the weaker reliability of the distractor response.

(4) Feedback blocks always contained two speakers, whereas half of the baseline trials contained only one speaker. Since the presence of a distractor altered the neural response, it is important that the neurofeedback comparison is based on acoustically matched multi-speaker baseline trials. If this were not the case, differences between baseline and feedback could partly reflect differences in the acoustic condition rather than neurofeedback.

(5) No artefact correction was applied to the signal used for online feedback. Because feedback was derived from fronto-central electrodes, eye or muscle activity could potentially contribute to the measured signal. An offline demonstration that the main neural effect remains after appropriate artefact control would strengthen the interpretation that the effect reflects neural modulation rather than systematic changes in non-neural activity.

(6) The behavioural evidence is weaker than the neural evidence. There was no significant overall improvement in speech comprehension in the neurofeedback group. The reported behavioural effect is instead based mainly on associations between changes in the neural response and changes in comprehension, and some of these effects were weak before the whole-scalp analysis. Therefore, these findings are better interpreted as exploratory associations rather than evidence that neural modulation directly caused improved comprehension.

(7) Adding the distractor did not significantly reduce comprehension performance. The absence of a significant distractor effect on comprehension suggests that the listening condition may not have produced a strong behavioural cocktail-party difficulty in this sample. The large spatial separation between speakers and the nature of the behavioural task may have reduced sensitivity to distraction, which could limit the strength of the conclusions regarding improvement of speech understanding in challenging listening conditions.

(8) The study is described as double-blind, but the manuscript provides limited detail on how blinding was maintained, particularly when the experimenter manually checked the N1 estimate. In addition, participants' belief in or perceived control over the feedback was not formally assessed. These factors make it difficult to determine how effectively expectancy or motivation-related effects were controlled.

Overall assessment:

This study provides a valuable methodological and conceptual advance by showing that online, trial-by-trial neurofeedback can modulate the neural response to attended speech during competing speech. The evidence is solid for an immediate neural effect during feedback, and it was supported by comparison with a sham-feedback group. However, it remains incomplete for broader claims about learned self-regulation, persistent effects, distractor suppression, and improved speech understanding.

eLife Assessment

This study presents a fundamental molecular resource, offering subtype-specific insight into the composition of ribosome-associated protein complexes in the developing cerebral cortex. The evidence is compelling in terms of data quality and is strongly supported by the results, given the rigorous technical execution. While primarily descriptive in nature, this resource will be of great use to the field.

Reviewer #1 (Public review):

This work provides a valuable toolkit for endogenous isolation of projection neuron subtypes. With further validation, it could present a solid method for low-input ribosome affinity purification using a ribosomal RNA (rRNA) antibody. The experimental evidence for the distinct ribosomal complexes is limited to this method and indirect support from complementary analyses of pre-existing data. However, with additional experimental data to support the specificity of ribosomal complex pulldown and confirmation of the putative ribosomal complex proteins of interest, the study would provide compelling evidence for translation regulation of neuronal development through compositional ribosome heterogeneity. This work would be of interest to neuroscientists, developmental biologists, and those studying translational networks underlying gene regulation.

Strengths

(1) This in vivo labeling of specific projection neurons and ribosomal rRNA affinity purification method accommodates a low input of <100K somata per replicate, which is useful for the study of neuronal subtypes with limited input. In principle, this set of techniques could work across different cell types with limited input depending on the molecule used for cell type labeling.

(2) The authors are also able to isolate endogenous neurons with minimal perturbation up to the point of collection, preserving the native state for the neuron in vivo as long as possible prior to processing.

(3) This study identified over a dozen potential non-ribosomal proteins associated with SCPN ribosomal complexes, as well as a ribosomal protein enriched in CPN.

Limitations

(1) In this study, the authors address the advantages of their ribosomal complex isolation method in SCPN and CPN against RPL22-HA affinity purification. While this does show more pull down of the ribosomal RNA by the Y10B rRNA antibody, the authors claim this method identifies cell-type specific ribosomal complex proteins without demonstrating a positive control for the method's specificity. There are very limited experiments to truly delineate how "specific" this method is working and whether there could be contamination from other complexes bound by the antibody. I see this as the major limitation that should be addressed. To boost their claims of capturing cell-type specific ribosomal complexes, the authors could consider applying their rRNA affinity purification pipeline to compare cell-types with well-characterized ribosome-associated proteins, like mouse embryonic stem cells and HELA cells. The reviewer can completely appreciate the elegance in the neural characterization here, but it seems there needs to be a solid foothold on the specificity of the method, perhaps facilitated by cell types that can be more readily scaled up and tested.

(2) The authors followed up on their differentially enriched ribosomal complex proteins by analyzing ribosome association of these proteins in external datasets. While this analysis supports the ribosome-association of these proteins, there is limited experimental validation of physical association with the ribosome, much less any functional characterization. The reciprocal pulldown of PRKCE is promising; however, I would recommend orthogonal validation of several putative ribosomal complex proteins to increase confidence. Specifically, the authors could use sucrose gradient fractionation of SCPN and CPN, followed by western blot to identify the putative interaction with the 80S monosome or polysomes. This would also provide evidence towards the pulldown capturing association with mature ribosome species, which is currently unclear. This experiment would provide substantial evidence for the direct association of these non-ribosomal proteins with subtype-specific ribosomal complexes.

(3) The authors state interest in learning more about the differences underlying translational regulation of projection neuron development. This method only captures neuronal somata, which will only capture ribosomes in the main cell body. There are also ribosomes regulating local translation in the axons, which may also play a critical role in axonal circuit establishment and activity. These ribosomal complex interactions may also be rather transient and difficult to capture at only one developmental stage. Therefore, this method is currently limited to a single developmental snapshot of ribosomal complexes at P3 within the main cell body. It would be exciting to see extended utility of this method to sample neurites and additional developmental stages to gain further resolution on the developmental translation regulation of these projection neurons.

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

The authors introduce a unique pipeline of techniques to identify cell-type specific ribosomal complex compositions. With more validation, there is certainly potential for those studying neuronal translation to leverage this method in limited primary cells as an alternative to existing methods that do not rely on ribosomal protein tagging, such as ARC-MS (Bartsch et al., 2023), RAPIDASH (Susanto and Hung et al., 2024), and RAPPL (Nature Communications, 2025).

Comments on revised version.

We thank the authors for their thorough response to our comments. The revised manuscript satisfactorily addresses most reviewer comments through clarification and expanded discussion, although we believe some important limitations remain. In particular, we continue to view experimental validation of the identified ribosome-associated proteins as an important component of introducing this methodology to the field, rather than work that falls beyond the scope of the study. The authors have acknowledged that these experiments are future directions, and it is clear they plan to pursue additional validation outside of the current manuscript. Given their emphasis that the primary contribution is the development of a methodological framework, we believe the work may be appropriately framed as a Tool and Resource article. Such positioning would better align reader expectations with the manuscript's strengths as a technical advance while recognizing that further validation and functional characterization will be needed in future studies. Despite these limitations, I believe the manuscript makes a valuable methodological contribution.

Reviewer #2 (Public review):

Summary:

The study by presents a sophisticated molecular dissection of ribosome-associated complexes (RCs) in two well-defined cortical projection neuron subtypes (ScPN and CPN) during early postnatal development. The authors develop and optimize an rRNA immunoprecipitation-mass spectrometry (rRNA IP-MS) workflow to recover RCs from FACS-purified, retrogradely labeled neurons, achieving remarkable subtype specificity and biochemical resolution. Through proteomic profiling, they reveal both shared and distinct ribosome-associated proteins between ScPN and CPN, with a focus on non-core RC components and their potential functional relevance. The work advances our understanding of cell-type-specific translation regulation, moving beyond the transcriptome to explore the proteome-level complexity in neuronal subtypes.

Strengths:

This work stands out for its technical sophistication and innovation. The authors combine retrograde labeling, FACS purification, and an optimized rRNA IP-MS approach (low input) to isolate ribosome-associated complexes from highly specific neuronal subtypes in vivo, a challenging issue that they execute with impressive rigor. The methodological pipeline is both elegant and well controlled, yielding high-quality, reproducible data. The depth of proteomic coverage is remarkable, with nearly all known cytoplasmic ribosomal proteins identified, along with hundreds of ribosome-associated proteins (RAPs), including translation factors, chaperones, and RNA-binding proteins. The analysis not only reveals shared components between ScPN and CPN RCs but also uncovers subtype-specific differences in associated proteins.

Particularly notable is the integration of this new proteomic dataset with previously published transcriptomic and ribosome footprinting data, which helps to validate the specificity and relevance of the findings. Overall, the clarity of the writing, the robustness of the data, and the transparency of the methods make this a strong and compelling contribution.

Weaknesses:

Despite the depth and high quality of the dataset, the study remains descriptive. While the identification of subtype-specific RC components is intriguing, the current version of the manuscript does not explore their functional roles or biological consequences of their alterations. There is no perturbation, causal testing, in vitro or in vivo manipulation to demonstrate whether these proteins are necessary for ScPN or CPN identity, specific axonal targeting, metabolism or synaptic function.

One important point that is also highlighted by the authors in their discussion and that is critical to establish the subtype specificity of the identified protein. One important point highlighted by the authors in the discussion - and critical for establishing the subtype specificity of the identified proteins-is that some ribosomal complexes may be specialized for specific developmental stages, rather than exclusively for the subtype-specific needs of projection neuron development. The work presented here provides a valuable starting point for further investigation into such RC specialization. However, it will be essential to determine to what extent these RCs exhibit true subtype specificity, independently of their temporal maturation context.

As a result, key mechanistic insights remain a bit speculative. Although several of the identified proteins have known roles in processes like synaptogenesis or metabolism, their relevance to the specific neuronal subtypes under study is not experimentally addressed. That said, given its rich content and the comprehensive early postnatal dataset, the manuscript represents an extremely valuable resource for the community. While primarily exploratory, it lays a strong foundation for future functional studies aimed at uncovering the biological impact of the identified ribosomal complexes.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

This work provides a valuable toolkit for endogenous isolation of projection neuron subtypes. With further validation, it could present a solid method for low-input ribosome affinity purification using a ribosomal RNA (rRNA) antibody. The experimental evidence for the distinct ribosomal complexes is limited to this method and indirect support from complementary analyses of preexisting data.

However, with additional experimental data to support the specificity of ribosomal complex pulldown and confirmation of the putative ribosomal complex proteins of interest, the study would provide compelling evidence for translation regulation of neuronal development through compositional ribosome heterogeneity. 

This work would be of interest to neuroscientists, developmental biologists, and those studying translational networks underlying gene regulation.

Strengths

(1) This in vivo labeling of specific projection neurons and ribosomal rRNA affinity purification method accommodates a low input of <100K somata per replicate, which is useful for the study of neuronal subtypes with limited input. In principle, this set of techniques could work across different cell types with limited input, depending on the molecule used for cell type labeling.

(2) The authors are also able to isolate endogenous neurons with minimal perturbation up to the point of collection, preserving the native state for the neuron in vivo as long as possible prior to processing. 

(3) This study identified over a dozen potential non-ribosomal proteins associated with SCPN ribosomal complexes, as well as a ribosomal protein enriched in CPN.

We appreciate the reviewer's thoughtful and detailed review. We especially appreciate the positive evaluation of its strengths, including the use of rRNA affinity purification to access ribosomal complexes in low-input neuronal subtypes in vivo with minimal perturbation, and the resulting identification of distinct ribosomal complexes in SCPN and CPN with associated non-ribosomal proteins. We are also pleased by the recognition of its significance in advancing our understanding of neuronal subtype-specific post-transcriptional gene regulation. We have carefully addressed the limitations below.

Limitations

(1) In this study, the authors address the advantages of their ribosomal complex isolation method in SCPN and CPN against RPL22-HA affinity purification. While this does show more pull-down of the ribosomal RNA by the Y10B rRNA antibody, the authors claim this method identifies cell-type-specific ribosomal complex proteins without demonstrating a positive control for the method's specificity. 

There are very limited experiments to truly delineate how "specific" this method is working and whether there could be contamination from other complexes bound by the antibody. I see this as the major limitation that should be addressed. To boost their claims of capturing cell-typespecific ribosomal complexes, the authors could consider applying their rRNA affinity purification pipeline to compare cell types with well-characterized ribosome-associated proteins, like mouse embryonic stem cells and HELA cells.

The reviewer can completely appreciate the elegance in the neural characterization here, but it seems there needs to be a solid foothold on the specificity of the method, perhaps facilitated by cell types that can be more readily scaled up and tested.

We thank the reviewer for the opportunity to further clarify how our experimental design addresses the question of specificity of ribosomal complex pulldown. The rRNA affinity purification pipeline was applied identically to both SCPN and CPN, with the analysis focused on comparative, differential analysis between the two subtypes. We employed this approach to subtract out potential background signal or non-specific binding to the Y10b antibody present in both subtypes. We have now clarified this experimental design in the text, at the end of the first result section.

(2) The authors followed up on their differentially enriched ribosomal complex proteins by analyzing the ribosome association of these proteins in external datasets. While this analysis supports the ribosome-association of these proteins, there is limited experimental validation of physical association with the ribosome, much less any functional characterization.

The reciprocal pulldown of PRKCE is promising; however, I would recommend orthogonal validation of several putative ribosomal complex proteins to increase confidence. 

Specifically, the authors could use sucrose gradient fractionation of SCPN and CPN, followed by a western blot to identify the putative interaction with the 80S monosome or polysomes. This would also provide evidence towards the pulldown capturing association with mature ribosome species, which is currently unclear. This experiment would provide substantial evidence for the direct association of these non-ribosomal proteins with subtype-specific ribosomal complexes.

We thank the reviewer for the feedback and suggested future directions for candidate validation. We appreciate the recognition of our analysis of external datasets from independent approaches that provides support for physical ribosome association of these candidates. We respectfully submit that the scope of this work is an unbiased comparison of ribosomal complexes between SCPN and CPN to identify and nominate candidates for future investigation. We agree that future work to advance this direction of inquiry would optimally include further characterization of their subtype-specific physical interactions with ribosomes to further elucidate functional implications.

We appreciate the reviewer's suggestion of sucrose gradient fractionation for polysome profiling. We carefully considered this approach midway through this work, and we pursued pilot experiments to test feasibility. These pilot experiments reinforced findings in the existing literature that it typically requires on the order of 10⁷ cells, well beyond the feasible scope of these low-input purified neuronal subtypes. We respectfully submit that imaging-based approaches, such as proximity ligation assays and super-resolution microscopy, are likely more applicable to such very limited material, though would require extensive candidate-specific optimization beyond the scope of this project. We have now expanded future experimental consideration in the Discussion’s penultimate paragraph.

(3) The authors state interest in learning more about the differences underlying translational regulation of projection neuron development. This method only captures neuronal somata, which will only capture ribosomes in the main cell body. There are also ribosomes regulating local translation in the axons, which may also play a critical role in axonal circuit establishment and activity. These ribosomal complex interactions may also be rather transient and difficult to capture at only one developmental stage. Therefore, this method is currently limited to a single developmental snapshot of ribosomal complexes at P3 within the main cell body. It would be exciting to see the extended utility of this method to sample neurites and additional developmental stages to gain further resolution on the developmental translation regulation of these projection neurons.

We thank the reviewer for the opportunity to further highlight the foundational significance of this work in translational regulation of projection neuron development. Here, we identified subtype-specific differences in ribosomal complex composition within somata at a critical developmental time window for two PN subtypes. This work provides foundation for future investigation of local translation and its regulation in growth cones and axons. It will also enable direct comparison with potential future results from axons and growth cones, developmental subcellular specializations at axon tips that implement pathfinding and circuit formation (such work is not yet feasible due to exceptionally low available input). Our lab has significant ongoing work regarding subtype-specific axon and growth cone biology, including recent investigations of growth cone-localised RNA and protein molecular machinery that regulate circuit formation, maintenance, and function of distinct cardinal PN subtypes (Poulopoulos*, Murphy* et al. Nature 2019; Engmann*, Hatch* et al. Nature Prot 2022; Itoh et al. Cell Rep 2023; Veeraraghavan*, Engmann* et al. Nature Neurosci 2026; Durak*, Kim* et al. bioRxiv 2023; Veeraraghavan*, Tillman* et al. bioRxiv 2025; Tillman et al. bioRxiv 2026). Combining subtype-specific growth cone purification with ribosomal complex investigation represents a logical and exciting future direction. We appreciate the reviewer's encouragement of this future line of investigation and now highlight it in the revised Discussion.

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

The authors introduce a unique pipeline of techniques to identify cell-type-specific ribosomal complex compositions. With more validation, there is certainly potential for those studying neuronal translation to leverage this method in limited primary cells as an alternative to existing methods that do not rely on ribosomal protein tagging, such as ARC-MS (Bartsch et al., 2023), RAPIDASH (Susanto and Hung et al., 2024), and RAPPL (Nature Communications, 2025).

Reviewer #2 (Public review):

Summary:

This study presents a sophisticated molecular dissection of ribosome-associated complexes (RCs) in two well-defined cortical projection neuron subtypes (ScPN and CPN) during early postnatal development. 

The authors develop and optimize an rRNA immunoprecipitation-mass spectrometry (rRNA IPMS) workflow to recover RCs from FACS-purified, retrogradely labeled neurons, achieving remarkable subtype specificity and biochemical resolution. Through proteomic profiling, they reveal both shared and distinct ribosome-associated proteins between ScPN and CPN, with a focus on non-core RC components and their potential functional relevance. The work advances our understanding of cell-type-specific translation regulation, moving beyond the transcriptome to explore the proteome-level complexity in neuronal subtypes.

Strengths:

This work stands out for its technical sophistication and innovation. The authors combine retrograde labeling, FACS purification, and an optimized rRNA IP-MS approach (low input) to isolate ribosome-associated complexes from highly specific neuronal subtypes in vivo, a challenging issue that they execute with impressive rigor. The methodological pipeline is both elegant and well-controlled, yielding high-quality, reproducible data. The depth of proteomic coverage is remarkable, with nearly all known cytoplasmic ribosomal proteins identified, along with hundreds of ribosome- associated proteins (RAPs), including translation factors, chaperones, and RNA-binding proteins. 

The analysis not only reveals shared components between ScPN and CPN RCs but also uncovers subtype-specific differences in associated proteins. Particularly notable is the integration of this new proteomic dataset with previously published transcriptomic and ribosome footprinting data, which helps to validate the specificity and relevance of the findings. Overall, the clarity of the writing, the robustness of the data, and the transparency of the methods make this a strong and compelling contribution.

Weaknesses:

Despite the depth and high quality of the dataset, the study remains descriptive. While the identification of subtype-specific RC components is intriguing, the current version of the manuscript does not explore their functional roles or the biological consequences of their alterations. There is no perturbation, causal testing, in vitro or in vivo manipulation to demonstrate whether these proteins are necessary for ScPN or CPN identity, specific axonal targeting, metabolism, or synaptic function. One important point highlighted by the authors in the discussion - and critical for establishing the subtype specificity of the identified proteins - is that some ribosomal complexes may be specialized for specific developmental stages, rather than exclusively for the subtype-specific needs of projection neuron development. The work presented here provides a valuable starting point for further investigation into such RC specialization. 

However, it will be essential to determine to what extent these RCs exhibit true subtype specificity, independently of their temporal maturation context. As a result, key mechanistic insights remain a bit speculative. Although several of the identified proteins have known roles in processes like synaptogenesis or metabolism, their relevance to the specific neuronal subtypes under study is not experimentally addressed. 

That said, given its rich content and the comprehensive early postnatal dataset, the manuscript represents an extremely valuable resource for the community. While primarily exploratory, it lays a strong foundation for future functional studies aimed at uncovering the biological impact of the identified ribosomal complexes.

We thank the reviewer for their excellent summary and for their very positive assessment of our work. We are pleased that the methodological rigor, proteomic depth, and integrative analyses were well-received. We thank the reviewer for highlighting that our “work presented here provides a valuable starting point for further investigation into such RC specialization” and that “it lays a strong foundation for future functional studies aimed at uncovering the biological impact of the identified ribosomal complexes.” This is exactly how we view this contribution – as a foundation to share with broader field so such functional investigation and investigation of developmental dynamics can be pursued by multiple groups in the broader related field.

We again thank the reviewer for the very positive and insightful comments.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

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

(1) As listed in the limitations, I would recommend that the authors consider applying their rRNA affinity purification to additional cell lines to confirm the specificity of the method as a positive control, where just demonstrating the technology may be easier to carry out than with more limited samples.

As we noted in our response above to Limitation 1: “The rRNA affinity purification pipeline was applied identically to both SCPN and CPN, with the analysis focused on comparative, differential analysis between the two subtypes. We employed this approach to subtract out potential background signal or nonspecific binding to the Y10b antibody present in both subtypes. We have now clarified this experimental design in the text, at the end of the first result section.”

(2) Also, as listed in the limitations, I recommend that the authors provide orthogonal experimental evidence for the putative SCPN and CPN ribosomal complex proteins of interest (e.g., sucrose gradient > western blot).

As we noted in our response to Limitation 2 above: “We appreciate the recognition of our analysis of external datasets from independent approaches that provides support for physical ribosome association of these candidates. We respectfully submit that the scope of this work is an unbiased comparison of ribosomal complexes between SCPN and CPN to identify and nominate candidates for future investigation. We agree that future work to advance this direction of inquiry would optimally include further characterization of their subtype-specific physical interactions with ribosomes to further elucidate functional implications.”

Regarding sucrose gradient fractionation (for polysome profiling), we also noted in our response to Limitation 2: “We carefully considered this approach midway through this work, and we pursued pilot experiments to test feasibility. These pilot experiments reinforced findings in the existing literature that it typically requires on the order of 10⁷ cells, well beyond the feasible scope of these low-input purified neuronal subtypes. We respectfully submit that imaging-based approaches, such as proximity ligation assays and super-resolution microscopy, are likely more applicable to such very limited material, though would require extensive candidate-specific optimization beyond the scope of this project. We have now expanded future experimental consideration in the Discussion’s penultimate paragraph”.

(3) The authors are interested in preserving the native state of the projection neurons to isolate ribosomal complexes; therefore, they may consider using biotin-conjugated CTB (Thermo Fisher) sorting through anti-biotin MACS columns (Miltenyi Biotech) as opposed to FACS in the future. While it does not allow for the same visualization as using a CTB-FP, this slight pipeline adjustment could help save time and physical processing of the projection neurons, helping preserve their endogenous state.

While we appreciate the reviewer’s constructive suggestion for this theoretically alternative approach, we respectfully submit that this approach is unlikely to effectively isolate projection neurons from the living brain as effectively as FACS approach employed here. We considered this approach. We respectfully offer that CTB standardly enters neurons by binding GM1 gangliosides at the axon terminal, after which it is internalized and undergoes retrograde transport to the soma, several millimeters or more away depending on the projection. By the time CTB reaches the soma, we further respectfully offer that it is standardly fully internalized and is no longer surface-exposed for the theoretically suggested antibiotin capture for MACS. We used magnetic bead-based pull-down for the ribosomes themselves and find those molecular approaches very beneficial. Despite our use and openness to magnetic-conjugate-based separation approaches, we judge that fluorophore-conjugated CTB and FACS remain the most efficient and feasible approach for isolation of these exceptionally polarized projection neurons while maintaining cell viability. 

(4) While the authors provided a comparison of overall protein detection levels between SCPN and CPN, I recommend an additional analysis and potential normalization for the average core ribosomal protein abundance across samples. I will note that this is more accessible when samples are prepared using TMT-labeling methods, which might be considered for future experiments.

We thank the reviewer for these suggestions. We appreciate the opportunity to address them together, to further clarify our deeply considered choice of MS-based proteomic analysis and corresponding primary normalization approach. To complement our initial normalization approach, we have now also implemented the reviewer’s suggested approach of normalization to the average intensity of core ribosomal proteins. Notably, these new results agree with those from our initial normalization approach. This insightful suggestion has further strengthened the paper’s results and interpretation. 

Here, we employed label-free quantification (LFQ), wherein samples are assayed sequentially rather than simultaneously, to most rigorously establish which proteins are truly present in some neuronal subtypes but absent in others. As the reviewer is aware, this capability to determine absence vs. presence of MS-detectable peptides distinguishes LFQ from approaches that assay samples simultaneously, such as isobaric tandem mass tag (TMT) labeling, which standardly offers advantages in relative quantification studies. Advances in sample preparation, instrumentation, and data analytical algorithms (from recent developments in single-cell proteomics and related approaches) now enable application of LFQ in quantitative differential analysis, even in the ultra-low-input regime. We now include both detailed discussion of these points and relevant citation in the text. 

As the reviewer is also aware, in LFQ, normalization is crucial to ensure the protein quantification is accurate and comparable across sequential runs. For quantitative differential analysis of proteins detected in both subtypes, we have implemented a primary normalization approach employing “median-of-ratios” normalization across all detected proteins for robustness against outliers and technical variability. This primary approach results in similar overall distributions of protein abundances across CPN and SCPN samples (Figure S2A), providing confidence in quantitative comparison between SCPN and CPN in the ultra-lowinput regime. 

Following the reviewer’s suggestion, to further ensure rigor of identification of differential proteins, we have also implemented a second normalization approach, rescaling each sample to the average intensity of its core ribosomal proteins alone (new Figure panels S2B, C). Subsequent differential analysis reveals equivalent CPN > SCPN enrichment of RPS30/eS30, GUCY1A1, and CELF3 (proteins identified as CPN-enriched with the primary normalization approach). These three proteins rank among the five proteins with lowest p-values, though false-discovery-rate-corrected significance is reduced. This confirmation by a second normalization approach further strengthens the findings.

We have included clarifications in the main text, added the second normalization approach and subsequent analysis in both the main text and Figure S2. In addition, we have now noted in the discussion that TMT labeling with correspondingly appropriate normalization approaches might better define relative quantitative differences between functional candidates present in multiple subtypes.

Recommendations for improving the writing and presentation:

(1) I recommend this as a Tools or Resource article, seeing as the biological conclusions are limited.

We respectfully submit that this work investigated biological questions and identified biological answers beyond pure development of Tools or offering a dataset as a Resource. We further respectfully submit that the question of differential neuronal subtype-specific translation of shared transcripts has become an emerging area of interest in regulation of precise neuronal and circuit development, maintenance, and function, as well as the neurobiological basis of disease. This has been quite hard to study, and this paper brings a first level of answers to that biological question. Of course, the biological results of this paper are not the complete answer, but as with all biological discovery papers, it provides a foundation for many further studies by multiple labs. 

(2) In the rationale for studying ribosomal complex machinery, it may be helpful to say that ribosome composition and associated proteins that are present in the cytoplasm provide a way in which ribosomes can tune translation rapidly. This is especially important, seeing as this affords post-mitotic neurons the opportunity to remodel and repair by using readily available proteins while also avoiding the energetic demands of producing new ribosomal complex proteins.

We thank the reviewer for this insightful comment and fully agree. We have now added this rationale to the Introduction. 

(3) Is there a need for a CTB injection control? Does GM1 binding affect translation pathways? Please list citations, if possible.

We respectfully submit that a CTB injection control is not necessary. As noted in our response to Limitation 1 in the Public Review portion, both PN subtypes underwent retrograde labeling with CTB in this work. While it remains unknown whether CTB-GM1 binding affects translation, potential effects of CTB are expected to apply equivalently to both subtypes and would therefore not confound these between-subtype comparisons. Please also see our response to recommendation 4 immediately below, in which we further clarify that retrograde tracing with CTB is a long-standing, well-accepted method shown to cause minimal damage and not interfere with continued neuronal development.

(4) Do the traced/labeled PNs keep developing normally? In other words, does retrograde tracing inhibit proper PN development? Please list citations, if available.

We thank the reviewer for encouraging us to further clarify that these are longstanding and well-accepted methods in the field, found to cause minimal damage and not to interfere with continued neuronal development. These and related retrograde labeling methods have led to the identification of the field's cardinal regulatory genes and molecules of axonal connectivity. This includes substantial work from our own lab (PMID in parentheses): Arlotta*, Molyneaux* et al. Neuron, 2005 (15664173); Lai*, Jabaudon* et al. Neuron, 2008 (18215621); Molyneaux*, Arlotta* et al. J. Neurosci., 2009 (19793993); Galazo et al. Neuron, 2016 (27321927); and more recently Sahni et al. Cell Rep., 2021a (34686320); and Sahni et al. Cell Rep., 2021b (34686337). These methods have also employed by other groups, such as Bin Chen (e.g. McKenna et al. PNAS, 2015 (26324926)) and Marta Nieto (e.g. De León Reyes et al. Nat. Commun., 2019 (31591398)). We have now clarified this in the text and included references for the benefit of the readers.

(5) It may be helpful to mention that RPS30 associates with immature ribosomes during biogenesis (PMID: 25706898).

We thank the reviewer for the opportunity to further clarify background knowledge of RPS30. As the reviewer is aware, RPS30/eS30 is definitively part of the mature 80S ribosome, as established, e.g., by cryo-EM of human 80S ribosomes (PMID: 25901680). Like multiple other ribosomal proteins, RPS30/eS30 also associates with immature ribosomes during biogenesis (PMID: 25706898). Intriguingly, RPS30/eS30 is produced by cleavage of a fusion protein comprising ubiquitin-like FUBI and RPS30/eS30, with cleavage recently identified as a late step in cytoplasmic 40S maturation (PMID: 34318747). As noted in the text, we confirmed that the peptides used for RPS30/eS30 identification appropriately map only to the amino acid sequence of RPS30/eS30 and not FUBI. We now mention that it is a core component of the mature 80S ribosome and its immature ribosomal association. 

(6) Please clarify how the rRNA-IP is pulling down mature ribosomes. If not, this should be incorporated into the discussion.

We thank the reviewer for raising this interesting point. As the reviewer notes, it is well established in the ribogenesis field that ribosomes are continuously produced and therefore exist at various stages of maturation. Our protocol removes a major source of immature ribosomes by subjecting FACS-purified cells to two centrifugal spins that remove the nucleus, the site of ribogenesis and early steps of maturation. In pilot experiments, nuclear removal was confirmed by the absence of a contaminating genomic DNA peak on Bioanalyzer electropherograms of total RNA extracted from input samples (without genomic DNA removal) immediately prior to rRNA-IP. However, ribosomes also undergo cytoplasmic maturation steps, and various functional states of ribosomes have been found to be present in the cytoplasmic fraction. For these reasons, we have referred to what we pulled down as "ribosomal complexes" throughout the manuscript. We now explain this nuclear/immature ribosome depletion and cytoplasmic ribosomal enrichment in the text.

(7) Would have been interested to see some discussion of the most enriched CPN RAPs or why these might not exist in most replicates (inter-subtype heterogeneity?)

The reviewer asks an interesting question. As the reviewer is aware, when considering a single sample in isolation, absence of mass spectrometry-based detection is not definitive proof of absence, especially not within this work’s ultralow input regime. One of us (B. Budnik) has substantial experience with ultra-low-input samples across multiple cell types outside of the nervous system, and identifying a protein in three of four identical samples is not uncommon. We therefore used detection in three or four samples as an indicator of presence, while absence across all samples was taken to indicate true absence.

That said, the reviewer is correct that further diversity and heterogeneity within both CPN and SCPN subtypes additionally might be involved. This is an interesting question for future research, and we have added relevant text to the Discussion. 

(8) It may be helpful to mention that RPL22, while not stoichiometric, is known to have extraribosomal functions and can pull down independently from assembled ribosomes (PMID: 17381311, PMID: 28575669. Moreover, RPL22/eL22-3xFLAG has been previously used as a control for ribosome affinity-based pulldowns and could be added to citations for Figure S1 (PMID: 28625553, PMID: 28625553).

We thank the reviewer for this helpful recommendation. We have added relevant text and citations. 

Minor corrections to the text and figures:

(1) Want to confirm that in Figure 2, P adj is <0.1 is correct? 

Yes

(2) It is not necessary to show MS spectra in Figure 2.

While we understand the spectra are not strictly necessary, we respectfully submit that they enhance the figure and aid readers in assessing data quality. 

Reviewer #2 (Recommendations for the authors):

To strengthen the impact and interpretation of the authors' findings, we encourage consideration of the addition of functional validation experiments for at least one (or more) of the ribosomeassociated proteins that are differentially enriched in ScPN. This could include genetic manipulation (e.g., knockdown or overexpression) to test whether these proteins influence subtype-specific features or neuronal function. Even a limited set of perturbation experiments, such as targeting PRKCE, which is particularly interesting due to its known role in synaptogenesis, would help move the study from descriptive to a more mechanistic nature of the work.

There appear to be no issues related to data availability, ethics, or compliance, assuming all raw proteomic data and associated code for differential analysis are made publicly available.

We again thank the reviewer for this encouragement and highlighting that our work provides the foundation for further functional and developmental dynamic investigations. We view this work as providing that foundation for further investigation by multiple labs in the broader fields, beyond the scope of this paper.

eLife Assessment

This important study addresses how listeners learn the statistical properties of acoustic spaces, combining well-designed psychophysics in virtual rooms with non-invasive brain stimulation. The evidence is solid: the behavioral results are strong and show that speech understanding is best in rooms with everyday levels of reverberation, and the stimulation data are consistent with a contribution of dorsolateral prefrontal cortex, though the effects are modest and the spatial precision of TMS is inherently limited. The work will be of interest to researchers in auditory neuroscience and psychoacoustics, helping to understand how the brain copes with reverberant environments.

Reviewer #3 (Public review):

Summary:

This manuscript presents a well-designed study examining human adaptation to room acoustics, building on prior work. The psychophysical results are convincing and add meaningful knowledge to our understanding of reverberation learning. The transcranial magnetic stimulation (TMS) component shows a role of prefrontal cortex in this listening task, targeting dorsolateral prefrontal cortex (dlPFC). Cautious interpretation of the TMS results is warranted, especially given the modest statistical effects, the fact that the main TMS result of interest is a null result, and the limited ability of TMS to precisely target dlPFC in individual subjects. A surprising and interesting finding in the study is that listeners performed the speech recognition task more poorly in anechoic conditions than in those with naturalistic levels of reverberation. This is likely due to contributions of spatial release from masking provided by reverberation acoustics, which may counteract the detrimental effects of reverberation on speech perception itself. Overall, the experiments are well performed and clearly presented, improving our understanding of how the brain copes with reverberant environments.

Strengths:

(1) Well designed acoustical stimuli and psychophysical task.

(2) Comparisons across room combinations is well conducted.

(3) Virtual acoustic environment is impressive and applied well here.

(4) Timely study with interesting behavioural results.

(5) Causal evidence of a role for dlPFC in reverberation learning.

Weaknesses:

(1) Poorer performance in anechoic environments than some reverberant environments suggests and interplay of spatial release from masking and speech intelligibility that are not fully unpicked here. This could be controlled in future experiments, for example by comparing monaural and binaural listening conditions.

(2) Lack of evidence for targeting TMS to dlPFC in individual participants. This is simply a limitation of the technique which the reader should keep in mind.

(3) Most interesting effect of TMS is a null result compared to a weak statistical effect for "meta-adaptation"

Reviewer #4 (Public review):

The authors use a d' defined for 2-alternative forced choice experiments, but their data are 4-alternative (for color) and 8-alternative (for number) forced-choice. So, the d' is not computed correctly. For mAFC experiments, the authors should use the Hacker-Ratcliff (1979) method, also defined in chapter 10 of the Macmillan & Creelman textbook.

Normalization of the stimuli was arbitrary, and consequently the unexpected improvement in performance in reverberation compared to anechoic condition is still not explained. A natural normalization across different environments is to take the direct portion of the BRIR (and HRTF for the anechoic condition) and make sure that that is scaled identically across the different simulated rooms (with the reverberant tails scaled naturally). That corresponds to the situation when the sources are emitting the sound at the same level in each environment. The current study scaled the overall levels. As a minimum, it should be reported how this scaling boosted/attenuated the targets and maskers in each environment.

The potential that the listeners are tuning to individual voices, as opposed to rooms, has not been eliminated. The authors suggest that a lack of interaction with different voices is evidence that that is not the case. This is not correct: lack of this interaction just means that there are no differences in tuning between the voices. But that does not mean that the same amount of tuning is happening for each voice, as observed in previous studies. Unless the authors provide a follow-up data with randomly varying voices within each trial, these claims should be tuned down.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

This manuscript describes the results of an experiment that demonstrates a disruption in statistical learning of room acoustics when transcranial magnetic stimulation (TMS) is applied to the dorsolateral prefrontal cortex in human listeners. The work uses a testing paradigm designed by the Zahorik group that has shown improvement in speech understanding as a function of listening exposure time in a room, presumably through a mechanism of statistical learning. The manuscript is comprehensive and clear, with detailed figures that show key results. Overall, this work provides an explanation for the mechanisms that support such statistical learning of room acoustics and, therefore, represents a major advancement for the field.

Strengths:

The primary strength of the work is its simple and clear result, that the dorsolateral prefrontal cortex is involved in human room acoustic learning.

Weaknesses:

A potential weakness of this work is that the manuscript is quite lengthy and complex.

Reviewer #2 (Public review):

Summary:

This study investigated how listeners adapt to and utilize statistical properties of different acoustic spaces to improve speech perception. The researchers used repetitive TMS to perturb neural activity in DLPFC, inhibiting statistical learning compared to sham conditions. The authors also identified the most effective room types for the effective use of reverberations in speech in noise perception, with regular human-built environments bringing greater benefits than modified rooms with lower or higher reverberation times.

Strengths:

The introduction and discussion sections of the paper are very interesting and highlight the importance of the current study, particularly with regard to the use of ecologically valid stimuli in investigating statistical learning. However, they could be condensed into parts. TMS parameters and task conditions were well-considered and clearly explained.

Weaknesses

(1) The Results section is difficult to follow and includes a lot of detail, which could be removed. As such, it presents as confusing and speculative at times.

(2) The hypotheses for the study are not clearly stated.

(3) Multiple statistical models are implemented without correcting the alpha value. This leaves the analyses vulnerable to Type I errors.

(4) It is confusing to understand how many discrete experiments are included in the study as a whole, and how many participants are involved in each experiment.

(5) The TMS study is significantly underpowered and not robust. Sample size calculations need further explanation (effect sizes appear to be based on behavioural studies?). I would caution an exploratory presentation of these data, and calculate a posteriori the full sample size based on effect sizes observed in the TMS data.

Reviewer #3 (Public review):

Summary:

This manuscript presents a well-designed and insightful behavioural study examining human adaptation to room acoustics, building on prior work by Brandewie & Zahorik. The psychophysical results are convincing and add incremental but meaningful knowledge to our understanding of reverberation learning. However, I find the transcranial magnetic stimulation (TMS) component to be over-interpreted. The TMS protocol, while interesting, lacks sufficient anatomical specificity and mechanistic explanation to support the strong claims made regarding a unique role of the dorsolateral prefrontal cortex (dlPFC) in this learning process. More cautious interpretation is warranted, especially given the modest statistical effects, the fact that the main TMS result of interest is a null result, the imprecise targeting of dlPFC (which is not validated), and the lack of knowledge about the timescale of TMS effects in relation to the behavioural task. I recommend revising the manuscript to shift emphasis toward the stronger behavioural findings and to present a more measured and transparent discussion of the TMS results and their limitations.

Strengths:

(1) Well-designed acoustical stimuli and psychophysical task.

(2) Comparisons across room combinations are well conducted.

(3) The virtual acoustic environment is impressive and applied well here.

(4) A timely study with interesting behavioural results.

Weaknesses:

(1) Lack of hypotheses, particularly for TMS.

(2) Lack of evidence for targeting TMS in [brain] space and time.

(3) The most interesting effect of TMS is a null result compared to a weak statistical effect for "meta adaptation"

Reviewer #4 (Public review):

Summary:

Several behavioral experiments and one TMS experiment were performed to examine adaptation to room reverberation for speech intelligibility in noise. This is an important topic that has been extensively studied by several groups over the years. And the study is unique in that it examines one candidate brain area, dlPFC, potentially involved in this learning, and finds that disrupting this area by TMS results in a reduction in the learning. The behavioral conditions are in many ways similar to previous studies. However, they find results that do not match previous results (e.g., performance in anechoic condition is worse than in reverberation), making it difficult to assess the validity of the methods used. One unique aspect of the behavioral experiments is that Ambisonics was used to simulate the spaces, while headphone simulation was mostly used previously. The main behavioral experiment was performed by interleaving 3 different rooms and measuring speech intelligibility as a function of the number of words preceding the target in a given room on a given trial. The findings are that performance improves on the time scale of seconds (as the number of words preceding the target increases), but also on a much larger time scale of tens to hundreds of seconds (corresponding to multiple trials), while for some listeners it is degraded for the first couple of trials. The study also finds that the performance is best in the room that matches the T60 most commonly observed in everyday environments. These are potentially interesting results. However, there are issues with the design of the study and analysis methods that make it difficult to verify the conclusions based on the data.

Strengths:

(1) Analysis of the adaptation to reverberation on multiple time scales, for multiple reverberant and anechoic environments, and also considering contextual effects of one environment interleaved with the other two environments.

(2) TMS experiment showing reduction of some of the learning effects by temporarily disabling the dlPFC.

Weaknesses:

While the study examines the adaptation for different carrier lengths, it keeps multiple characteristics (mainly talker voice and location) fixed in addition to reverberation. Therefore, it is possible that the subjects adapt to other aspects of the stimuli, not just to reverberation. A condition in which only reverberation would switch for the target would allow the authors to separate these confounding alternatives. Now, the authors try to address the concerns by indirect evidence/analyses. However, the evidence provided does not appear sufficient.

The authors use terms that are either not defined or that seem to be defined incorrectly. The main issue then is the results, which are based on analysis of what the authors call d', Hit Rate, and Final Hit rate. First of all, they randomly switch between these measures. Second, it's not clear how they define them, given that their responses are either 4-alternative or 8-alternative forced choice. d', Hit Rate, and False Alarm Rate are defined in Signal detection theory for the detection of the presence of a target. It can be easily extended to a 2-alternative forced choice. But how does one define a Hit, and, in particular, a False Alarm, in a 4/8-alternative? The authors do not state how they did it, and without that, the computation of d' based on HR and FAR is dubious. Also, what the authors call Hit Rate, is presumably the percent correct performance (PCC), but even that is not clear. Then they use FHR and act as if this was the asymptotic value of their HR, even though in many conditions their learning has not ended, and randomly define a variable of +-10 from FHR, which must produce different results depending on whether the asymptote was reached or not. Other examples of usage of strange usage of terms: they talk about "global likelihood learning" (L426) without a definition or a reference, or about "cumulative hit rate" (L1738), where it is not clear to me what "cumulative" means there.

There are not enough acoustic details about the stimuli. The authors find that reverberant performance is overall better than anechoic in 2 rooms. This goes contrary to previous results. And the authors do not provide enough acoustic details to establish that this is not an artefact of how the stimuli were normalized (e.g., what were the total signal and noise levels at the two ears in the anechoic and reverberant conditions?).

There are some concerns about the use of statistics. For example, the authors perform two-way ANOVA (L724-728) in which one factor is room, but that factor does not have the same 3 levels across the two levels of the other factor. Also, in some comparisons, they randomly select 11 out of 22 subjects even though appropriate test correct for such imbalances without adding additional randomness of whether the 11 selected subjects happened to be the good or the bad ones.

Details of the experiments are not sufficiently described in the methods (L194-205) to be able to follow what was done. It should be stated that 1 main experiment was performed using 3 rooms, and that 3 follow-ups were done on a new set of subjects, each with the room swapped.

We sincerely thank the Editor and the Reviewers for their careful evaluation of our manuscript and for their constructive and insightful comments. We greatly appreciate the time and expertise invested in reviewing our work. The feedback has been invaluable in improving the clarity, rigor, and overall presentation of the manuscript.

In response to the reviewers’ comments, we have carefully revised the manuscript throughout. The revisions include clarification of the study hypotheses, re-analysis of the TMS data using a mixed ANOVA framework, additional methodological details regarding the TMS procedures and behavioural analyses, expanded justification of the statistical modelling approach, clarification of the room-acoustics paradigm, revision of figures and figure legends, additional discussion of study limitations, and a more balanced interpretation of the TMS findings. We have also substantially revised the Discussion section and improved the overall structure and readability of the manuscript.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) It is understood that this topical area is necessarily detail-heavy, but if there are ways to streamline the manuscript to more quickly arrive at key results (Figure 3?), the work might have an even greater overall impact.

We appreciate the reviewer’s feedback and have carefully revised the manuscript to address all comments from all reviewers. However, we have retained the existing order of figures and results to maintain consistency and avoid extensive structural changes that could compromise the clarity and flow of the manuscript.

(2) Minor point: I believe Equation 1 should be d' = z(H) – z(F).

Thanks for noticing this, we have fixed the equation.

Reviewer #2 (Recommendations for the authors):

(1) Line 115: Towards the end of the introduction, the hypotheses for the current study remain unclear. Please explicitly outline each hypothesis before the Methods section.

We have now specified the hypotheses tested at the end of the Introduction.

(2) Line 229: Please state the minimum MEP amplitude criterion used during TMS thresholding (usually 50 µV). Please also reference the EMG hardware and software used to measure MEPs.

We are grateful to the reviewer for noticing that a few details regarding our TMS procedure were missing in the “Continuous theta-burst stimulation” section of the Methods. We have extensively revised this section to include the required details. We did not, however, use MEP amplitude as a criterion for estimating motor thresholds. For single-pulse TMS-induced motor threshold determination, we used visual observation of the first dorsal interosseous (FDI) muscle twitch (Varnava et al., 2011).

(3) Line 248: The Coordinate Response Measure corpus contains combinations of callsigns, colours, and numbers. What was the rationale in asking participants to only identify the colour and the number spoken, and not the callsign?

The rationale for reporting only Color and Number was to ensure an equal number of keyword identifications across phrase lengths—for example, CP0 and CP1 do not contain a callsign. This has now been clarified in the Procedure section of the Methods.

(4) Lines 327–334: The analyses outlined here are unclear – it appears that there are multiple different statistical tests being conducted on the same outcome variable in this study. Given that the design includes a between-subjects factor (TMS condition) and two within-subjects factors (Rooms, Carrier Length Phrase), could the analyses be simplified by employing a mixed ANOVA as opposed to separate repeated-measures and univariate ANOVAs? If this is, in fact, the analysis that was conducted, please improve the wording. Clarification/correction is also needed surrounding the use of the term “univariate” ANOVA, as this can refer to different statistical tests.

We appreciate the reviewer pointing this out. We have re-analysed the TMS data using a mixed ANOVA design and reported it as such in the Results section. Although the numerical values have changed, the significant findings and conclusions remain the same.

(5) Line 340: Whilst the authors identify that an alpha value of 0.05 and Bonferroni corrections were used for statistical inference in two-tailed t-tests, there is no indication of the alpha value used in the interpretation of the ANOVA results. Please include this before the Results section. Furthermore, given that multiple tests are being conducted in this project, the alpha value used to infer statistical significance should be corrected in accordance with the number of hypotheses, to reduce Type I error rates (e.g., 4 hypotheses would result in an alpha inference criterion of α = 0.0125).

We appreciate the reviewer’s observation. The corrected alpha value was not explicitly reported because all statistical analyses were conducted using IBM SPSS Statistics for Windows, Version 29.0.2.0 (IBM Corp., Armonk, NY; RRID: SCR_002865). In SPSS, Bonferroni corrections are applied by adjusting the p-values rather than the alpha threshold itself. For transparency, we have now clarified in the manuscript the factors included in each statistical comparison to make the tested hypotheses fully explicit.

(6) Line 346: The sample size calculation used in the current study could be improved. It is unclear why a sample size estimation of ≥18 is used when the actual sample recruited is significantly greater than this (62). Is this because 62 participants were divided across multiple experiments in this paper? Further clarification is needed. The alpha value used in this calculation should also be corrected to account for multiple statistical models.

We thank the reviewer for noting this. We have clarified that the initial sample size estimation (n = 18) referred to individual ANOVA analyses. In the revised manuscript, we specify in each experimental section (Identity of Sound Environments and Continuous Theta Stimulation) the exact number of participants recruited per experiment, which together sum to a total of 74 participants across all experiments (also clarified in the Participants section of the Materials and Methods).

(8) Line 438: Many of the statistical tests presented in the Results section have not been outlined in the Methods section or had the rationale explained in the Introduction – this makes the analyses feel confusing and speculative. Explicitly identifying the core hypotheses earlier in the manuscript and clearly stating which hypotheses are confirmatory or exploratory would be an important improvement.

We appreciate the reviewer noticing this. We have clarified the hypotheses tested in the Introduction (4th and 5th paragraphs) and provided a more detailed account of the statistical analyses in the Materials and Methods (Statistical Analysis section).

(9) Line 565: It is unclear how the 62 participants recruited in the study were divided across each of the experimental conditions. I would recommend expanding the Participants section in Methods to outline the number of participants involved in each stage of the study.

Thanks for noticing this discrepancy—this calculation was indeed confusing and incorrect. We ultimately tested a total of 74 participants. We have specified the sample size per experiment in both the “Identity of selected sound environments” and “Continuous theta-burst stimulation” sections of the Methods, and reiterated this in the Results section to prevent confusion.

(9) Line 792: The Results section as a whole is incredibly complex and lacks structure. This could be condensed significantly – details regarding previous research should be removed from Results, as this should already be outlined in the Introduction as rationale for the current project. It would be clearer to outline each confirmatory and exploratory hypothesis in the Introduction, then identify at each stage in the Results section where it is being tested.

We appreciate the reviewer’s point. We have rewritten the 4th and 5th paragraphs of the Introduction to outline the confirmatory and exploratory hypotheses. While we have streamlined parts of the Results section to enhance clarity, we have retained contextual information for each analysis to help readers follow the logic of the findings, given the complexity and scope of the study.

Reviewer #3 (Recommendations for the authors):

(1) Introduction – Overinterpretation and Hypothesis Clarity. The final paragraph of the Introduction (page 4) discusses the experimental findings and their interpretation, which belongs in the Discussion. This section should instead clearly state hypotheses for both the behavioural and TMS experiments. In particular, the TMS experiment lacks a clear rationale: what mechanism is being tested, and what behavioural outcome is predicted? Please revise this section to focus on the theoretical motivation, clearly defined hypotheses, and expected results, and less on summarizing the results.

We appreciate this point and have accordingly deleted the final paragraph of the Introduction, as it is already incorporated into the Discussion section. We have stated the hypotheses/rationale more clearly in the Introduction.

(2) TMS – Mechanism, Timeframe, and Clarity. The manuscript does not adequately explain how TMS produces long-lasting effects relevant to the task, which occur minutes (or possibly longer) after stimulation.

(a) What is the specific timeframe between stimulation and behavioural testing?

The timeframe between stimulation and behavioural testing has been clarified in the Methods section, e.g.: “Participants exposed to ‘real’ or ‘sham’ TMS completed the familiarization and behavioural task right after cTBS procedures.”

(b) What is the evidence that TMS to the prefrontal cortex affects function on this timescale?

We have added the following paragraph to the Discussion to address the timescale of continuous theta-burst stimulation (cTBS): cTBS, as used in our study, typically induces aftereffects lasting 20–50 minutes (Huang et al., 2005; Wischnewski & Schutter, 2015). While these effects are well established in the motor cortex—with motor-evoked potential changes persisting for up to one hour—recent evidence suggests that similar durations of cortical modulation can also occur in the prefrontal cortex (Taylor et al., 2025). Specifically, studies applying inhibitory rTMS to the dorsolateral prefrontal cortex (dlPFC) during cognitive tasks have demonstrated functional effects lasting up to one hour in healthy participants (Wagner et al., 2006). Furthermore, Tupak et al. (2013) showed that inhibitory rTMS to the dlPFC leads to reduced oxygenation levels, reflecting decreased cortical activity, for at least 45 minutes—the same duration as the experimental task in our study. Given that changes in cerebral haemoglobin concentration closely correspond to neuronal activation (Liao et al., 2013), the fNIRS-measured alterations in local cerebral blood oxygenation provide an indirect but reliable indicator of TMS-induced neural modulation within this timescale.

(c) Can post-stimulation effects be objectively measured or confirmed?

Although no objective post-stimulation measures were collected in the present study, we acknowledge this as a limitation. However, previous research has shown that inhibitory rTMS to the dlPFC leads to reduced oxygenation levels—reflecting decreased cortical activity—for at least 45 minutes (Tupak et al., 2013). Given that changes in cerebral haemoglobin concentration closely correspond to neuronal activation (Liao et al., 2013), these findings indicate that fNIRS can serve as an indirect but reliable method for confirming TMS-induced neural modulation. We plan to incorporate such objective measures in future studies.

We thank the reviewer for raising these important points and have addressed them by updating the Methods and Results sections and adding a paragraph to the Discussion. We would like to clarify, however, that the TMS effects observed in our study are not weak: the statistically significant differences between sham and TMS conditions were accompanied by large effect sizes, indicating that bilateral inhibitory stimulation of the dlPFC produced a robust and consistent effect across participants—specifically, a reduction in performance, reflecting decreased improvement in speech understanding with increasing exposure to the reverberant environment.

(3) Figure 3A – Anatomical Specificity and Interpretation. Figure 3A implies precise stimulation of dlPFC and its projections to auditory cortex (A1), but the authors cannot actually target dlPFC or its connections specifically with this approach. Rather, the TMS protocol disrupts an undetermined region of PFC, with diffuse downstream effects. This should be clearly acknowledged in the figure legend and main text.

We appreciate this comment and have acknowledged this point in the figure legend and Discussion, e.g., Figure 3 legend: “Although the TMS protocol was intended to target the dlPFC, it likely affected adjacent prefrontal regions, leading to diffuse downstream effects that may have included modulation of A1.”

(4) Additionally, the Discussion overstates the evidence for a specific dlPFC → AC role in reverberation learning. The weak and poorly localized TMS effect does not support strong claims about this pathway. Please scale back this interpretation and focus more on the robust psychophysical results, which are the manuscript's stronger contribution.

We thank the reviewer for this comment. We have revised our interpretation to clarify that the proposed dlPFC–auditory cortex link is speculative, and have added caveats regarding the limited spatial precision of TMS targeting and individual variability in its effects, in the Discussion section “A role for dlPFC in statistical learning of room acoustics.”

(4a) Line 152: Extra comma after “of”? Also, why are there square brackets around “callsigns” etc.?

Fixed.

(4b) Line 156: “RRID:SCR_001622” is unexplained and likely unnecessary—consider removing.

Removed.

(4c) Line 159: Why was no ramping applied at the end of the noise? Please clarify.

Similar to Brandewie & Zahorik (2013), no ramping was applied. This has been clarified in the Methods (“Acoustic Stimuli”).

(4d) Line 207: Methods do not describe the sham TMS protocol—please add this information.

Thanks for noticing this. Information on the sham TMS protocol has been added.

(4e) Line 352: Fix bracket formatting.

Fixed.

(4f) Line 382: Sentence is grammatically incorrect—please revise.

Fixed.

(4g) Line 394: Unclear use of square brackets—clarify or standardize.

Fixed.

(4h) Line 401: It is unclear how interleaving the talker and length ensures a different room each trial. Aren't these variables independent?

The reviewer is correct: the only variable that was pseudorandomized was room order, to prevent carry-over effects, similar to Brandewie & Zahorik (2013). This has been clarified in the Methods section.

(4i) Figure 1: Clarify that AI-generated images refer only to the room images, not other components.

Fixed.

(4j) Figure 2A: Confirm that “overall” includes all speakers and durations—clarify in legend.

Fixed.

(4k) The interesting duration effects in Figure 1D are not discussed in the text and appear before overall room effects in Figure 2A—please reorder and comment on these results.

Fixed.

(4l) Supplementary Figure 2: Caption contains a typo (“Lecture Room/Open-Plan Office”).

Typo has been fixed.

Also, I recommend adding this result to the main figure set—e.g., include overall d′ for all six talkers in Figure 2 alongside rooms (2A) and lengths (2D).

We thank the reviewer for the suggestion. Including overall performance for all six talkers in Figure 2 would require substantial restructuring and risk making the figure crowded. We have therefore retained these results in the Supplementary Materials (Supplementary 2 and 3), as originally presented.

(4m) Line 555: Phrase “to better understand” could be clearer—consider rewording.

This section has been reworded.

(4n) Lines 587–592: The lack of main effect of TMS is helpful, but more important is whether interactions between TMS and room/length variables occur. Please report these interactions, as they are central to interpreting the TMS effects.

We appreciate the reviewer highlighting this. We have reviewed this analysis and reported the interaction Condition x CP length as follows: “A mixed ANOVA with a between-group factor of Condition and within-group factors of room and CP length confirmed that performance in these two populations was comparable, with no significant main effect of TMS conditions observed (‘sham’ vs. no exposure to TMS): [F (1,31) =0.01, p=0.91, ŋp2 = 0.00], and no significant interaction Condition x CP length was observed: [F (3,93) =0.48, p=0.69, ŋp2 = 0.01]; confirming that participants experiencing ‘sham’ TMS did not perform significantly differently from the ‘no exposure to TMS’ population”. 

(4o) Line 601: Reiterate the timeframe of the TMS-behaviour gap. Is there supporting evidence that TMS can affect behaviour over this duration? Could null effects reflect fading TMS efficacy?

We appreciate the reviewer pointing this out. We have clarified the timeframe of TMS stimulation in both the Methods and Results, e.g.: “The procedure began with TMS manipulation, and although the behavioural task lasted 45 minutes, the inhibitory effects of TMS extended for at least 60 minutes post-stimulation (Huang et al., 2005; Gamboa et al., 2010; Hoogendam, Ramakers, & Di Lazzaro, 2010; Romero et al., 2022).” However, we cannot dismiss individual differences in the duration of TMS effects, nor differences in efficacy duration between anatomical areas (motor cortex vs. dlPFC). We have noted this in the Discussion section “A role for dlPFC in statistical learning of room acoustics” (Pallant, 2011).

(4p) Figure 3I: The “meta-adaptation” effect is marginal in both Exp 1 (p = 0.03) and Exp 2 sham (p = 0.04). These should be interpreted cautiously, given their statistical fragility.

We appreciate this comment. We have now calculated effect sizes for all Wilcoxon signed-rank tests (Pearson’s r) and report them. For the two comparisons noted by the reviewer, the effect sizes are medium (Exp 1) and large (Exp 2). We are therefore confident that, even where the p-values are not extremely low, the statistical differences are reliable.

(4q) Line 696: Reverberation is described as “common,” but it is nearly universal. Consider rephrasing to reflect this.

We appreciate this suggestion and have rephrased this line.

(4r) Line 816: The authors state that TMS reduced overall performance, but the earlier ANOVA (lines 587–592) shows no such effect. Please correct this discrepancy.

We appreciate the reviewer noticing this. This section has been clarified: the lack of statistical significance at lines 587–592 relates to the comparison between a subset of ‘no-TMS-exposed’ listeners and ‘sham’-TMS-exposed listeners, made only to demonstrate the absence of placebo effects in the sham sample. Following the reviewers’ suggestions, we also re-analysed the data using a one-way ANOVA; this slightly changed the numerical values of the reported main effect but did not change the statistical outcome.

Reviewer #4 (Recommendations for the authors):

(1) Lines 201–202: It's not clear what is meant by combination and by carrier length here.

This section has been rewritten for clarity.

(2) Line 330: What is meant by “Univariate” here? I think this was a mixed ANOVA, with a betweensubject factor of TMS exposure and the remaining factors within-subject.

We appreciate this suggestion; we have re-analysed this section to use a mixed-ANOVA design. The numerical results differ, but the statistical outcome remains the same.

(3) Lines 335–343: This is impossible to follow if one does not understand that there were 3 followup experiments.

Thank you for highlighting that this section was confusing. We have rewritten it to clarify the following: “Three follow-up experiments were performed (univariate ANOVA) to assess whether speech understanding was affected by room context (i.e., the third room in which Open-Plan Office and Underground Car Park were learnt), with one between-subjects factor: room context (levels: Anechoic Room, Living Room, Lecture Room, and Highly Reflectant Room).” We have also added the following earlier in the Methods: “Additionally, we performed three follow-up experiments in different groups of listeners, assessing performance across combinations of three rooms: (1) Anechoic Room/Open-Plan Office/Underground Car Park (10 naïve listeners); (2) Living Room/Open-Plan Office/Underground Car Park (11 naïve listeners); and (3) Highly Reflectant Room/Open-Plan Office/Underground Car Park (10 naïve listeners). These conditions were used to determine whether a specific room combination was required to observe improvements in speech performance with increasing exposure to room acoustics i.e., with increasing carrier phrase length—and were assessed in the same way as Brandewie & Zahorik (2013).”

(4) Lines 414–416: The review of Tsironis et al. (2024) (doi:10.1177/23312165241273399) does not provide strong evidence that there are multiple scales for adaptation to room reverberation (most adaptation effects stabilize within 1 sec).

We apologize for this mistake, which arose from an issue with our reference manager. It has been corrected to: Robinson, Harper, & McAlpine (2016), Nature Communications, and Simpson, Harper, Reiss, & McAlpine (2014), Journal of Neuroscience.

(5) Line 427: The supplementary figure shows that many subjects did not achieve asymptotic performance.

We appreciate the reviewer pointing this out. The fittings have been extensively reviewed; please see the Methods and Results for the new fitting analysis. Indeed, some participants, although very slowly, keep improving over time without reaching clearly asymptotic behaviour. This section, however, referred specifically to the point at which performance stabilised within ±10% of final performance.

(6) Line 428: The ±10% statistic is random (as discussed below). And why switch to HR now? And what is its meaning when the HR did not converge by the end of the run?