Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

Zhang et al. report on an ambitious study that investigates multiple aspects of the neural and behavioral underpinnings of auditory-motor surprisal in the context of an auditory-motor learning paradigm (piano keyboard). Using an intricate design comprising several sub-parts and control procedures, they report that early ERPs (50-100 ms latency) reflect violations of established key-pitch mappings.

Strengths:

This is a carefully devised and executed study. The paradigm is quite intricate and, at the same time, addresses multiple aspects of auditory-motor learning, and does so in a rigorous way.

Weaknesses:

Perhaps because of the exhaustive approach, it is sometimes difficult to follow which parts of the experimental design the results come from; there are some questions regarding appropriate statistical methods, the inclusion/treatment of musical background in participants, and the nature (latency & extent) of the identified neural components that detect auditory-motor violations.

Reviewer #2 (Public review):

Summary:

Zhang et al. report an EEG study (n=18) of participants playing a keyboard where the correspondence between keys and pitches is varied to introduce sensory-motor mismatches (discrepancies between sensory inputs and expected sensory consequences of motor commands). They find that the auditory N100 amplitude is enhanced for the initial keystroke following a mapping switch but rapidly attenuates for subsequent keystrokes (showing rapid updating of the forward model), whereas the motor-related P50 amplitude only differentiates trained versus untrained mappings after 30 minutes of goal-directed practice (potentially showing timescales of inverse model updating). Using parallel univariate and mTRF decoding analyses, they conclude that forward models (mapping action to predicted sound) update almost instantly to track short-term context, while inverse models (mapping sound to motor commands) update slowly and require extended, targeted practice.

Strengths

(1) Methodological innovation:

The study utilizes an interesting, continuous auditory-motor paradigm that moves beyond standard trial-by-trial oddball designs, offering a more ecologically valid measure of trial-to-trial adaptation.

(2) Analytical elegance and rigor:

The combination of traditional univariate ERP analyses with multivariate temporal response function (mTRF) decoding is elegant, allowing the authors to successfully dissociate overlapping auditory and motor variance streams.

(3) The dissociation between the rapid adaptation of the N100 forward model and the slower adaptation of the P50 inverse model is interesting.

Weaknesses

(1) Confounded passive listening baseline:

The passive listening control condition lacks an orthogonal behavioural task (e.g., an occasional oddball detection task). Active playing inherently necessitates focused attention on auditory feedback to monitor performance, whereas passive playback does not. The globally weaker stimulus-evoked pattern at electrode Fz during passive listening strongly suggests that the absence of an N100 effect in this condition may simply reflect a lower state of attention, rather than isolating the absence of a motor-driven forward prediction, in particular because the pure sensory suprisal was also enhanced for "firsts" notes, so this could also lead to stronger N1, but this effect may be masked.

Here, our goal is to probe surprisal resulting from natural deviations of the expected sensorimotor map, and to test whether the observed response can be accounted for by the auditory components alone. In previous work, passive listening (without an explicit behavioral task) has been widely deemed sufficient to measure auditory surprisal (cf. Di Liberto 2020). Because the listener is not privy to the order of firsts and others within a session, any general attentional effects would be expected to influence all notes and therefore cannot explain the selective enhancement observed for “first” notes which follow a map change.

(2) Overclaimed theoretical novelty:

The conceptual framing leans excessively on the authors' specific "MirrorNet" framework, presenting foundational, decades-old tenets of the motor control literature (i.e., unsupervised exploration for forward models vs. supervised skill acquisition for inverse models; Wolpert, Jordan, both in the nineties) as their own novel "conjectures." This theory-heavy introduction obscures the paper's actual empirical contribution to the design and the interesting question regarding the distinct temporal adaptation scales of forward versus inverse models. I think some rewriting can improve the paper.

Thank you for pointing this out. It was not our intention to present the work of Wolpert etc. as a novel conjecture. We substantially revised the Introduction to emphasize that our contribution builds upon that theoretical framework and is also a study of how this framework evolves over time. We have cited Wolpert in the Introduction, and have now integrated the forward and inverse pathways more clearly into our hypotheses about the different effects of long- versus short-term sensorimotor experience on the MirrorNet framework.

(3) Misplaced surprisal terminology:

In a similar vein, I find the use of the term "auditory-motor surprisal" more theoretical grandstanding than actually useful. The significance statement claims to "extend this principle from sensory processing" but in fact, the concept of sensory motor unexpectedness is again a staple of the forward motor literature. Moreover, nowhere in the paper do they actually estimate sensorimotor surprisal. While the authors compute surprisal for their auditory baseline using IDyOM, their central sensorimotor analysis relies entirely on a simple categorical mismatch (first vs. subsequent keystrokes). The phenomenon can equally be referred to by its established nomenclature-"sensorimotor mismatch" or "sensory motor unexpectedness".

In the revised Introduction, we added a discussion of the relationship between surprisal and contextual predictions to clarify our terminology. In practice, the terms auditory-motor surprisal and sensorimotor mismatch refer to closely related phenomena. However, we chose the term surprisal because it emphasizes that prediction violations depend not only on the overall frequency of an event, but also on the context in which it occurs. In the surprisal literature, an event can be unexpected because it violates predictions generated from recent context, or long-term statistical regularities, or prior experience, even if the event itself is not objectively rare.

This distinction is important for our paradigm. A given note may occur frequently throughout the experiment and therefore is not rare in an absolute sense. Nevertheless, the same note may be highly surprising if it occurs immediately after a key-pitch map change, thus violating the participant's sensorimotor predictions. We therefore use the term surprisal to emphasize the role of contextual expectations rather than simple deviance or rarity.

We finally agree that, in the absence of an auditory-motor equivalent of models such as IDyOM, our study does not provide a continuous estimate of surprisal. Instead, we use the distinction between first and keystrokes as a categorical approximation of high- and low-surprisal events. Developing computational models that estimate continuous auditory-motor surprisal from the preceding sensorimotor context would be an interesting direction for future work, and we have added a note concerning this in the Conclusion.

(4) Incremental conceptual advance regarding the N100:

The paper frames the N100 finding as a major discovery, but as far as I know, the attenuation of the auditory N1 to self-generated sounds via accurate motor prediction-and its enhancement during sensorimotor mismatch - is one of the most heavily documented phenomena in the auditory-motor literature (e.g. Timm et al., 2013; Bendixen et al, 2012; 2013). As far as I'm concerned, the authors should clarify that the novelty lies in the novel, elegant design that provides a new way to correct for non-sensory-specific motor-induced attenuation, and characterizing the distinct adaptation timescales of forward versus inverse models -- not in demonstrating N100 modulation by sensorimotor mismatch, which is well-documented, AFAIC.

We agree now that the main finding of the paper is not discovering N100 as a signature of sensorimotor mismatch and we have revised the Introduction as discussed above. We now instead emphasize how it evolves over time and connect it to behavioural studies of sensorimotor perturbation where a behavioural adaptation is observed after one trial. We also incorporated the suggested literature on the N100 in the Introduction and Discussion because it shows that this neural signal has been previously seen in sensorimotor mismatch studies.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

As very general feedback, I would encourage the authors to revise the manuscript so that it is much clearer which results come from which part of the experiment. For example, it took me a while to figure out that the ERP results in Figure 3 came solely from the 'Variable map playing' parts of the study (and perhaps only from the Pre-test phase?).

To improve clarity, we have rearranged the order of the figures and the respective text to organize the article into three main parts: the Variable Playing Task (Experiment I), the Training (Experiment II), and the TRF analysis (Experiment III). The paradigm panels are now closer to the Figure explaining their results. The Figure outlining how these tasks are carried out (previously Figure 2D) during one experimental session has been relegated to the supplementary materials.

Major:

(1) Statistics

(a) I couldn't shake the impression that the authors are treating the statistical analyses a bit too casually. Some analyses use parametric (ANOVA, t-test), others non-parametric tests (Wilcoxon) or bootstrapping, without explicitly reasoning for one or the other; there are also some examples where I believe no correction for multiple comparisons is applied, but should be applied (e.g., tests in Figure 4?).

We have added information in the Methods section to clarify the statistical choices. Here is a summary of our reasoning:

Bootstrapping (to find the difference between first and others): this was to account for the imbalance in class sizes and is more conservative than parametric alternatives. That being said, parametric tests do converge on the same result (Figure 6C, main effect of keystroke type in the 2-way within-subjects

ANOVA).

For Figure 4, we have replaced the pairwise tests with a more robust linear mixed-effects model to capture the relationship between the number of previous keystrokes and amplitude. This avoids multiple pairwise comparisons between conditions. However, the conclusions of the figure remain unchanged: the amplitude difference increases with the number of previous keystrokes.

Wilcoxon tests (subject-wise differences): With N = 18 participants, we do not meet the conventional threshold for normality (n > 30). The Wilcoxon test was therefore the appropriate choice.

Within-subjects ANOVA (training and first vs. others): A two-way within-subjects ANOVA was used when comparing two conditions. Within-subjects designs with N = 18 do not violate ANOVA assumptions in the same way between-subjects designs would, since the critical assumption is the sphericity of difference scores rather than marginal normality.

(b) Relatedly, I am not sure it is ok to run uncorrected statistical tests to identify 'time regions of interest', and to then zoom in on these and run additional statistical tests on them; this seems conspicuously like double dipping?

We did the uncorrected tests as an exploratory analysis, but we would have arrived at the same result if we chose timepoints of interest based on the literature (P50 and P100 were both well-documented; P250+ also potentially could have had an effect based on the literature (Lutz et al., 2013 for example), but in our experiment we did not find it).

(c) Comparing firsts versus other keystrokes: I wonder whether the bootstrapping procedure is necessary? In the MMN literature, this imbalance (oddball vs. standard) has not been an issue, as far as I am aware (or it has not been addressed?); I can follow the authors' reasoning for addressing this imbalance, but would feel more comfortable with the bootstrapping procedure if the authors can show that there is only a quantitative, but not a qualitative difference between statistics with bootstrapping vs. without bootstrapping (i.e. having a large imbalance between firsts and others keystrokes).

While bootstrapping is less commonly used in some ERP studies, we chose this approach because it provides a robust estimate under class imbalance between conditions, as is typical in oddball-like paradigms. The effect of firsts versus others keystrokes remains significant under standard parametric analyses, consistent with the main effect observed in the two-way ANOVA (Figure 6C).

(d) In addition, is it really correct to derive a null distribution only from the other keystrokes, as opposed to from both firsts and other keystrokes?

Our procedure defines a null distribution based on differences between randomly sampled other keystrokes. This allows us to quantify whether the observed amplitude difference between first and other keystrokes exceeds what would be expected from differences within the other condition alone. Under the null hypothesis, the first–other difference does not differ from the distribution of differences obtained by comparing randomly selected subsets of other keystrokes of equal size.

(2) Latency and duration of ERP differences

I was rather surprised by how early the effects appear to be. Coming back to the MMN paradigm: here, the latency of the peak MMN for oddballs is typically in the ~150-250 ms range, i.e. in P2 territory. Granted, the effect can be initiated in the N1 component range, but then it persists through P2; in the current paradigm, the effect is very selective to the N1 (or even the P50 latency for Pre- vs. Post-training comparisons, which puts this effect squarely in the primary auditory cortex). I would encourage the authors to explore this apparent discrepancy with respect to the MMN latency a bit more; is this related to passive vs. active paradigms? But why does the effect not persist and is seemingly restricted to a brief time window? Presumably, the auditory-motor mismatch, once it is detected, will have 'downstream' effects?

The early N100 effect has been reported multiple times in previous literature so we don't find this result surprising. It's possible that there are downstream effects that we're not seeing here. For example, we show in Figure S13 that the playing ERP is likely a linear sum of auditory and motor signals. The motor ERP also peaks at around 150, so in theory it could obscure the classic MMN. This point was mentioned in the Discussion (line 290).

(3) Musical background of participants

The authors state that some participants had more than 10 years of formal musical training, but that "none of the musically trained participants played piano as their primary instrument". How many of those nevertheless played piano? And how did this affect their performance? It would have been much cleaner to restrict participants to non-musicians...

I am not convinced that performance in the training task is an appropriate proxy for musicianship (as the authors suppose on page 10). In general, I think the consideration of musicianship in the study is by far the weakest and should probably be left out.

That being said, it is unfortunate that not more information on participants' background is provided, and that the authors did not exclude musicians, as this likely also has an impact on the results, since they presumably have had a stronger 'natural' key-pitch mapping than non-musicians.

Participants did fill out a questionnaire adapted from the Goldsmiths Musical Sophistication Index previously used in our laboratory’s other studies.We found no correlation with the GSI general score, nor the subscores. We have added the questionnaire results in the supplementary materials and the correlation plots for the overall musical sophistication score and the perceptual abilities score (the subscale most closely associated with the demands of our task). Nevertheless, for our use case, we do not believe that the questionnaire is more relevant for predicting sensorimotor learning abilities than the actual performance during training. For example, aspects of emotion and social engagement in music are also measured, which we don’t find to be relevant to musical learning abilities, and perceptual abilities are self-reported.

(4) How were peak amplitudes determined? (They should not be determined by simply picking the maximum, as this is susceptible to outliers, but instead as an average over a pre-defined time window.) In general, the description of methods would benefit from being more detailed.

We indeed computed the peak response as the maximum over a 40 ms window. However, given the large number of trials, and that the signal was already low-pass filtered to 30 Hz, corresponding to a ~33 ms cycle, it is unlikely that the estimate is significantly affected by transient noise or spurious peak fluctuations. The concern about outliers would be more relevant for single-trial data.

(5) Figure 3A and 6A 'Pre-training ERP' seem to be identical; why is that? Shouldn't Figure 3A essentially show the average of Figure 6A 'Pre-test ERP' and 6A 'Post-test ERP'?

Yes, it is indeed identical. Figure 3A is the variable map playing without the influence of any other tasks, therefore it’s the pre-training ERP.

(6) I had trouble following the results in Figure 4B/D. Why does 4B only go as far as 3 previous keystrokes, but 4D goes as far as 7? Maybe I am misunderstanding something here?

We showed only the contexts for which there were more than 300 trials, which we noted in the Methods section. There are fewer firsts in general, and fewer trials for higher numbers of keystrokes in the context. Therefore the 300 trial cutoff allows us to go up to 3 previous keystrokes for Figure 4B, but 7 previous keystrokes for Figure 4D.

(7) In Figures 3E and 3F, eyeballing and comparing the null and listen vs. null distributions (3E) with the First vs. Other distributions (3F), I had trouble wrapping my head around how the ones in 3F can be highly significantly different (p<0.001), while the others in 3E are not. (See also my question above re the calculation of the null distribution.)

Regarding Figure 3E, as detailed in the Methods section, the comparison between playing and listening was performed using a permutation test, whereas the p-values for comparisons between playing and null or listening and null were computed empirically as the proportion of values in the null distribution that exceeded the observed statistic. This is because playing and listening are both empirical (non-null) distributions, making a direct permutation test more appropriate for their comparison.

(8) Please clarify whether or not the decoders were compared to all keystrokes (firsts and others)?

The decoders were compared to all keystrokes in the main text (Figure 7), but a sized-match sample of firsts and others yielded the same conclusion (Figure S12).

(9) Last paragraph of Disentangling auditory...

If I understand it correctly, then neither ANOVA revealed an interaction; yet, the authors computed post-hoc pairwise comparisons nevertheless?

There is an interaction for P50 according to the ANOVA (Figure 6C). We followed up with post-hoc comparisons to investigate whether this interaction is driven by a particular key-pitch map.

(10) Figure S9: More information is needed re the TRF decoder; why such a short time window (as opposed to (showing) the ERP epoch -.2 to .5 s)? What does it mean for the decoder to have its peak at 0 s?

Since we used an inverse TRF formulation, the target reconstruction corresponds to a sparse impulse vector with value 1 at keystroke onsets and 0 elsewhere. As a result, only the temporal location at t=0 is of interest, with the expectation that the reconstruction should be flat outside this point. As a sanity check, we verified that averaging across onset-aligned windows reveals a clear peak at t=0, confirming that the model captures the expected temporal alignment between keystrokes and reconstructed responses.

Minor:

(1) Please include line numbers in the revised document to facilitate the review of the manuscript.

(2) Baseline period: either baseline correct to 100 ms, or show the entire 200 ms baseline period in the figures.

No baseline correction was applied to the ERP signals. Instead, data were re-referenced to the mastoids and band-pass filtered (1–30 Hz) to reduce slow drifts and high-frequency noise. As shown in Figure S5, the pre-stimulus baseline period does not exhibit systematic drift across conditions, consistent with stable baseline activity following preprocessing.

(3) I was surprised to read that the authors used Sennheiser 650 headphones - surely they introduce significant electrical interference?!

We have previously used headphones in EEG experiments in our lab without issues (cf. Cantisani 2023, Di Liberto 2020). In preprocessing, a notch filter at 50 Hz is applied to remove line noise, and ERP analyses are further low-pass filtered at 30 Hz to isolate the relevant evoked response components.

(4) ICA should be run on continuous data to avoid situations where an eyeblink cannot be accurately identified (and removed) because it's cut off by the epoch (and this way it would remain in the epoch and contribute noise).

ICA was indeed run on the continuous data (10 minutes for each task). We clarified this in the Methods section.

(5) The supplementary video was not available.

We have let the eLife team know about this.

(6) Figure 2F: I believe the x-axis tick marks should read Block1 and Block2, instead of Pre and Post? Please clarify (also in the corresponding text) whether this is averaged across Pre-training and Post-training sessions, or only for one of them?

Thank you for pointing out the error, it should indeed read block 1 and block 2, and has been updated. Both take place during the 30-minute training session, which consists of 2 blocks.

(7) Figure 3: It wasn't clear to me how only significant channels are shown.

We applied a mask so that only the significant channels are coloured according to amplitude difference. Non-significant channels are shown in white. The explanation for this is now found in Results > Experiment II > Effects of targeted skill acquisition training.

(8) For the decoder analyses, how did the authors determine that investigating/using the same electrodes for auditory vs. motor ERPs is appropriate? I am aware that ERPs evoked by the auditory cortex are maximal at fronto-central electrodes; is the same the case for motor ERPs?

We did not perform any pre-selection of channels for the decoder analyses. All channels were included in model training and prediction, allowing the decoder to learn data-driven spatial weights for reconstruction without imposing priors about channel relevance for auditory or motor processing.

(9) Figure 4A/C: The stems represent keystrokes during the Variable map Pre/Post test? This indicates that this particular participant often only played 3 notes?

Participants occasionally paused after producing short sequences of 3–5 notes. This behavior varied across individuals, with some producing near-continuous sequences with brief (< 1 s) pauses, and others inserting longer pauses (2–3 s) between melodic segments. Participants were instructed to generate short, varied melodic motifs and to avoid repeating identical sequences.

(10) Figure 5E: Were these based on size-matched comparisons, i.e. similar to the method the authors applied to the other analyses comparing first vs. other keystrokes?

The figure shows the means without size matching, but using size-matched comparisons doesn’t change the conclusions of the figures; we added this analysis in a supplementary figure.

(11) Figure 6C and 6G: there seem to only be 16 and 17 datapoints, respectively?

Figure 6C: We double-checked in the code and SVG file and there are indeed 18 subjects and 18 points.

Some points are not clearly visible in the figure due to very close overlapping.

Figure 6G: We unintentionally excluded one subject from the plot by setting the x-axis limit to between 2 and 4 on the training score. We have now adjusted the plot so that all subjects are visible.

(12) Figure 6C: Why an ROI here, but not elsewhere?

The ROI selection was based on prior ERP studies reporting robust auditory responses over central electrodes and motor-related error responses over frontal midline electrodes (Gehring 1993, Lutz 2013).

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

This manuscript presents compelling evidence from a wild chickadee population linking heritable spatial cognition to extra-pair paternity success, supporting sexual selection via good genes in a food-caching species. The integration of RFID cognition tests with ddRAD paternity assignment is methodologically strong and timely for behavioral ecology, though causal mechanisms and confounds warrant clarification.

Overall, a major revision of the manuscript is recommended, addressing the points below.

(1) Confirmation of manipulation and treatment effects.

The central claim hinges on spatial cognition driving EP siring, but direct evidence that cognition predicts observed copulations (vs. post-copulatory mechanisms) is absent. While territories do not cluster by performance (Figure S4), quantify male aggression/movement data during fertile periods to rule out intrusion-based EPP. The authors should provide metrics like nearestneighbor distances for EP sires or playback responses linking cognition to dominance, as in prior chickadee work. Without this, causal female preference remains correlational.

We do provide the mean distance to all known EP sires in Figure S2, in addition to the known neighbors coded by cognition and EPP (Figures S3 and S4). Unfortunately, we do not have data with playbacks for this set of individuals, though we have shown that males respond to threats from high or low elevation birds equally, which provides a potential proxy for cognitive performance and dominance (e.g., high elevation birds perform better on the task than low elevation birds, and low elevation birds are dominant/,more aggressive than high elevation birds; Kozlovsky et al. 2014, Beh Ecol and Sociobiol; Branch et al. 2015, Behaviour; Branch & Pravosudov 2016, Ethology).

As mentioned in discussion of the manuscript, we do not see a significant relationship between dominance and task performance in our system (Heinen et al 2021) – this is also true for the closely-related black-capped chickadees (Robayo Noguera et al 2025). This is not to say that social dominance status does not affect female preference or choice, but that data is outside the scope of this work. We would like to highlight that we’ve shown high repeatability in individual task performance and shown a strong gene c basis for spa al learning and memory performance (Sonnenberg et al. 2019; Branch et al 2022; Semenov 2024, Current Biology). While social dominance status is a rela ve trait and known to change with me and age (eg adults are dominant to juveniles).

From discussion:

“Furthermore, while higher social dominance status is associated with access to better territories in chickadees (86), we see no association with dominance status and spatial cognitive abilities in our system (46) or closely related black-capped chickadees (81). While it is possible that our results reflect some unmeasured trait(s) linked to spatial cognitive ability, such as boldness, aggression, or increased exploratory behavior (e.g., 32), previous data from our system do not support these additional alternative hypotheses. Chickadees with enhanced spatial cognitive abilities are not more aggressive (78) nor do they show higher rates of exploratory behavior (e.g., higher space use) (79).”

We agree that the results we present are correlational. A causal relationship is outside the scope of this research, as we cannot manipulate cognition in the wild and chickadees will not breed in captivity. The strength of our approach lies in multi-year data collection and the ability to compare among the social and extra-pair males, as well as using what we know about the system and species to rule out additional explanations, including age.

(2) Female cognition-EPY link inconsistency.

Poor female cognition predicts more EPY (first-20-trials: offspring-level χ²=6.21, P=0.013; nests: χ²=6.79, P=0.009), but not for full-task (P>0.5). The authors should discuss why (e.g., learning speed vs. memory stability) and add exploratory correlations (female errors vs. EPY proportion). They should soften claims in the Discussion section of "female-driven" without consistent support and should frame this as a hypothesis.

Absolutely, we agree that this is an interesting nuance to the results regarding female cognition. While number of errors on the first 20 trials and across the entire task are highly correlated, this is not a 1-to-1 relationship (Figure S7a). We suggest that performance in the first 20 trials reflects memory acquisition, while performance across the full task reflects memory retention and recall (Sonnenberg et al. 2019) – both critical components of spatial learning and memory for food-caching birds.

Previous work has shown that performance in the first 20 trials and across the entire task is linked to survival (Sonnenberg et al. 2010) and longer lifespan (Welklin et al. 2024) – meaning both metrics reflect fitness. In the discussion, we suggest females may be compensating for their poorer abilities by seeking EPY, but this is speculative, as we do not have data beyond the correlative relationship we report and cannot provide more insight to the difference between the first-20 and entire task. This said, it is not only poor performing females that have EPY in the nest and we included the female/mother identity as a random factor in our models (see Statistical analysis section of Methods). Certainly, further investigation into female task performance and mate choice is warranted.

Edit to MS:

In the discussion we have edited the sentence to be more specific to our findings:

“Indeed, females with poorer spatial memory acquisition (made more errors on the first 20 trials) had more extra-pair young in their nests, while social male cognitive performance did not predict EPY in the nest.”

(3) Cognitive task sensitivity and validity.

Mean errors aggregate learning curves effectively, but single feeder-assignment (nonpreferred) confounds neophobia/motivation with spatial ability. The authors should report trial-by-trial improvements (Figure S7 subset) or criterion-to-learn metrics. Justify excluding high-error birds (<3 mean); sensitivity analysis needed to check bias toward high performers.

We respectfully disagree that our task lacks sensitivity or validity. The criterion-to-learn or trials-to-criterion metric has been criticized for decades and should not be used in studies comparing individual variation, in our opinion (e.g., Pravosudov 2022, Current Opinion in Behavioral Science; Harrington & Lambert 2025, Biology Letters).

We use metrics based on the nature of our task to assess performance and ensure birds have learned before we include them in our analyses, for instance, all birds made < 3 errors on average and completed at least 20 trials. Random chance performance on our task is 3.5 errors (7 possible errors), therefore, birds that make more than 3 errors have not learned the task and therefore would not be included in analyses. It should be noted that this is very rare and typically if birds are excluded its because they do not complete 20 trials.

See Testing spatial cognition section of the manuscript:

“In addition, birds were included in analyses if they performed at least 20 trials and made fewer than mean 3 errors across the 4-day testing period.”

We can certainly understand concerns about individual differences in motivation and neophobia, however, we have also considered this and made efforts to address these issues. That said, we do rely on birds to participate willingly in the spatial task and there may be some bias associated with those that participate vs. those that do not that we cannot account for. Chickadees, as a caching species, are particularly well-suited for our work as they appear to have infinite motivation to obtain and store food items in the wild (and individuals indeed differ in this, hence the differences in the number of trials completed, which we control for in our analyses). We know this not only from our study but work from many researchers, where birds have ad libitum food and continue to cache. Regarding neophobia, birds are introduced to the feeder array in stages, as we explain in the methods, and no humans are present during testing.

“Each array consisted of eight equidistant RFID-based feeders on a square (122 x 122 cm) aluminum frame suspended ca. 4 m above the ground (Figure 1). Each feeder is equipped with a small, motorized door. Prior to testing, we kept the feeder doors of the arrays open for approximately one month. Next, the feeder doors were closed and programmed to open for any bird with a PIT tag, this allowed birds to habituate to the motorized feeder doors for one week. Finally, we measured the spatial learning and memory abilities of mountain chickadees using a 4-day task. The spatial learning and memory task involved pseudo-randomly assigning each bird to a single feeder in the 8-feeder array that was not its most-visited feeder during the previous two habituation stages.”

Finally, using the first-20 and 4-day task performance metrics we’ve shown relationships between survival, longevity, genetic variation, and reproductive output, while seeing none of these relationships with the cognitive flexibility task (all with different groups of birds over the years), which we find to be the most compelling evidence that our metric is valid and sensitive.

(4) Paternity assignment robustness.

ddRAD-CERVUS with bimodal LODs (Figure S8) is solid, but unassigned EPY (social-genotyped but no sire) implies missing sires (~?% of EPY?). Include all alive males as candidates yearly? Test power simulations for LOD thresholds. 2019 exclusion justified, but multi-year SNP alignment could boost resolution.

One of the limitations or challenges of our system is that the birds inhabit a highly contiguous forest and our field site is not demarked by boundaries or barriers, meaning we do have undetected males just outside our field site that likely sire offspring and we have no data for. That said, we were able to assign paternity to 630 out of 732 offspring, giving us a success rate of 86%. We have now added this to the first paragraph of the results. For all 732 chicks we knew the social males genotype and could ID presence of EPY, but in that 14% we could not ID the EP male specifically. We did include all alive males as potential sires. This includes males that may not have been nesting in our boxes that particular year, but were detected alive in the previous winter testing season that we were able to genotype.

We tried a multi-year SNP alignment first, but obtained stronger paternity assignments and differentiation between first and second-tier candidate sires when we ran each year separately. Running the SNP analysis for each year separately resulted in more SNPs to use in each year which increased our ability to confidently assign paternity.

(5) Mechanistic speculation vs. data.

Discussion invokes hippocampus genes (GWAS priors) and good genes, but no offspring cognition/survival data. Label as hypotheses; suggest tracking EPY recruitment. No brood size costs for EP sires is key, but monitor long-term nest investment (e.g., feeding rates).

Indeed, these are informed speculations/hypotheses based on our previous work showing the genetic bases of cognition and high levels of heritability (Branch et al 2022; Semenov 2024, Current Biology). We also know that juvenile survival is predicted by performance on our spatial cognitive task (Sonnenberg et al 2019, Current Biology). However, we do not have offspring survival for these particular EPY (past fledging the nest). We recruit about 5% of the young back into our study site (Whitenack et al. 2025), which makes it difficult to make meaningful inferences at this point. Though, as we continue to collect data in this system we hope to obtain a sample size to address these questions.

We have collected data on feeding rates at the nest via RFID in some years, however, these measures come with additional caveats as they do not control for the amount/quality of food. Though, preliminary analyses suggest no difference in feeding rates based on cognitive abilities.

We use the mass of the nestlings at Day 16, which is a common proxy for survival likelihood in Passerines, and we know individuals of higher mass are more likely to survive and be recruited back into the system (Whitenack et al. 2025).

Reviewer #2 (Public review):

Summary:

In this study, the authors ask whether spatial cognition is under sexual selection in mountain chickadees. To do so, the authors examined a large dataset that includes a) spatial cognition data for both males and females (obtained via use of a clever RFID-based feeder system) and b) social and extra-pair paternity nesting data. As predicted, males with higher spatial cognition sired more extra-pair offspring, and extra-pair sires had, on average, higher spatial cognition scores than the males they cuckolded. Interestingly, females with lower spatial cognition scores were more likely to seek extra-pair copulations, potentially to compensate for their own low spatial cognition. Surprisingly, there was no difference in spatial cognition scores between males that sired their own offspring and those that lost paternity at the nest. Also surprising was the fact that there were no differences in patterns of extra-pair paternity and spatial cognition between high- and low-elevation sites. The latter is particularly surprising in that spatial cognition should be under stronger selection at the high elevation site. Overall, this is a fascinating study that demonstrates that spatial cognition - a trait under natural selection as it directly impacts winter foraging and survival behaviour -is also under sexual selection.

Strengths:

The authors have a robust dataset (n = 732 offspring sampled over 3 years), high-quality spatial cognition data collected with a procedure that has been well-honed over the years, and couple the data with solid statistical procedures that address many potential covariates and potentially confounding factors. In addition, the authors are careful in the discussion to elaborate on the many potential alternative explanations from the results and questions that are likely to arise in the minds of readers (e.g., how are females assessing male spatial ability?)

Weaknesses:

Overall, no major weaknesses were identified in this study. As always, there are editorial issues that I would encourage the authors to consider, including presentation of data/results and clarification on some statistical issues. Overall, however, this is an excellent study that will make an important contribution to our understanding of the evolution of cognition and targets of sexual selection.

Reviewer #3 (Public review):

Summary:

The authors presented evidence that spatial cognition in this population is under sexual selection, with extra-pair males, primarily chosen by the females, having better spatial cognition than males they cuckolded and males with better spatial cognition having more extrapair young.

Strengths:

This cognitive ecology study was conducted on a well-known long-term study population of free-ranging mountain chickadees. This strong base, alongside a thorough study design and extensive statistical analyses, enabled the authors to address research questions that few other labs can address, making this a potentially powerful study of broad general interest.

Weaknesses:

Throughout the manuscript, there is a focus on the "mean number of location errors per trial over the first 20 trials". Performance changes across trials, so why weren't learning vs peak performance analyzed separately? Similarly, authors also describe results in the context of the entire task, but sometimes in the context of the first 20 trials - why is one prioritised over the other, and why is the emphasis not always consistent? Are the results across the two generally the same? A more thorough explanation addressing all these points is necessary.

Results are often similar in both metrics, however, the relationship between first 20 and total trials is not 1 to 1 (reported at top of results section and Figure S7a). We suggest that performance in the first 20 trials reflects memory acquisition, while performance across the full task reflects memory retention and recall (Sonnenberg et al. 2019) – both critical components of spatial learning and memory for food-caching birds. Previous work has shown that performance in the first 20 trials and across the entire task is linked to survival (Sonnenberg et al. 2010) and longer lifespan (Welklin et al. 2024) – meaning both metrics reflect fitness.

We did locate several instances where the metric used is not clear and we have corrected this, thank you.

To summarize, we reported results for both metrics for analyses related to the main hypotheses, and then reported first-20 trials in the main text for additional tests and provided the entire test data in the Supplemental Materials.

Lines 429-432: Why was a categorical (i.e., chi-square test) and not a numerical comparison implemented? A numerical statistical test would capture more of the variation (i.e., the number of years separating the social and EPY males).

We agree and have added a paired t-test to assess whether within each offspring, the social father differed in age from the EP father. This test returned a similar result (χ²₁=0.27, P=0.662) and has been added to the results.

Recommendations for the authors:

Reviewer #2 (Recommendations for the authors):

(1) Statistical analysis:

The authors include elevation as a fixed effect in their models; however, I am curious as to why there were no elevation interaction terms included in the model, as I would predict that selection for higher spatial cognition would be stronger in high-elevation sites.

We did test for an interaction between elevation and cognition in many of our models and did not find any support for interactions. For example, there was no interaction between elevation and cognition in the number of EPY sired model.

(2) General comments:

(a) I would prefer to see extra-pair paternity written out rather than EP, EPY, EPP, etc., as the inclusion of the words takes little extra space in the text and makes for easier reading (personal preference).

We agree and have spelled out EP, EPY, EPC, and EPP throughout the MS.

(b) The discussion does an excellent job addressing these questions, but it could be worth noting in the introduction why it is unlikely that this pattern would result simply from selection for dominance (or other factors), given that readers familiar with chickadees would likely immediately think about the role of dominance in extra-pair paternity.

We have added this point to the introduction, thank you:

“Previous research in chickadees shows that females often produce extra-pair young with socially dominant males (e.g., 44, 45), however, in our study system we do not see a significant relationship between social dominance and spatial cognitive abilities (46). One potential explanation for this, is that social dominance changes over an individual’s lifetime and with age, while spatial cognition is repeatable and consistent over individual mountain chickadee’s lifetime (25, 27-32).”

(3) Specific comments:

(a) Line 27-31: This feels like a weak justification. The study is really about selection on cognition rather than the study of sexual selection per se. I would encourage the authors to revise this justification statement to focus on how sexual selection can help shape cognition.

We have edited the abstract.

(b) Line 49: Suggest a stronger start rather than justifying the paper by stating that mate choice has been a focus of evolutionary biology.

We have edited this statement.

(c) Line 50: I believe this should be "mate choice" rather than "sexual selection"

Edited.

(d) Line 59-62: Confusing wording throughout, especially as "high quality" does not refer to sperm competition, but rather sperm that may have an advantage during sperm competition.

Suggest reworking the sentence for clarity.

We changed this to quality instead of competition.

(e) Line 69: Predictable variation in what?

We have removed predictable variation.

(f) Line 87: time;

Corrected.

(g) Line 104: Cut "specifically (i.e., caches are not used for provisioning young),".

Removed.

(h) Line 106: Presumably referring to assortative mating?

Added.

(i) End of the introduction focuses on a couple of primary questions; however, once the reader gets to the methods and results, we find many more tests (e.g., age, brood size, female cognition, etc.). If the authors are going to include these additional tests (which I think they should), then I encourage them to provide the predictions or justifications for those analyses here. In addition, please double-check to ensure the presentation of all tests is consistent throughout the intro/methods/results/discussion.

We have now added this information to the end of the introduction as alternative explanations, rather than specific predictions. These additional analyses were implemented post-hoc to exclude alternative explanations for the patterns observed, but we have linked them to the statistical analyses as requested by Reviewer 3 and for clarity.

(j) Suggest including sample size (nests, nestlings, etc. per year) in methods.

We have provided all sample sizes in the Supplemental Tables and in the text where appropriate.

(k) Line 255: How many egg dumps? Would be interesting to have a number here for future meta-analyses, reviews, BOTW accounts, etc.

Unfortunately, we do not have this data available, and the numbers were very low which is why we did not report them in the manuscript. As we continue to work in the system we will be able to provide this information.

(l) Line 273: See comment above re: elevation as an interaction term in models.

Addressed above.

We did test for an interaction between elevation and cognition in many of our models and did not find any support for interactions. For example, there was no interaction between elevation and cognition in the number of EPY sired model.

(m) Line 282: extra period.

Removed.

(n) Line 328: Change "Here" to "Next".

Edited.

(o) Line 465: I would suggest bringing this in earlier and considering the flow of how ideas are presented. Seems more logical to first look at whether males lost paternity, then, if so, to whom those males lost paternity.

We have reorganized the results section to be consistent with the stats methods order.

(p) Line 553: suggest "likely means" as there may be other attributes of individual quality outside of spatial cognition that are important.

Yes, we have added this qualifier.

Reviewer #3 (Recommendations for the authors):

(1) Section starting at line 268: This section has a long list of statistical analyses. To better help the reader follow the aims of the study and the relationship between them, I recommend numbering the research questions in the introduction and pairing them with the description of each statistical test here in the Statistical Analyses section.

We agree, thank you for this suggestion.

We have now added this information to the end of the introduction as alternative explanations, rather than specific predictions. These additional analyses were implemented post-hoc to exclude alternative explanations for the patterns observed, but we have linked them to the statistical analyses and results as requested.

(2) Lines 295-297: What was the percentage of tested individuals that had brood size data available?

We only have brood size information for birds that breed in our nestboxes and make it to day 16 post-hatching – this is a much-reduced sample from those that participate in cognitive testing (we test around 150 birds a year between both elevation sites). In addition, throughout breeding stages we lose nests to predation, prior to day 16, when we collect blood samples from the chicks. Birds also participate in cognitive testing and breeding in multiple years, so our sample size for EPP is a result of repeated measures in some instances.

(3) Lines 473-479: The study is done, so use the past tense throughout the manuscript.

Thank you, we have edited this for consistency.

I am so glad that Ethnic Studies was able to be put as a required class because I genuinely believe that if everyone just gave each other the time of the day to learn just a bit from everyone's culture, it'll be much easier for everyone to get along and understand each other. Just be open minded and learn about other culture. I think it's always fun to learn about other people's way of living because we are all similar than different, more than we think.

I think of all the patients that we label as "noncompliant" or they end up in the hospital for missed treatments or not taking their medications. This makes me think of all the other reasons that someone could be missing treatments or medications. It is not because they are bad people. There are so many obstacles in the way.

Author response:

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

Summary of the Key Clarification Underlying This Revision

Both reviewers independently identified what appeared to be a direct contradiction between our LC-MS/MS measurements of intracellular ATP (Figure 2) and our single-cell QUEEN reporter measurements of intracellular ATP (Figure 5): NTT1 expression appeared to lower rather than raise intracellular ATP, and exogenous ATP treatment appeared to further lower the QUEEN signal even though LC-MS/MS showed the opposite. We have carefully reviewed the reviewers’ comments alongside our original figures and legends, and we agree that the source of this apparent contradiction was insufficiently explained in the original submission.

To make the reported quantity intuitively track ATP abundance, we have now:

- Plotted the reciprocal of the 488 nm signal (1/488 nm) in the updated Figure 5, eliminating the inverse correlation between AU values and ATP abundance;

- Revised the Figure 5 legend, axis labels, Methods, and Results to explicitly state that the plotted value is directly proportional to intracellular ATP abundance, removing any ambiguity about directionality;

- Subtracted autofluorescence from the raw QUEEN reporter fluorescence signal;

- Expanded the Methods and Results to explain, side by side, why the QUEEN-based and LC-MS/MS based measurements are complementary but not numerically identical (different dynamic ranges; live single-cell sampling over time versus bulk lysates at fixed timepoints); and

- Re-examined Figures 2, 5, and 7 together to confirm that, once the QUEEN directionality is correctly read, the two datasets are internally consistent: NTT1 expression lowers baseline intracellular ATP relative to Wt, and exogenous ATP supplementation raises intracellular ATP in NTT1 cells (and, more modestly and via a distinct mechanism, in Wt cells), by both methods.

Because this misunderstanding affected interpretation of the foundational ATP data, it appears to have influenced evaluation of all downstream conclusions. For example, neither reviewer meaningfully engaged with:

- The identification of distinct cell death trajectories of aged cells;

- The mitochondrial dependency of NTT1-associated toxicity and the observed lifespan differences; and

- The distinction between intracellular ATP manipulation and extracellular ATP sensing mechanisms.

Example of a Data Discrepancy Resolved by This Clarification

In some instances, we think the original figures did not present the data clearly enough to support the intended reading, which we address below.

Public Reviews:

Reviewer #1 (Public review):

Summary:

The authors aim to engineer a synthetic system for manipulating ATP homeostasis in budding yeast by expressing the microsporidian nucleotide transporter NTT1, thereby enabling ATP import from the extracellular environment. Using this system, they attempt to test whether intracellular ATP abundance causally regulates replicative lifespan and whether extracellular ATP sensing contributes independently to longevity pathways. The manuscript presents data from ATP biosensing, transcriptomics, mitochondrial perturbations, and microfluidic aging assays to build a dual-mechanism model linking ATP availability, MAPK signaling, mitochondrial function, and aging trajectories.

Strengths:

A major strength of the study is its creative application of xenotopic synthetic biology to directly manipulate ATP homeostasis-an ambitious approach that addresses an important and difficult question in aging biology. The use of complementary methods, including single-cell ATP reporters, microfluidic lifespan measurements, and RNA-seq, generates a rich experimental dataset with the potential to reveal multiple layers of ATP-dependent physiological regulation. The manuscript also raises interesting hypotheses regarding extracellular nucleotide sensing and HOG/MAPK pathway involvement, opening conceptual space for future exploration of ATP-based signaling in yeast.

Weaknesses:

Despite these strengths, the manuscript suffers from several critical weaknesses that undermine the central conclusions. Foremost, the intracellular ATP measurements contradict key interpretations: NTT1 expression lowers ATP levels, yet multiple sections assert or assume that NTT1 increases intracellular ATP via import. This unresolved contradiction propagates throughout the mechanistic model. The authors do not consider or experimentally address the more parsimonious explanation that NTT1 may be a bidirectional ATP transporter, which would unify many perplexing results. Several important analyses are missing (e.g., transcriptomic comparison of NTT1 cells with vs. without ATP), and key signaling claims lack proper validation (e.g., Hog1 quantification, AMPK controls). Additionally, inconsistencies in figures-such as incorrect scale bars, mismatched ATP measurements, and a conceptual model contradicted by the data-further detract from clarity. As a result, the manuscript does not yet convincingly achieve its stated aims, and the current evidence does not adequately support the proposed causal relationships between ATP homeostasis and lifespan.

We thank the reviewer for a rigorous and constructive critique. The central objection that our intracellular ATP measurements contradict our interpretation arose from a presentational error in how the QUEEN reporter data were plotted. As described in our Methods (QUEEN reporter section), the QUEEN biosensor is a ratiometric reporter whose 410 nm/488 nm excitation ratio increases with ATP binding. Because repeated 410 nm excitation causes phototoxicity over the multi-day time course of a replicative aging experiment, our longitudinal single-cell measurements (Figure 5) used only the 488 nm channel, for which fluorescence intensity decreases as ATP binds the reporter. In the original Figure 5, arbitrary fluorescence units (AU) were therefore inversely correlated with intracellular ATP abundance, such that higher AU values corresponded to lower ATP levels. We described this inverse relationship in the Results section and labeled the relevant figure panels “Low versus High,” but on reflection we agree this was not stated clearly enough in the figure legend itself, where a reader would most naturally look for it. As a result, the two datasets read as contradictory even though they are fully consistent, and we take responsibility for that lack of clarity.

The reviewer proposes that NTT1 may function as a bidirectional transporter, with net ATP export accounting for the reduced ATP we observe in untreated NTT1-expressing cells. We considered this possibility, and our expanded metabolite data argue against it. LC-MS/MS shows that ATP, ADP and AMP are all significantly reduced in untreated NTT1-expressing cells relative to wild type (new Figure S2B), with AMP most severely affected a contraction of the entire adenylate pool rather than a shift in its distribution.

Our transcriptome data identify the source of this contraction. NTT1 expression produces a coordinated downregulation of de novo purine biosynthesis, spanning the pathway (new Figure S2A), consistent with the pronounced AMP deficit. Parallel pyrimidine biosynthesis genes are unaffected, indicating a purine-specific response rather than a general biosynthetic shutdown. We therefore conclude that reduced de novo purine synthesis, not reverse transport, is the parsimonious explanation for the lower baseline nucleotide levels in NTT1-expressing cells, and we have added this analysis and interpretation to the Results and Discussion.

Under ATP-replete conditions, both LC-MS/MS and the corrected QUEEN readout show a clear increase in intracellular ATP in NTT1-expressing cells, consistent with import. We have additionally added the transcriptomic comparison of NTT1-expressing cells with and without exogenous ATP that the reviewer requested (new Figures S1–S3), quantified Hog1 phosphorylation, and audited every figure, legend and numerical value in the manuscript.

Reviewer #2 (Public review):

Summary:

This work presents interesting findings where the addition of exogenous ATP extends the replicative lifespan of yeast cells in a way that seems uncorrelated with actual increased intracellular ATP levels or mitochondria. To be clear, the addition of ATP to yeast growth media increases the number of cell divisions per cell in yeast. Expression of the NTT1 ATP transporter gene increases intracellular ATP levels according to LCMS analysis, but the effect on replicative lifespan works without the NTT1 gene and without an intracellular increase in ATP (possibly with a decrease in intracellular ATP), so the effect appears to be independent of the effect on intracellular ATP levels or mitochondria, as mitochondria-less R0 yeast cells also have increased numbers of cell division when grown with extracellular ATP. The plots in Figure 5 make it seem like exogenous ATP addition lowers intracellular ATP for both the NTT1 cells and the wild-type cells, and that is not what the data in Figure 2d with LCMS shows.

As an aside, this seems like a better model for increased tumor cell growth in the presence of increased extracellular ATP, which happens in some cancers.

Restated, the data suggest they were successful in increasing intracellular ATP by LCMS, but not by queen reporter, and that the seemingly likely increased intracellular ATP was not causative, as cells that did not have an increase in intracellular ATP, but had the same exogenous ATP addition, also gained an increase in replicative lifespan. There could also be two distinct mechanisms extending replicative lifespan to the same degree in these two different strains. More measurements, controls, and analyses are needed to accurately determine what is happening with intracellular ATP levels with age. It is currently unknown if there is any correlation between ATP levels and replicative aging (with properly controlled longitudinal measurements).

Strengths:

Longitudinal imaging of single cells. Analyzed ATP levels with two approaches. Creative approach to use NTT1 transporter to increase intracellular ATP levels. Solid replicative lifespan data.

Weaknesses:

Mostly unclear about ATP levels with age and the relationship, or lack thereo,f between intracellular ATP levels and replicative lifespan. No idea what this effect depends on, but some ideas what it does not depend on (mitochondria or increased intracellular ATP). Experiments seem to lack biological controls (cells without gfp) for age related changes in autofluorescence (and pH that can affect gfp signal) for the fluorescent microscopy quantifying ATP with age using the QUEEN reporter (seems that way as written); conflicting evidence on ATP levels; lack of LC-MS measurements in old cells; no apparent correlation between ATP levels and replicative lifespan, but that could be wrong - just not apparent from the longitudinal data plots. The LCMS data seems better than the microscopy data on ATP because the microscopy approach seems to lack proper biological controls, and the selection of only the top 40% of pixels to quantify signal seems unjustified as written, and possibly prone to technical artifacts. Figure 2 B&C plots of ATP levels should show what the cells were normalized to. The figures also seem too diluted and should probably be combined or put in the supplements (hog1 western) if they do not relate to the lifespan effect. There seem to be some technical scientific editorial errors, like in Figure 7.

We appreciate this careful and, in most respects, accurate reading. The reviewer concludes that the lifespan extension conferred by extracellular ATP does not depend on an increase in intracellular ATP, since it occurs in cells lacking NTT1 and in rho⁰ cells, and suggests that two distinct mechanisms may extend lifespan in the two strains. This is precisely the model our data supports, and we are encouraged that the reviewer arrived at it independently: we propose an intracellular, import-dependent and mitochondria-dependent mechanism operating in NTT1-expressing cells, and a separate extracellular ATP-sensing mechanism that acts without import and without functional mitochondria. We have rewritten the Results and Discussion to make this dual-mechanism structure explicit rather than leaving it to be inferred, and Figure 8 has been revised so that the model matches the data.

The apparent conflict between the QUEEN and LC-MS/MS measurements, which underlies much of the reviewer's uncertainty about ATP levels with age, is resolved by the correction described below. We have additionally subtracted autofluorescence from the reporter signal, stated the normalization for the ATP measurements in the Figure 2 legends, and added a justification in the Methods for restricting quantification to the brightest pixels. The QUEEN reporter is a soluble cytoplasmic protein excluded from the vacuole, which occupies an increasing fraction of cell volume in ageing mother cells, so whole-cell quantification systematically underestimates cytoplasmic signal in old cells for reasons unrelated to ATP. On the request for LC-MS/MS on sorted old cells, we agree this would be valuable in principle, but because individual cells follow divergent ATP trajectories with age, a bulk measurement of a sorted population would average across those trajectories and would not be directly comparable to our single-cell data.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

The intracellular ATP measurements contradict key interpretations: NTT1 expression lowers ATP levels, yet multiple sections assert or assume that NTT1 increases intracellular ATP via import. This unresolved contradiction propagates throughout the mechanistic model. The authors do not consider or experimentally address the more parsimonious explanation that NTT1 may be a bidirectional ATP transporter… Several important analyses are missing (e.g., transcriptomic comparison of NTT1 cells with vs. without ATP), and key signaling claims lack proper validation (e.g., Hog1 quantification, AMPK controls). Additionally, inconsistencies in figures, such as incorrect scale bars, mismatched ATP measurements, and a conceptual model contradicted by the data, further detract from clarity.

We thank the reviewer for this central and constructive critique. As explained above, the apparent contradiction in intracellular ATP directionality stemmed from an underexplained sign convention in the QUEEN reporter readout in Figure 5, which we have now corrected and clarified throughout the text, legends, and axis labels. With this correction, NTT1 cells show reduced baseline ATP and a clear, dose-dependent increase in intracellular ATP upon exogenous ATP treatment, consistent between the QUEEN and LC-MS/MS assays. There is a discrepancy between the two methods (QUEEN versus LC-MS/MS) specifically in the Wt cell ATP measurements, which we discuss in the Results section.

The authors seem to assume that NTT1 expression should result in ATP influx… the authors should consider an alternative interpretation: the ATP transporter is bidirectional… this interpretation seems to be consistent with many of the observations in the manuscript, and this bidirectional ATP flux can be experimentally tested.

We thank the reviewer for this insightful alternative hypothesis. With the QUEEN directionality now corrected (see summary above), the core observation motivating this suggestion lower ATP in NTT1 cells alongside evidence of import is substantially resolved: NTT1 cells have lower baseline intracellular ATP than Wt, and both LC-MS/MS and the corrected QUEEN readout show that exogenous ATP raises intracellular ATP specifically in NTT1 cells, consistent with net import under ATP-replete conditions. In addition, our expanded LCMS/MS data (Figure S2) suggest that NTT1 overexpression results in decreased de novo purine biosynthesis, offering a possible explanation for the decreased ATP levels in these cells.

The RNA-seq analysis compared the effects of adding exogenous ATP in WT and NTT1 cells. However, analysis can also be done to compare the effects of NTT1 under conditions with or without exogenous ATP.

We have added the missing transcriptomic comparison of NTT1 cells with versus without exogenous ATP, and the corresponding data are now presented in three new supplementary figures (Figures S1–S3).

“In NTT1-expressing cells, ATP is directly imported from the extracellular environment…” the authors are assuming NTT1 cell imports ATP from media with ATP supplementation. This should be reconciled with the lower intracellular ATP concentration and lifespan shortening.

This statement refers specifically to the ATP-treated condition, in which both LC-MS/MS and the corrected QUEEN measurements show elevated intracellular ATP in NTT1 cells relative to untreated NTT1 cells and to Wt. We have revised the text to make this conditional context explicit.

The western blots for Hog1p and Hog1 should be quantified… I suggest using p-Hog1 or phos-Hog1 to indicate the phosphorylated form.

We have now quantified Hog1 phosphorylation by western blot analysis from two independent biological replicate experiments, each probed with a different commercial phospho-Hog1 antibody, to confirm that the result is not antibody-specific (Figure 4, Figure S8; Methods). We have also adopted the reviewer’s suggested nomenclature and now consistently denote the phosphorylated form as Hog1ᵖ throughout the text and figures to avoid ambiguity with the Hog1p gene product naming convention.

The model in Figure 8 indicates a larger lifespan extension in the NTT1 cells. This is not consistent with the data presented in Figure 5-7.

The statement regarding a larger lifespan extension is consistent with the data presented in Figures 5 and 7, but we agree this connection was not spelled out clearly enough in the original text. These two figures differ in their treatment conditions. In Figure 6D, 10 µM ATP treatment resulted in a significant median lifespan extension in both Wt and NTT1 cells, though the magnitude of the extension differed: As stated in the Results, Wt cells showed a median RLS increase of 41% (p = 1.28E-12) upon 10 µM ATP supplementation, while NTT1 cells, which also showed an increase in ATP levels (Fig. 6B, C), showed an even more pronounced extension (median RLS increase = 60%, p = 4.03E-18) in lifespan (Fig. 6D). In Figure 7, we analyzed the higher dose of ATP treatment (10 mM) to examine its toxic effect on lifespan. Figure 7A shows that the lifespan-extension effect observed at the low ATP dose (Fig. 6) diminished under the 10 mM treatment condition for NTT1 cells but not for Wt cells. Figure 7B shows that elimination of functional mitochondria rescues this mitochondrial toxicity in NTT1 cells, such that these cells extend their lifespan to a magnitude comparable to Wt under 10 mM ATP treatment conditions.

Reviewer #2 (Recommendations for the authors):

The fluorescence imaging shows that cells with exogenous ATP have lower ATP levels, and that is not what was shown in Figure 2 by LCMS. So, as it is, this is confusing and not conclusive and may have to do with technical artifacts.

We would like to clarify that our data do not in fact conflict. Figure 2B (fluorescence imaging) shows that NTT1 cells have lower intracellular ATP than Wt under baseline (no exogenous ATP) conditions, and that exogenous ATP treatment increases intracellular ATP abundance in both cell types. Figure 2C shows that under 2-deoxyglucose (2DG) treatment, Wt cells display decreased ATP levels regardless of exogenous ATP treatment, whereas NTT1 cells show increased intracellular ATP upon ATP treatment, further supporting the import function of NTT1. Our LC-MS/MS data (Fig. 2D, left panel) independently corroborate the fluorescence results in Figure 2B: NTT1 cells show lower ATP abundance than Wt cells at baseline, and exogenous ATP treatment raises intracellular ATP in NTT1 cells but not in Wt cells. We discuss the modest discrepancy between the LC-MS/MS and QUEEN measurements specifically for Wt cells in the Results section.

The plots in Figure 5 make it seem like exogenous ATP addition lowers intracellular ATP for both the NTT1 cells and the wild-type cells, and that is not what the data in Figure 2d with LCMS shows… Restated, the data suggest they were successful in increasing intracellular ATP by LCMS, but not by queen reporter, and that the seemingly likely increased intracellular ATP was not causative…

We appreciate the reviewer’s detailed reading of Figures 2 and 5. As described above, this apparent conflict arose because Figure 5 originally plotted a raw fluorescence value that is inversely related to ATP abundance without stating this clearly enough in the legend. We have corrected the legend, axis labels, and Results text so that the plotted quantity in Figure 5 (1/488 nm QUEEN signal) increases with ATP abundance, matching the LC-MS/MS data in Figure 2. With this correction, both assays agree that exogenous ATP treatment raises intracellular ATP in NTT1 cells; we discuss in the Results the more modest and assay-dependent behavior we observe in Wt cells, where LC-MS/MS and QUEEN differ somewhat in sensitivity and time-resolution.

It needs a bit more experimental clarification and some thinking about what it means to disrupt ATP homeostasis with high extracellular levels of ATP, a generally biologically unnatural/pathological situation.

The central premise of our study is that altered intracellular ATP is associated with lifespan. Mitochondrial functional decline is a hallmark of ageing, but whether this correlates with decreased ATP, and whether age-associated ATP changes are linked to cellular aging, remains an overlooked question. Here, for the first time, we show that not every cell exhibits a decreasing ATP trajectory with age, and that maintaining ATP homeostasis can extend lifespan. Interestingly, extracellular ATP sensing is directly relevant to cell-to-cell communication (purinergic signaling); however, this has never been characterized in yeast. Our data indicate that a similar, conserved mechanism may also be present in yeast, although the exact components of this sensing cascade require further study. This information is included in the Introduction and Discussion sections of the manuscript.

The data for ATP levels with age needs to be cleaned up/refined… Sort some high bud scar cells and test them with LCMS… run wild-type cells to subtract out the autofluorescence… or redo it on a scope with linear unmixing.

Our data indicates that each cell follows a different ATP-abundance trajectory during aging: while some cells show decreasing ATP with age, others show no change, and still others show increasing ATP. Population-level testing of sorted old cells would therefore not yield results that are directly comparable to our microfluidic experiments, in which we track individual cell trajectories over time. In the updated figure, we have subtracted autofluorescence.

Figures 1 and 2 could be combined, and so could 3 and 5, 6 and 7. Figure 4 should probably be a supplement or part of another figure since upregulating HOG1 has nothing to do with the lifespan extension effect.

We appreciate this suggestion for streamlining the figures. Our data show only decreased Hog1 activity under ATP treatment conditions; we did not test whether this decline in Hog1 activity is associated with lifespan extension. However, we would like to include this figure in the main text, because it directly validates the effect of extracellular ATP sensing on modulation of Hog1 activity.

Figure 7 seems like it is showing that the NTT1 strain’s shorter replicative lifespan is rescued by losing mitochondria, and not that toxicity from ATP in the NTT1 is alleviated by losing mitochondria.

Both the NTT1 strain’s shorter replicative lifespan and its ATP toxicity (10 mM) are rescued by eliminating respiratory mitochondria. In Figure 7, we analyzed the higher dose of ATP treatment (10 mM) to examine its toxic effect on lifespan. Figure 7A shows that the lifespan-extension effect observed at the low ATP dose (Fig. 5) diminished under the 10 mM treatment condition for NTT1 cells but not for Wt cells. Figure 7B shows that elimination of functional mitochondria rescues this mitochondrial toxicity in NTT1 cells, such that these cells extend their lifespan to a magnitude comparable to Wt under 10 mM ATP treatment conditions.

I think you should make sure your pinhole is opened up to catch all the signal in z from each cell… It seems like taking the mean intensity of the top 40% of pixels in a cell can create technical artifacts… Please justify why you use that approach.

We have added justification for the top-40%-pixel approach to the Methods: because the QUEEN reporter is a soluble cytoplasmic protein excluded from the large vacuoles that occupy an increasing fraction of cell volume as mother cells age, whole-cell or full-z-stack quantification systematically underestimates cytoplasmic ATP signal in older cells for reasons unrelated to ATP abundance. Restricting analysis to the brightest pixels focuses quantification on reporter-containing cytoplasm and avoids this age-confounded dilution artifact.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Objectives of the study and impact of the work

The authors of this article primarily aim to reconstruct the evolutionary history of the insect odorant receptor (OR) family, which is responsible for the detection of odorant signals by olfactory neurons. Due to the lack of phylogenetic signal present in the sequences of this multigene family, which evolves very rapidly, phylogenetic analyses have so far never made it possible to precisely retrace how ORs diversified prior to the appearance of present-day insect orders, and what the drivers of this diversification were. For example, one may suspect that the adaptation of ORs to odors emitted by plants constituted a critical step in insect evolution during the "angiosperm terrestrial revolution," which occurred at the end of the Cretaceous, but nothing currently allows this to be asserted.

There are very nice examples, notably in drosophilids, derived from comparisons between closely related species and documenting mechanisms of OR adaptation to certain signals. However, what the authors attempt to do in this work is to produce a macroevolutionary analysis at the scale of insects as a whole, based almost exclusively on bioinformatic analyses. To do this, they annotated OR genes in about one hundred insect species and developed pipelines for analyzing sequence similarity, structural similarity and functional similarity, the latter being estimated through a molecular docking approach. An important element in the evolution of insect ORs is the appearance of a unique co-receptor, called Orco, which appears to be an OR that has lost the ability to bind odorants. In addition to the large-scale bioinformatic analysis, the authors also aim to explore more specifically the factors that favored the emergence of Orco and the selective advantage conferred by the existence of OR-Orco complexes.

Given the importance of odorant receptors in insect biology and in their adaptation to different environments and lifestyles, retracing their evolutionary history is indeed a major question in evolutionary biology. In principle, this type of work therefore has the potential to become a reference in the field and to provide a basis for significant scientific advances.

Major strengths and weaknesses

The sampling chosen for collecting OR sequences is very impressive, with more than 100 insect families represented, covering most of the major orders. This sampling appears appropriate for the question being addressed. The analysis pipeline used to collect the sequences makes sense, relying on homology-based annotation tools coupled with a structure-based filter. Nevertheless, one can note aberrant numbers of ORs for certain species (much lower than reality). A lower number of OR genes is somewhat expected, as the authors chose to apply a fairly stringent filter on sequence quality (based on predicted 3D structure), which reduces the number from 14,000 to 9,000. This choice seems logical given the subsequent use of these data, but it inevitably leads to data loss. However, the low number of genes also results from the fact that the pipeline did not function correctly for all genomes.

In the revised version of the manuscript, the authors included a benchmarking step, which is a good point. They compared their OR gene annotations with previous reports in the same species. Unfortunately, this comparison is irrelevant because the chosen reference OR repertoires are actually a mix of transcriptome and genome annotations. Furthermore, comparisons with entire OR gene repertoires essentially demonstrate that their annotation was of good quality for species in which OR sequences were already present in the query OR database, but poor for species in which they were not. Therefore, these supplementary analyses made by the authors are not particularly in favor of an overall good quality of OR gene repertoires in the >110 species studied. The fact that some OR genes may be missing and that the total number may not be exact for each species is not prohibitive for studying the evolution of the family on a broad scale. However, it does call into question the correlation between the number of ORs and lifestyles and diets.

Thank you for this important comment. We agree that it is inappropriate to directly compare genome-based OR annotations with OR repertoires derived solely from transcriptomes, because transcriptome-only datasets generally do not capture the complete OR gene complement of a species. We therefore repeated the benchmarking analysis and collected, wherever available for the species included in this study, published OR repertoires based on genome annotation or genome annotation supported by transcriptomic evidence. Transcriptome-only OR datasets are no longer included in this comparison.

The updated benchmarking analysis shows that, for most species with comparable genome-based reference repertoires, the number of ORs identified in this study exceeds 70% of the previously reported number, with good agreement in OR repertoire size for most species (Table S1). Diabrotica virgifera is an exception: a previous manual annotation reported 124 complete ORs, whereas we identified 78, approximately two-thirds of the previously reported number. This result indicates that our automated annotation and stringent structural filtering pipeline may indeed underestimate OR repertoire size in some species. The large, repeat-rich genome of this species may further complicate gene prediction and the reconstruction of OR loci. We have therefore explicitly stated in the revised manuscript that incorporating transcriptomic evidence and manual curation may help recover more complete OR repertoires from such complex genomes.

Another notable outlier is Anagrus nilaparvatae. A previous study reported 88 ORs, whereas we identified 330. Examination of the methods used in that study revealed that its OR search relied primarily on homology searches using known OR sequences from two other hymenopteran species. Because insect ORs constitute a rapidly evolving gene family with pronounced lineage-specific expansions, a limited query set may fail to detect highly divergent or species-specific ORs. In comparison, our study used OR queries from a broader range of insects and a genome-level annotation pipeline specifically designed for insect ORs, which may have enabled the detection of more highly divergent candidate ORs. Because the protein sequences of the 88 ORs were not made available in the original study, we are currently unable to perform a one-to-one comparison to verify whether all of these ORs are included in our annotations.

You also noted that our better performance in species such as Drosophila melanogaster, Anopheles gambiae, and Bombyx mori might partly reflect the inclusion of known OR sequences from these species in the query database. We consider this an important and directly testable question. We therefore divided the benchmark species into two groups according to whether conspecific OR sequences were represented in the query database, and used ln(OR count_this study / OR count_previous) to quantify differences in OR counts relative to previous genome-based annotations. No significant difference was detected between the two groups (P = 0.841, Fig. S1 B). Given the unusually large difference in OR counts between the two studies for A. nilaparvatae, we also performed a sensitivity analysis excluding this species, which yielded the same conclusion (P = 0.413, Fig.S1 C). Thus, among the species for which comparable genome-based reference repertoires are currently available, we found no evidence that the inclusion of conspecific ORs in the query database systematically affected the final OR repertoire size. We have added this analysis to the supplementary material of the revised manuscript.

Finally, we agree that annotation biases in OR repertoire size may affect analyses of its correlations with ecological traits. We therefore repeated all relevant ecological sensitivity analyses using an updated OR count dataset, taking the larger of the OR counts from our study and the previous annotation for each species (Fig. S1 D- G). The main statistical results remained consistent with the original analyses: OR counts were still significantly associated with adult diet, larval diet, and habitat, whereas no significant association was detected with circadian rhythm. We therefore consider the statistical associations between OR counts and the main ecological variables to be reasonably robust within the range of annotation discrepancies detectable using the currently available genome-based benchmarks, although automated annotation and stringent structural filtering may underestimate OR counts in some species. The updated benchmarking analyses are described in Supplementary Text S1 and summarized in Table S1.

The following revision has been added (lines 103-107): “Benchmarking against curated OR repertoires showed that the automated pipeline recovered most previously reported ORs and that stringent structural filtering produced a high-confidence set of structurally intact receptors (Supplementary Text S1, Tables S1–S3, and fig. S1B–C). For most species with comparable genome-based references, retained OR counts exceeded 70% of published values.”

From the dataset collected, the authors attempted to categorize ORs in several ways, starting with the reconstruction of sequence similarity networks. The approach is interesting, but fails to reveal homology relationships between ORs from species belonging to different insect orders. So it is unclear what the advantage of this approach is compared with the "classical" phylogenetic approach.

Thank you for raising this important question. Our intention was not to replace classical phylogenetic analysis with sequence similarity networks. Rather, we used network-based approaches as a class-wide framework to classify ORs independently according to sequence similarity, structural similarity, and docking profiles, and then compared how these different classifications correspond across insect taxa and major macroevolutionary transitions.

For smaller gene families with limited sequence divergence, defining subfamilies based on gene trees is a well-established and highly effective approach, because phylogenetic trees can both identify subfamilies and reveal their evolutionary relationships. However, the insect OR superfamily exhibits pronounced birth-and-death evolution, with frequent gene duplications and losses across lineages, and comprises a vast number of highly divergent sequences. Consequently, when a single phylogenetic tree is constructed for the entire OR superfamily, deep nodes often lack sufficient support, and relationships among subfamilies may be difficult to resolve consistently. It is therefore challenging to obtain a stable and consistent classification of thousands of ORs into subfamilies across insects using a single gene tree alone. We therefore used sequence similarity networks as a complementary classification approach. Their main advantage is that they allow large datasets to be grouped according to sequence similarity among all ORs without requiring the resolution of every deep phylogenetic relationship. More importantly, similar network frameworks can be used to construct sequence similarity, structural similarity, and docking-profile similarity networks, allowing SeqC, StrC, and dPC to be compared directly within a common analytical framework. This is difficult to achieve using conventional gene trees alone and is the main reason for our choice of a network-based approach.

Sequence similarity networks alone cannot directly resolve homology relationships among ORs from different insect orders. During the previous revision, we therefore sought to link sequence communities to phylogenetic relationships. We conducted additional phylogenetic analyses of shared sequence communities containing multiple insect orders to search for potentially conserved OR lineages spanning different orders. However, among these shared communities, we identified only one conserved OR lineage spanning four insect orders with relatively clear phylogenetic support. We have added this result to the Supplementary Data S6. This finding further indicates that clearly identifiable orthology relationships spanning multiple orders are very limited among extant insect ORs.

The following revision has also been added (lines 150-154): “The SSN is not intended to replace phylogenetic reconstruction, but rather to provide a complementary framework for summarizing sequence relationships among thousands of highly divergent ORs at a class-wide scale. It allows major patterns of OR sequence similarity and diversification to be visualized more clearly across the entire dataset. Phylogenetic analyses can then be used to further resolve evolutionary relationships within specific sequence communities.”

The clustering based on structure also leads to the identification of a majority of "orderspecific" clusters, which does not provide major insights into the evolution of ORs. However, the authors highlight a group of ORs in flies that appear to possess an unusual intracellular region, as well as a cluster of OR shared across many insect orders that exhibit a larger binding cavity. This is really interesting, although more relevant to OR structure than to their evolution.

Thank you for this important comment. We agree that the previous version of the manuscript focused primarily on structural differences among structural communities and did not adequately explore their potential evolutionary implications. StrC23 is the most widely distributed structural community, spanning 12 insect orders and containing 46.3% of the ORs. We further found that its putative binding pockets were significantly larger than those of other ORs, which we previously interpreted as a potentially conserved structural pattern across taxa. Following your suggestion, we conducted additional analyses of the phylogenetic and orthology relationships within StrC23. The results showed that StrC23 does not correspond to a single, broadly conserved orthogroup spanning insect orders, but instead contains 156 distinct orthologous groups. Of these, 24 encompass more than 10 species. Only a few of these larger groups span multiple insect orders: one contains ORs from Hymenoptera, Diptera, and Trichoptera, and two contain ORs from both Lepidoptera and Trichoptera. The remaining groups show pronounced order specificity, including nine Hymenoptera-specific groups, eight Lepidoptera-specific groups, and four Diptera-specific groups.

These results indicate that the large putative binding pocket shared by StrC23 members cannot simply be attributed to a single conserved orthologous lineage spanning multiple orders, but is distributed across several phylogenetically independent OR lineages. This pattern may reflect convergent evolution toward similar structural features in different OR lineages, or the retention of an older structural feature in multiple OR lineages that subsequently underwent substantial sequence divergence. The current data do not allow us to distinguish conclusively between these two possibilities. We have added the phylogenetic and orthologous-group analyses of StrC23 to the revised manuscript and supplementary material to further clarify the evolutionary implications of this structural community shared across insect orders.

The following revision has been added (lines 208-218): “To further investigate the evolutionary basis of this broadly shared structural feature, we examined the phylogenetic and orthology relationships among StrC23 receptors. StrC23 was divided into 156 orthologous groups, 24 of which contained ORs from more than 10 species. However, only a few of these larger groups spanned multiple insect orders: one included ORs from Hymenoptera, Diptera, and Trichoptera, while two included ORs from both Lepidoptera and Trichoptera (Supplementary Data S6). Thus, StrC23 does not represent a single conserved cross-order orthologous lineage, but instead comprises multiple phylogenetically distinct OR lineages. Its shared large-pocket architecture therefore cannot be explained solely by conservation of a single orthologous lineage and may reflect either structural convergence or retention of an ancient structural feature followed by substantial sequence divergence.”

The analysis of structural diversity then leads the authors to focus on the Orco co-receptors, which are characterized by modifications of the binding pocket and the appearance of an extracellular loop that could explain the loss of the ability to bind odorant molecules. This part, which relies on in vitro experiments, is interesting and constitutes the most striking result of this study, which could in itself have been the subject of a separate manuscript.

We thank the reviewer for the positive assessment of this part of our work.

The rest of the manuscript is based on the prediction of OR response spectra using molecular docking. The work that has been carried out is extremely substantial, and the objective of linking clusters based on sequence similarity or 3D structural similarity with functional categories is entirely relevant. The docking score threshold used was chosen thoughtfully, which is very good, and according to the calculation performed should ensure a true positive rate of more than 20%, which is excellent in such a docking analysis. But in the absence of functional validation, this 20% true positive rate is not sufficient to extrapolate OR function, and docking-derived binding breadth measures used in the remaining of the manuscript have to be taken with caution, as acknowledged by the authors themselves. Consequently, the chance that results of this part of the work will enlighten the evolution of OR on a broad scale is low. For example, the fact that insect lineages that emerged after the Permian-Triassic extinction have more broadly-tuned OR is an interesting observation, yet remains highly speculative.

Thank you for this important comment. We agree that, even after optimizing the docking threshold, the current hit rate of approximately 20% remains insufficient to interpret molecular docking results as reliable predictions of actual OR ligand responses or functions. We also acknowledge that the biological implications of some docking results were still overstated in the previous revision, potentially leading readers to interpret these computational results as approximations of actual OR function. To avoid this misunderstanding, we have further revised the relevant terminology and interpretation of results throughout the latest manuscript. For results derived entirely from molecular docking, we no longer use terms such as ‘docking-derived function’, ‘functional community’, or other expressions that might imply experimental evidence of function. Instead, we consistently use ‘docking profile’ to make clear that these analyses reflect only similarities in computational docking patterns among receptors.

In addition, following your comments and the related suggestions from Reviewer 2, we have removed all results and discussion that directly linked docking-based predictions of OR function or recognition breadth to species ecology. We have explicitly presented the few remaining macroevolutionary comparisons as hypothesis-generating observations rather than evidence of functional evolution. For example, differences in docking-profile composition among extant insect lineages that originated before or after the end-Permian mass extinction (EPME) are now described only as a broad statistical pattern, with any interpretation framed as an experimentally untested hypothesis. Whether this pattern reflects actual differences in receptor tuning, and whether it is evolutionarily linked to environmental changes associated with the EPME, still requires testing through broader taxonomic sampling, reliable ancestral-state reconstruction, and functional experiments. We hope that these revisions restrict the interpretation of molecular docking results to what the evidence can support and bring the corresponding conclusions into closer alignment with the current strength of evidence.

The following revision has been added in Result section (lines 367-369): “These observations should be interpreted as a docking-derived comparative pattern among extant lineages rather than direct evidence of ancestral functional changes across the

EPME.”

And Discussion section (lines 410-414): “However, this interpretation remains hypothetical. Because rapid OR evolution and limited cross-order orthology preclude reliable reconstruction of deep ancestral repertoires, the EPME-related pattern should be viewed as a descriptive comparison among extant lineages. Further validation will require broader taxon sampling, ancestral reconstruction, and experimental testing of receptor tuning breadth.”

In summary, despite the large number of analyses performed, the authors do not really succeed in achieving the stated objective of reconstructing the evolutionary history of insect ORs, and the results obtained do not strongly support all the conclusions regarding the links between OR repertoires and environment or lifestyle.

Thank you for this important comment. We agree that ‘reconstructing the evolutionary history of insect ORs’ was too broad a formulation and exceeded what our methods could reliably address. A rigorous reconstruction of evolutionary history requires well-resolved phylogenetic relationships across taxa, ancestral-state inference, and systematic analysis of gene duplication and loss events. We have therefore redefined the scientific objectives of this study. The revised manuscript no longer claims to have reconstructed the evolutionary history of insect ORs. Instead, it aims to systematically characterize insect OR diversity and classification patterns at the levels of sequence, structure, and docking profile, compare the correspondence among these levels, and describe differences in their distribution across insect taxa and broad macroevolutionary contexts.

We have also reassessed the strength of different types of evidence concerning the relationships between OR repertoires and environment or lifestyle. For relationships between OR repertoire size and ecological traits, we repeated the genome-based benchmarking. After rerunning the ecological correlation sensitivity analyses using the updated OR count dataset, the main statistical results remained consistent with the original analyses. We therefore consider the current data to continue to support statistical associations between OR counts and ecological traits, with a degree of robustness. By contrast, we have removed results and discussion directly linking predicted OR function or recognition breadth to species ecology, and no longer use terms such as ‘docking-derived function’ or ‘functional community’ that might imply experimental evidence of function. The remaining macroevolutionary comparisons of docking profiles, such as differences in docking-profile composition among groups considered in relation to the EPME, are treated only as hypothesis-generating comparative patterns, rather than direct evidence of receptor functional evolution. We explicitly state that these hypotheses require future testing through functional experiments and more reliable ancestral-state reconstruction.

In summary, we have redefined the study objectives and no longer describe this work as a reconstruction of insect OR evolutionary history. We have retained the statistical associations between OR counts and ecological traits that remained supported after reassessment, while removing results and discussion linking receptor function to ecology on the basis of molecular docking. We believe these revisions better align the scientific objectives and scope of the conclusions with the evidence provided by the available data and methods.

We have revised the final paragraph of the Introduction to clarify the scope and objectives of this study (lines 80-91): “In this study, we characterized large-scale patterns of OR diversification across 115 species spanning 16 insect orders. Using a framework that integrates network analysis, protein structure prediction, and molecular docking, we constructed sequence-similarity (SSN), structural-similarity (StSN), and docking-profile similarity networks (dPSN) to classify ORs from three distinct perspectives. We identified differences in OR sequence-community diversity between holometabolous and non-holometabolous insects, as well as differences in docking-profile community composition among extant lineages whose order-level origins fall on opposite sides of the end-Permian mass extinction (EPME). Across this class-wide sampling, OR repertoire size was associated with adult diet, larval diet, and habitat, but not with circadian rhythm. Moreover, the conserved β-sheet in the extracellular loop 2 (EL2) region of Orco, together with its specialized binding-pocket architecture, is associated with its reduced ligand-binding capacity and represents a prominent structural specialization of the co-receptor lineage.”

Reviewer #2 (Public review):

The remarkable evolvability of the olfactory system enables animals to rapidly adapt to dynamic and chemically complex environments. Over the past two decades, substantial effort has been devoted to uncovering the evolutionary principles that drive the diversification of odorant receptors (ORs), yielding key insights into the forces shaping their striking variability in both vertebrates and insects. In this manuscript, Zhang and colleagues analyze the OR repertoires of over 100 insect species, leveraging sequence and structural similarity to infer patterns of gene family evolution within this diverse and ecologically important clade. By integrating sequence-based and structure-based comparisons, their study builds on a compelling and recently emerging line of research made possible by the advent of AlphaFold, which has previously clarified the phylogenetic relationship between insect Ors and the gustatory receptor gene family and revealed the unexpectedly deep evolutionary origins of this ancient structural fold.

Applying this approach to a large set of ORs derived from species throughout the insect phylogeny, the authors confirm many previously reported patterns of OR evolution. More importantly, with their large-scale approach the authors found new structural features of different Or clades, resulting in intriguing testable hypotheses about Or evolution that have the potential to support future directions in studying this important gene family. For example, the authors identify a structural feature mostly unique to the OR co-receptor ORco, a beta-sheet in EL2, which they functionally show reduces odorant binding affinity - a key aspect of ORco, which does not bind ligands in the ancestral ligand-biding site. This is a particularly strong part of the manuscript, since the authors support their in silico-derived hypothesis with functional data.

We thank the reviewer for the positive assessment of this part of our work.

In an attempt to assess the relationship between sequence identity and structure on one hand and function on the other, the authors perform an in-silico structure prediction and chemical docking analysis. While not suitable to assess the actual function of individual receptors without functional testing, this strategy revealed potential receptor clades with differences in the number and type of docked chemicals. As a response to the previous reviews, the authors now changed their writing to refer to these results as 'docking-derived function' instead of just 'function'. While I appreciate that the authors changed their wording, this semantic change still can be read as referring to dockingderived predictions as conclusions of actual biological function. However, this is not the case. Any functional claims based solely on the docking approach need to be interpreted with caution, as in silico-only approaches are currently not well enough predictors for actual receptor function. Accordingly, I strongly recommend to remove the parts that connect receptor function to structure or ecology.

Thank you for highlighting this important issue again. We agree with your comments and acknowledge that the presentation of molecular docking results in the previous revision still overstated their biological implications. Following your suggestion, we have removed all results and discussion that directly linked receptor function to species ecology solely on the basis of molecular docking, to avoid interpreting computational predictions as actual biological functions. We then systematically reviewed and revised docking-related terminology throughout the manuscript. For results derived entirely from docking analyses, we no longer use ‘docking-derived function’, ‘functional community’, or other expressions that might imply experimental evidence of function. Instead, we consistently use ‘docking profile’ to clarify that these analyses reflect similarities in computational docking patterns among receptors, rather than experimentally validated functional categories.

Through these revisions, we hope to distinguish more clearly between computational docking profiles and experimentally validated receptor function, and to avoid biological interpretations of docking results that exceed the available evidence. We believe these changes bring the manuscript's conclusions into closer alignment with the strength of the evidence.

Assessing their docking analyses with respect to species ecology, the authors identify correlations suggesting that Or repertoires might follow predictable evolutionary trajectories broadly aligned with species ecology. These are interesting hypotheses. However, due to the inability to predict actual receptor function the author's claims about ecology-function relationships are not well supported. Accordingly, the authors should change the respective parts of the manuscript in way that it is clear these are currently untested hypotheses. This includes adjusting the title, since the work does not find any experimental support for ecological tuning.

Thank you for this important suggestion. We agree that the current molecular docking analyses cannot support direct conclusions about relationships between actual receptor function and species ecology. Following your suggestion, we have removed the results and discussion directly linking docking-based predictions of OR function to species ecology. For the remaining macroevolutionary comparisons, such as differences in docking-profile composition among groups considered in relation to the EPME, we explicitly state that these results represent only computational patterns observed in extant taxa. The evolutionary interpretations proposed from these patterns remain experimentally untested hypotheses and cannot be considered direct evidence of changes in actual receptor function.

In addition, following your suggestion, we have changed the manuscript title to ‘Classwide sequence, structural, and docking-profile diversity of insect odorant receptors and structural specialization of Orco’. The new title no longer emphasizes ‘ecological tuning’ or ‘olfactory perception’, but instead focuses on class-wide diversification of insect OR sequences, structures, and docking profiles, together with the experimentally supported structural specialization of Orco.

The following revision has been added in Result section (lines 367-369): “These observations should be interpreted as a docking-derived comparative pattern among extant lineages rather than direct evidence of ancestral functional changes across the EPME.”

And Discussion section (lines 410-414): “However, this interpretation remains hypothetical. Because rapid OR evolution and limited cross-order orthology preclude reliable reconstruction of deep ancestral repertoires, the EPME-related pattern should be viewed as a descriptive comparison among extant lineages. Further validation will require broader taxon sampling, ancestral reconstruction, and experimental testing of receptor tuning breadth.”

I believe that future studies combining functional testing with an explicit evo-eco framework could benefit from this work and the explicit hypotheses it generates. But the authors should be careful to not overstate their in-silico derived results.

Thank you for this suggestion. We have revised the manuscript accordingly.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Below are my comments in response to the rebuttal letter. I thank the authors for their careful revision and detailed responses to the points raised in my review.

(1) OR annotation pipeline and correlation analyses

Previous comment: "One can note aberrant numbers of ORs for certain species (much lower than reality), which indicates that the pipeline probably did not function correctly for all genomes. In the absence of a validation step comparing the results with already known OR repertoires, it is difficult to estimate the overall quality of the data. [...] It calls into question certain results that rely on this total number, such as the correlation between the number of ORs and genome size, lifestyle, and diet."

The response made by the authors on that point is not particularly convincing. They compared their OR gene annotations with previous reports in the same species, but this comparison is irrelevant because the chosen reference OR repertoires are actually a mix of transcriptome and genome annotations (the OR counts for Harmonia axyridis, Plutella xylostella, Pierus brassicae, Dendrolimus kikuchii, Carposina sasakii, Hermetia illucens, Chlorops oryzae and Propsilocerus akamusi are from transcriptomes). As not all OR genes are expressed in a given tissue, the number of ORs in transcriptomes is always lower than in genomes. Furthermore, comparisons with entire OR gene repertoires essentially demonstrate that their annotation was of good quality for species in which OR sequences were already present in the query OR database (Bombyx mori, Drosophila melanogaster, Anopheles gambiae) but was of bad quality for species in which OR sequences were NOT in the query (Diabrotica virgifera). However, re-annotation of Diabrotica led to an OR repertoire of 78 complete genes, vs. 124 in the manually curated genome annotation (1/3rd of the genes are missing). So these supplementary analyses made by the authors are not particularly in favor of an overall good quality of OR gene repertoires in the >110 species studied. They have also repeated the correlation analyses using 'full' OR gene sets where available. This showed that the correlation of OR count with genome size is no longer valid, but the correlation with diet or lifestyle is. However, if a mix of gene numbers from transcriptomes and genomes was used (see my comment above), I am afraid that these novel correlation analyses are not relevant. In conclusion, I would disagree with the claim that "These new benchmark and sensitivity analyses directly strengthen the evidence supporting our dataset and its ecological interpretations".

Thank you for further highlighting this issue. As detailed in our response to the Public Review, we repeated the OR annotation benchmarking, excluded transcriptome-only repertoires, and restricted comparisons to genome-based reference datasets or genome-based datasets supported by transcriptomic evidence. The updated results show that, for most species with comparable reference data, the number of ORs identified in this study exceeds 70% of the previously reported number. We also explicitly acknowledge that repertoire size may still be underestimated in some species.

We also directly tested whether query database composition systematically affected the number of annotated ORs. No significant difference was detected between species with and without conspecific OR queries (P = 0.841; P = 0.413 after excluding Anagrus nilaparvatae). Thus, we currently find no evidence that conspecific queries systematically increase the final OR count.

In addition, we repeated the sensitivity analyses of ecological correlations using the updated OR count dataset. The main statistical results remained unchanged: OR counts were still significantly associated with adult diet, larval diet, and habitat, but not with circadian rhythm. We therefore consider these statistical associations between OR counts and ecological traits to be reasonably robust to the annotation differences currently detectable. Detailed results are provided in our response to the Public Review and in the revised supplementary text S1.

(2) sequence similarity-based clusters

Previous comment: "The authors attempted to categorize ORs in several ways, starting with the reconstruction of sequence similarity networks. The approach is interesting, but in the end, the results do not seem to be sufficiently exploited. [...] For example, clusters SeqC26 or SeqC28, which appear to be shared by many insects, are potentially very interesting. It might have been relevant to combine this similarity-based clustering approach with phylogenetic reconstructions within each shared cluster."

The authors have followed this suggestion and identified an orthogroup conserved across several insect orders, which is an interesting observation. However the phylogeny of this orthogroup should be provided in supplementary data, which does not seem to be the case.

We thank the reviewer for the positive assessment. The corresponding phylogenetic tree has been added to the supplementary data S6.

(3) structure-based clusters

Previous comment: "The clusters shared by several orders are not truly exploited, which does not provide new insight into the evolution of ORs"

The authors show an interesting feature for a cluster of ORs from several insect orders, with a large putative binding pocket. However, it is not clear whether they verified or not if this cluster also correspond to an orthogroup or if this shared feature (a large binding pocket) is a convergence. They also improved the discussion of their results on a cluster of fly ORs with a long intracellular domain, which is a good thing.

Thank you for this important question. To determine whether StrC23, a structural community shared across multiple insect orders, corresponds to a conserved orthogroup, we performed additional phylogenetic analyses of its OR sequences and identified orthology relationships within the community based on the gene tree. The results showed that StrC23 does not correspond to a single orthogroup spanning insect orders, but instead contains 156 distinct orthologous groups. Of these, 24 encompass more than 10 species. Among these 24 larger groups, one contains ORs from Hymenoptera, Diptera, and Trichoptera, and two contain ORs from both Lepidoptera and Trichoptera. The remaining groups show pronounced order specificity, including nine Hymenoptera-specific groups, eight Lepidoptera-specific groups, and four Diptera-specific groups.

These results indicate that the large putative binding pocket characteristic of StrC23 is not explained by a single, broadly conserved orthogroup spanning multiple orders, but is distributed across several phylogenetically independent OR lineages. We therefore consider that this shared structural feature cannot simply be interpreted as direct retention within a conserved orthologous lineage. It may reflect convergent evolution toward similar structural features in different OR lineages, or the retention of an older structural feature in multiple OR lineages that subsequently underwent substantial sequence divergence. The current data do not allow us to distinguish conclusively between these two possibilities. We have added the phylogenetic analysis of StrC23 to the revised manuscript to clarify the evolutionary relationships within this structural community.

The following revision has been added (lines 208-218): “To further investigate the evolutionary basis of this broadly shared structural feature, we examined the phylogenetic and orthology relationships among StrC23 receptors. StrC23 was divided into 156 orthologous groups, 24 of which contained ORs from more than 10 species. However, only a few of these larger groups spanned multiple insect orders: one included ORs from Hymenoptera, Diptera, and Trichoptera, while two included ORs from both Lepidoptera and Trichoptera (Supplementary Data S6). Thus, StrC23 does not represent a single conserved cross-order orthologous lineage, but instead comprises multiple phylogenetically distinct OR lineages. Its shared large-pocket architecture therefore cannot be explained solely by conservation of a single orthologous lineage and may reflect either structural convergence or retention of an ancient structural feature followed by substantial sequence divergence.”

(4) molecular dynamics simulation

Previous comment: "The molecular dynamics modelling does not add anything in the way it is conducted (5 ns is too short)."

The authors argue that such a short simulation is sufficient for testing the interaction between a compound and the extracellular beta-sheet of the coreceptor Orco. I'm not a specialist enough to confirm whether this is actually true, but I trust the author's expertise in this area.

We thank the reviewer for the positive assessment.

(5 / 6) molecular docking and functional extrapolation

Previous comment: "in the absence of functional validation, this 20% true positive rate is not sufficient to extrapolate OR function"

The authors argue that molecular docking was not used to identify specific OR/ligand pairs, but rather to "estimate the potential binding tendencies of OR repertoires". I agree with this point; correlations were made using "binding breadth index values" that are calculated for entire OR repertoires. The text of the manuscript has been edited to refer to "docking-derived" functional clusters and binding breadth index, and to emphasise that the results should be interpreted with caution, which is a good point as it will prevent potential misinterpretation by the reader. However, this does not change the fact that interpreting the olfactory capacity of one species based on docking-derived binding breadth values of its OR repertoire is highly speculative (especially when OR repertoires are incomplete) and the chance that results of this part of the work will enlighten the evolution of OR on a broad scale is low.

Thank you for raising this concern. We agree that repertoire-level analyses do not resolve the inherent limitations of molecular docking in predicting actual receptor function. Although such analyses summarize overall docking patterns rather than individual OR–ligand interactions, they still cannot reliably define a species’ true olfactory capabilities. It therefore remains insufficient to describe a species' actual olfactory capabilities solely on the basis of docking-derived binding breadth. As detailed in our response to the Public Review, we have addressed this issue by following your suggestions and those of Reviewer 2 and removing the results and discussion that used the binding breadth index to directly link predicted receptor function to ecological traits such as diet, habitat, and circadian rhythm. We have also further standardized the terminology, replacing ‘docking-derived function’, ‘functional community’, and other expressions that could imply experimentally established function with ‘docking profile’, to emphasize that these results describe computational docking patterns rather than experimentally determined receptor functions. Through these revisions, we hope to distinguish more clearly between computational docking patterns and experimentally established receptor functions, and to restrict the interpretation of the related macroevolutionary comparisons to what the current data can support.

(7) EPME

Previous comment: "ORs of non-holometabolous insects cannot be considered equivalent to those of species that existed before the Permian-Triassic extinction"

The authors have now clarified the fact that they compared extant insect orders rather than ancestral and derived OR repertoires.

We thank the reviewer for the positive assessment of the revised manuscript.

(8 to 16)

The authors have carefully considered all the points raised in the recommendations for the authors, improving the manuscript on several aspects.

We thank the reviewer for the positive assessment of the revised manuscript.

Minor comment

Line 217: Orco did not emerge in the ancestor of Zygentoma, it emerged in the common ancestor of Zygentoma and Pterygota.

Thank you for pointing this out. We have corrected the statement.

Reviewer #2 (Recommendations for the authors):

The authors have done a good job in their revision of the manuscript. They addressed many of the reviewers' concerns well.

We thank the reviewer for the positive assessment of our previous revision.

However, the functional claims are still too strong and need to be removed or tempered down as described in the public review.

Thank you for this suggestion. We have removed or tempered the functional predictions in the manuscript in accordance with the Public Review. Please see our response to the Public Review for details.

Further, the manuscript title is not a good fit for the content. I would argue that the paper does not 'reveal ecological tuning shaping olfactory perception', since Or structurefunction relationships are involved in olfactory sensation or detection. Perception, however, requires interpretation, which is done by neural circuits but not receptors expressed within. Further, I still think that referring to 'ecological tuning' is far-fetched based on the docking approach that cannot really resolve the tuning of receptor sets. I would think that the work reveals interesting correlations between docking-derived population tuning and ecology. But that does not necessarily have anything to do with actual function and thus may not make much sense to advertise in the title or abstract.

Thank you for your suggestions concerning the manuscript title. Following this comment, we have changed the title from ‘Evolutionary dynamics of insect odorant receptors reveal ecological tuning shaping olfactory perception’ to ‘Class-wide sequence, structural, and docking-profile diversity of insect odorant receptors and structural specialization of Orco’ The new title no longer emphasizes ecological tuning or olfactory perception, but instead focuses on the two aspects of this study supported by the most direct evidence: class-wide patterns of sequence and structural diversification in insect ORs, and the experimentally supported structural specialization of Orco.

Consistent with the revised title, we have further adjusted the relevant wording in the Abstract, Results, and Discussion, and removed content directly linking receptor function to species ecology on the basis of docking results. We believe that the revised title and abstract more accurately reflect the main content of the study and the scope of its evidence, while avoiding functional or ecological interpretations of computational predictions that exceed their evidential support.

I suggest selecting a title that fits the sequence/structure/in silico docking nature of their large macroevolutionary approach and findings better. After all, apart from the orco work this manuscript is mostly a resource of in silico predictions.

Thank you for this suggestion. We have revised the manuscript title.

Author response table 1.

Numbers of OR genes in previously annotated species.

Reference

Carey AF, Wang G, Su CY, Zwiebel LJ, Carlson JR. 2010. Odorant reception in the malaria mosquito Anopheles gambiae. Nature 464: 66-71.

Engsontia P, Sangket U, Chotigeat W, Satasook C. 2014. Molecular evolution of the odorant and gustatory receptor genes in lepidopteran insects: implications for their adaptation and speciation. J Mol Evol 79: 21-39.

Ma Y, Guo Z, Wang L, Wang B, Huang T, Tang B, Zhang G, Zhou Q. 2022. The genome of the rice planthopper egg parasitoid wasp Anagrus nilaparvatae casts light on the chemo- and mechanosensation in parasitism. BMC Genomics 23: 541.

Mier P, Fontaine JF, Stoldt M, Libbrecht R, Martelli C, Foitzik S, Andrade-Navarro MA. 2022. Annotation and Analysis of 3902 Odorant Receptor Protein Sequences from 21 Insect Species Provide Insights into the Evolution of Odorant Receptor Gene Families in Solitary and Social Insects. Genes (Basel) 13.

Paddock KJ, Corcoran JA. 2025. Life-stage dependent behavior mimics chemosensory repertoire diversity in a belowground, specialist herbivore. G3 (Bethesda) 15.

Robertson HM, Warr CG, Carlson JR. 2003. Molecular evolution of the insect chemoreceptor gene superfamily in Drosophila melanogaster. Proc Natl Acad Sci U S A 100 Suppl 2: 14537-14542.

Tanaka K, Uda Y, Ono Y, Nakagawa T, Suwa M, Yamaoka R, Touhara K. 2009. Highly selective tuning of a silkworm olfactory receptor to a key mulberry leaf volatile. Curr Biol 19: 881-890.

Wang Q, Dicke M, Haverkamp A. 2023. Sympatric Pieris butterfly species exhibit a high conservation of chemoreceptors. Front Cell Neurosci 17: 1155405.

Xiao S, Ye X, Wang S, Yang Y, Fang Q, Wang F, Ye G. 2023. Genome assembly of the ectoparasitoid wasp Theocolax elegans. Sci Data 10: 159.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

The authors aim to understand, in the context of leaf shape, how the constraints imposed by development inform evolution. Leaf shape is a good place to study the influence of development on evolution because it is a trait that exhibits a lot of diversity, and the developmental mechanisms that give rise to leaf shapes are apparently rather conserved across angiosperms.

As part of the motivation for their work, the authors cite a previous study (Geeta et al), which found that in angiosperm phylogenies, transitions from complex to simple leaf shapes occur through evolution more often than transitions in the opposite direction. Is this due to developmental constraints or adaptation?

The authors undertake two parallel lines of work:

(1) Extending the study of Geeta et al with more data, consisting of both phylogenies and a shape classification dataset. The conclusion from this line of inquiry is that transitions from lobed to unlobed leaves are more common than transitions away from unlobed leaves.

(2) The authors conduct evolution simulations in a computational model of leaf development. Here, they look at {\it neutral} mutations and whether simply neutral evolution is sufficient to drive the observed trend.

The conclusion of the second part of the work is that the driver of the evolution toward simple leaf shape is entropy: there are more ways to make unlobed leaves than to make lobed leaves (at least in terms of gene regulation parameters that will produce the two leaf types). The argument is that random gene regulatory networks are more likely to produce unlobed leaves than lobed leaves; therefore, neutral evolution drives this trend.

Data Analysis

Roughly $9000$ images of leaves were classified into 4 categories: unlobed, lobed, dissected, and compound. These labels were applied to the tips of 5 phylogenetic trees of angiosperms (3 resolved at the genus level and 2 at the species level). By fitting a continuous-time Markov chain to the labelled trees, the authors claim that there is a significantly higher rate of transition to the unlobed leaf shape compared to transitions to more complex shapes.

Simulation

First, the authors validate a computational model (Runions et al) for leaf growth on an experimental dataset. By changing parameters in the model, they can recapitulate the morphological changes in the shapes of Arabidopsis leaves engendered by expression of two particular genes.

Then the authors run an evolutionary model (without selection, just random mutations) on top of the computational leaf development model. As the random walk in parameter space reaches a stationary distribution, they look at both the proportions of the leaf categories in the steady state as well as the transition rates between different categories. The result is that transitions to unlobed leaves are more common than from unlobed leaves.

We thank the reviewer for the helpful and clear summary of our work.

General Comments

The authors use angiosperm phylogenies from other works as the basis for the data analysis part of their work. Given the centrality of these phylogenies for their conclusions, more information is needed about how these phylogenies were constructed and what they mean. What is the timescale that they span? What method is used to infer them? What regions of DNA were sequenced in order to build the phylogenies? Also, maybe some more discussion of angiosperm evolution (e.g., when was the most recent common ancestor of all angiosperms?) would help put the study in context.

We also need a more in-depth discussion of the computational model. What are all the $>100$ parameters doing, and what informs the seemingly strange mutational model that changes parameters by 3 orders of magnitude?

I am confused about how the rates of transitions were inferred from the phylogeny. Here, one has a phylogeny inferred by some method (which needs to be described in more detail), and just the leaves are labelled. It is stated in the methods that BayesTraits was used to infer the transition rates. I realize this method is probably documented elsewhere, but a bit of a summary of how it works and how to interpret its results would (1) make the paper more selfcontained and (2) if the algorithm is credible, make the results firmer.

We thank the referee for the suggestion to make the paper more accessible. The tool we use to infer transition rates from the phylogenies, BayesTraits, is standard in the field. However, the referee is right that for an interdisciplinary journal, it may be helpful to more fully flesh out how these methods work. To that end, we have added an additional section S2.A "Phylogenetic rate inference" in the supplementary information that includes a longer description of how BayesTraits works, and how we used it to infer transition rates from phylogenies.

All trees are shown in the supplementary information section S2.B "Phylogenetic trees" with scale bars showing the amount of time or genetic change that the trees span. We have added details of the specific genes used to construct the trees in our analysis in Methods section F. For a broader discussion of angiosperm evolution, there is supplementary information section S4 "A short literature review of the adaptive significance of leaf shape".

Regarding the more in-depth discussion of the computational model, we have added supplementary information section S1.A "Leaf model details" to give a more detailed description of the leaf model. We chose our mutational scheme over other methods, such as uniform or Latin hypercube sampling, as the biologically relevant ranges for each parameter were unknown. Mutations of multiple orders of magnitude are a way to sample both parameters with large and small ranges with the same scheme.

Additionally, larger mutations help to move a walk out of a local region if it is stuck while small mutations ensure sensitive parameters are still varied. We use multiple schemes for additional robustness.

I am a bit skeptical of the authors' interpretation of the biological trend (of complex to simple leaf shapes) as being driven by neutral evolution. Why does one expect that the mutations generated by the random walk models described in the work are in fact neutral mutations?

A random walk is a well-established way of modelling the dynamics of neutral evolution in the monomorphic regime, where the population has a narrow diversity of different genotypes. In the higher mutation rate polymorphic regime, where the diversity of genotypes in the population is larger, we also expect that a random walk should still recapitulate the correct average transition rates. The purpose of the simulations is not to model every aspect of population genetics, but to ask whether developmental bias alone is sufficient to generate the observed directional asymmetry. By assigning equal fitness to all viable leaves, we isolate the contribution of development from that of selection. The agreement with the phylogenetic transition rates therefore demonstrates sufficiency rather than exclusivity: selection may also contribute, but it is not required to explain the observed bias. We discuss the evidence for the role of adaptation in leaf shape further in supplementary information section S4 "A short literature review of the adaptive significance of leaf shape".

- If the entropy of simple leaf shapes is higher than that of complex leaf shapes, why did we have complex leaves at all? I suspect the authors might argue that this is due to selection. In that case, what allows these complex shapes to become simpler? Wouldn't they be losing the selective advantage that drove them to be more complex in the first place? Or maybe the idea is that the rates are inferred assuming some steady state that generates the phylogeny? I did not understand this point.

The entropy language is a useful framing. Within that framework, one can view our study as showing that the entropy (defined here as the logarithm of the volume of parameter space mapping to a phenotype) of simple leaf shapes is higher than that of complex leaf shapes. If this entropy were to be ignored, and were we not to take fitness differences into account, then all states would be equally likely in our simulations. What we show is that the differences in entropy, which are related to differences in volumes of the parameter space that map to different phenotypes, also affect the rates. The inferred transition rates for both simulation and phylogeny from unlobed to more complex shapes are lower than the reverse but not zero. Therefore, complex leaf shapes arise stochastically through mutation and in this model would eventually reach a steady-state proportion, even in the absence of selection. This steady state proportion for complex leaves would be smaller than that of unlobed leaves, but non-zero.

Are the rates of transitions between leaf types inferred for the phylogeny assuming that the phylogeny is generated by the steady state of some Markov process? (I think the answer is no: in that case, how does one explain the initial condition?)

The tool we use to infer transition rates from phylogenies—BayesTraits—allows the initial state at the root of the tree to vary during the numerical optimisation (Pagel, 1994). Therefore, it is not assumed that the initial state is generated by the steady state of the Markov process.

If I take the mutation model (random walk) seriously, then shouldn't I expect that this steady state obeys detailed balance? In that case I should have $p_i r_{i\to j} = p_j r_{j\to i}$ for each of the occupancies $\{ p_i\}$ and transition rates $r_{i\to j}$ for the shape categories. How close are the rates inferred from the phylogenies to obeying detailed balance? Presumably, the Markov chain fitted to the simulation data obeys detailed balance because the mutation model itself does?

BayesTraits allows off-diagonal transition rates of the rate matrix to vary freely during numerical optimisation (Pagel, 1994). Therefore, there is no requirement for detailed balance to hold for the inferred rate matrix. For our simulations, the mutations are symmetric at the parameter level, therefore at this level, the process would be expected to obey detailed balance. We investigated this further by calculating the posterior signed equilibrium flux difference $\pi_iq_{ij}-\pi_jq_{ji}$ for all inferred rate matrices (see new material in supplementary information Fig S23). The posterior signed equilibrium fluxes for each transition pair in the simulations have 95% credible intervals overlapping with 0, which is consistent with detailed balance. Some phylogenetic state pairs are inconsistent with detailed balance. This could be due to something other than symmetric neutral drift acting on these specific transitions, such as selection or mutation biases not captured by the model. However, the identity of the transition pairs that are inconsistent with detailed balance varies between phylogenies, indicating that these apparent violations could be noise due to phylogenetic uncertainty. In any case, a violation of detailed balance does not disprove a developmental bias explanation, it just suggests that the underlying process is more complex than the reversible evolutionary algorithm we use in our leaf-model simulations. However, introducing non-reversible mutation dynamics into our leaf-model simulations would require additional assumptions and parameters describing mutational asymmetries, which are not necessary to reproduce the key bias towards unlobed.

I find it hard to take the discussion of development seriously without some consideration of mechanics. Presumably, the mechanics are hidden in the computational leaf development model, but this model is not discussed in enough detail for the reader to know. It seems to me that the interesting question is: what are the {\it mechanical} constraints on development that drive the apparent trend in evolution towards simpler leaf shapes? Maybe it is something about the type of differential growth needed to make complex leaf shapes less robust to mutation. But in this case, I would assume that selection plays a role in the complexity of shape. In any case, a better understanding (or explanation) of the computational model is needed to make this interpretation.

We thank the referee for the suggestion to make the paper more accessible. We have added a new, more detailed and pedagogical description of the model from (Runions, Tsiantis and Prusinkiewicz, 2017) in the supplementary information section S1.A “Leaf model details". We also note that Fig. 5 in the methods gives an overview of how the model works, including some mechanical aspects of development and growth.

More generally, mechanics is one component of the developmental map that determines which parameter combinations produce viable leaf morphologies. Our analysis concerns the geometry of this complete developmental map, irrespective of whether its constraints arise from gene regulation, tissue mechanics, or their interaction.

On the interesting question of what is causal, perhaps the example in figure 2 is helpful. We focus on two parameters, a morphogen repression strength, and a duration of growth. A key physical process here is called webbing, where cellular growth fills in the gaps between branching veins. This process flattens the leaf structure and creates a continuous, solid leaf blade (lamina). Strong webbing, characterized by a significant resistance to stretching and bending, results in a smoother margin (Runions, Tsiantis and Prusinkiewicz, 2017). The morphogen repression strength affects the physical parameters that determine how strong the webbing is. The duration of growth determines how long the leaf has to grow. If an unlobed leaf has some marginal patterning that results in small protrusions, such as serrations, increasing the duration of growth will amplify these protrusions, eventually forming lobes. Similarly, increasing the strength of morphogens that repress growth along the margin will deepen the sinuses between protrusions, resulting in lobes. Combinations can result in highly dissected and compound leaves, as illustrated in figure 2. Conversely, decreasing either or both will result in a smoother margin and eventually leaves with an unlobed shape. Thus, varying these two developmental parameters varies the physical processes that determine leaf shape. The mechanics of growth operate downstream of these parameters that we vary in our evolutionary simulations according to the details of the leaf developmental model.

Some discussion of timescales is needed, especially when invoking neutral evolutionary arguments. If a neutral mutation occurs, its time to fix in a population of size $N$ is $\sim N$ generations. What are the relevant angiosperm population sizes and the number of mutations that separate branches on the tree? Are timescales remotely consistent with e.g., the age of angiosperms on Earth?

Neutral processes have a well-established role in key aspects of angiosperm evolution, for example genome complexity (Lynch and Conery, 2003). This would suggest that the relevant timescales and generation times are not completely prohibitive of neutral processes also playing a role in the evolution of angiosperm leaf shape. Effective population sizes in plants are highly variable but estimates span 10^3-10^6. Assuming diploidy (and therefore average fixation time of 4Ne) and generation times of 1-10 years, this gives fixation timescales of 10^3-10^7 years. This is within the timescales of the trees we analyse, which span >150 million years.

Reviewer #2 (Public review):

Strengths:

The paper's underlying question is interesting, extending the authors' prior work on RNA along similar conceptual lines. The paper combines both image analysis of leaves and a computational analysis of a simple model of leaf development.

Weaknesses:

The entire paper is based on the Runion model. More intuition about the Runion model would be useful for a broader readership that cares about the evolutionary aspect of this, but may not know the developmental model in question. Obviously, this is prior well-established work, but 2 - 3 sentences highlighting the key structural aspects of such a model would be great.

Currently, that intuition is found implicitly in a sentence on page 2 ("complex leaf shapes need more specificity in their GRNs than their simpler unlobed leaf shape"), but the reader is left wondering - is the Runion model a detailed mechanistic one with multiple interacting genes/proteins? If so, how many? Or is it just 2 - 3 genes but with complexity entirely in how long they are each expressed/when they are turned off, etc.

We thank the referee for the suggestion to make the paper more useful for a broader readership. To that end, we have added a more detailed description of the (Runions, Tsiantis and Prusinkiewicz, 2017) model in supplementary information section S1.A "Leaf model details".

The Runions model has nearly 100 free parameters. Random walks in 100dimensional spaces have generic properties like a tendency to move toward regions of larger volume that have nothing to do with leaf biology. How do you disentangle the geometry of high-dimensional random walks from genuinely biological developmental bias? Would a toy model with 100 parameters and arbitrary phenotype categories also show "bias toward simplicity" if "simple" phenotypes occupy more volume?

Our argument is largely independent of the number of parameters. While it is true that most of the volume is near the surface in a high-dimensional space, our argument is about the relative volumes of the sets of parameters that map to each of the four phenotypes, an entropic argument if you wish. The basic intuition is that a simple phenotype needs fewer parameters to be fine-tuned, and so a larger volume of parameter space will map to a simpler phenotype.

The question about a toy model with arbitrary phenotypes is helpful because it allows us to clarify that what we are illustrating here with the biologically realistic example of leaf shapes is a much more generic principle. We can say with confidence that if the toy model generates a many-to-one set of outputs (phenotypes) through an algorithmic process whose description length does not grow faster than logarithmically with the size of the genotype space, then it should produce a bias towards simplicity regardless of the number of dimensions, see for example Johnston et al. (2022) and Dingle, Camargo and Louis (2018) for a longer discussion of this more general point which is based on arguments from algorithmic information theory (AIT). We do not use that framing in the current paper because the basic intuition for GRNs, that more complex phenotypes need more parameters to be fine-tuned and so have relatively smaller volumes, is more straightforward to understand than the more abstract AIT arguments. Our general prediction that this principle should hold more widely for GRNs can be made both by the more formal AIT route, or via the more heuristic fine-tuned parameter route.

It is also true that random walks can have biases towards regions of parameter space with high robustness (Van Nimwegen et al., 1999). For our model, this would mean a bias towards valid leaves, however we have no reason to expect this would bias the rates between different valid leaf shapes. We address this point in methods section C.

The discussion of Figure 4 (PCA of parameter space) uses "area" loosely when what's actually being measured is bin count in a 2D projection of a highdimensional space. I would think that, in general, PCA projections can be misleading about volume in the full parameter space, but I can't tell if that's an issue in this case. Some comments/thoughts here would be useful.

The quantitative estimate of phenotype frequencies is computed directly in the full parameter space and does not depend on PCA. We estimate that the total volume of viable leaves maps to simple unlobed leaves about 80% of the time. However, the volume is extremely high-dimensional, and so hard to visualise. PCA is used solely to provide an interpretable visualization of this otherwise high-dimensional structure. The PCA plots in Fig 4 and Fig S16 are there to be illustrative, not quantitative. Because the volume differences are large, we do not think that the projections of the main PCA components would be misleading on at least the ordering of the sizes of the parameter space components that map to each leaf shape. We provided a similar analysis for other projections -- PC1-PC6 (supplementary information section S3.B "PCA occupancy for higher dimensions"), finding the same trend. To make this point clearer, we have now changed the sentence in the Fig. 4 caption slightly “This (reveals that --> illustrates how) unlobed leaves occupy a larger region of model parameter space than more complex shapes and that this larger space also contains the majority of more complex leaves.”

The classifier validation section is in the Methods section, but it seems critical to the whole story. The < 80% agreement with manual classification could propagate to the rest of the estimates in the paper. Again, some comments/thoughts here would be useful.

The review raises a valid concern. In response, we have repeated the analysis of the agreement between by-eye and automatic morphometric classification and produced a confusion matrix for the two classification methods to make the uncertainty clearer (see supplementary information Fig S7, section S1.E). The confusion matrices show that the agreement between the by-eye and automatic morphometric methods is high for unlobed, dissected and compound. The main source of disagreement is leaves that were classified as lobed by eye being classified as either unlobed or dissected by the automatic morphometric method. The proportion of by-eye lobed leaves classified by the automatic-morphometric method as either unlobed (27%) or dissected (23%) is relatively balanced, which we think will cancel out some error as well. Moreover, we find that the agreement between the automatic-morphometric method and by-eye classification increases to 90.0% when using the categories unlobed and all other categories grouped into one (complex). This is the most important classification for our finding that development and phylogeny are both biased towards unlobed.

The authors should explain Mut2 and Mut5 in the main paper with a sentence or two, at least schematically, because how you mutate is obviously very relevant to interpreting a paper about biases in variation.

We agree that this information should be readily available in the main text. In response, we have added a sentence to the results section C for more detail on the random walk.

"[We mutated the initial sample using a random walk algorithm with two different mutational schemes, MUT2 (alg. 1) and MUT5 (alg. S2).] These algorithms work by iterating through model parameters one by one and perturbing the value by a small amount. We then [automatically classified the resulting shapes...]"

However, we note that in methods section C there is already a more detailed description of both algorithms.

“MUT2 (alg. 1) iterates through the parameters in a random order, and attempts to change the parameter by a value selected at random from an array of numbers randomly generated at 3 different orders of magnitude. MUT5 (alg. S2) is the same as MUT2 except that each mutation is additionally scaled by 10% of the current parameter’s range within the initial leaves (fig. S6). The aim here was to provide some way of accounting for the biologically relevant sampling range."

Moreover, the MUT2 algorithm is described in pseudocode in Algorithm 1 in the main text, and the pseudocode for MUT5 is in supplementary information section S1.C, as algorithm S2.

The two mutational schemes use additive perturbations to individual parameters. Real mutations presumably affect regulatory networks in more structured ways (e.g., changing binding affinities that affect multiple parameters simultaneously). How sensitive are the results to the assumption of independent single-parameter mutations?

The referee raises an interesting and well-known issue concerning this widely studied class of GRN models. Without a detailed understanding of how individual genetic mutations map onto model parameters, it is difficult to determine with confidence whether a mutation would produce correlated changes in certain sets of parameters. Our main argument, however, is that the primary source of the observed bias is geometric: the volume of parameter space (or equivalently, the entropy) corresponding to simple leaf morphologies is substantially larger than that corresponding to complex morphologies. As long as mutations explore parameter space approximately symmetrically, even if they involve correlated changes in multiple parameters, larger phenotype regions will tend to be encountered more frequently and retained for longer than smaller regions. We therefore expect the observed bias to be robust to many alternative mutation models, as is already supported by the agreement between our two mutational schemes, although quantifying this robustness is an interesting direction for future work.

The connectedness argument is made using a 2D PCA projection. Is there a way to check this statement in the full parameter space or perhaps in higherdimensional projections to test the robustness of this result? Connected components can merge/split under different projections.

We agree that the 2D projection alone is limited. We therefore performed a new analysis using the same method but in the full dimensional parameter space. The nearest neighbour graph for the full-dimensional data has the following numbers of connected components: unlobed-146, lobed-273, dissected-255, compound-315. This follows the same pattern identified for the PC1-PC2 projection, that unlobed splits into fewer connected components than other leaf shape categories. We have added this result to the caption in figure 9.

References:

Dingle, K., Camargo, C.Q. and Louis, A.A. (2018) ‘Input–output maps are strongly biased towards simple outputs’, Nature Communications, 9(1), p. 761. Available at: https://doi.org/10.1038/s41467-018-03101-6.

Johnston, I.G. et al. (2022) ‘Symmetry and simplicity spontaneously emerge from the algorithmic nature of evolution’, Proceedings of the National Academy of Sciences, 119(11), p. e2113883119. Available at: https://doi.org/10.1073/pnas.2113883119.

Lynch, M. and Conery, J.S. (2003) ‘The Origins of Genome Complexity’, Science, 302(5649), pp. 1401–1404. Available at: https://doi.org/10.1126/science.1089370.

Pagel, M. (1994) ‘Detecting correlated evolution on phylogenies: a general method for the comparative analysis of discrete characters’, Proceedings of the Royal Society of London. Series B: Biological Sciences, 255(1342), pp. 37–45. Available at: https://doi.org/10.1098/rspb.1994.0006.

Runions, A., Tsiantis, M. and Prusinkiewicz, P. (2017) ‘A common developmental program can produce diverse leaf shapes’, New Phytologist, 216(2), pp. 401–418. Available at: https://doi.org/10.1111/nph.14449.

Van Nimwegen, E., Crutchfield, J.P. and Huynen, M. (1999) ‘Neutral evolution of mutational robustness’, Proceedings of the National Academy of Sciences, 96(17), pp. 9716–9720. Available at: https://doi.org/10.1073/pnas.96.17.9716.

I have a Math teacher who grew up in Greece, and at the very start of the year she told us never to raise our hands with our fingers spread. You would think it was a weird rule but the reason was in Greece when you put out your hand with 5 fingers spread its like 5 middle fingers toward someone. Like F*** you 5 times. So she just said Don't do it, as she would always have a negative reaction to it.

I think this is important because patients may avoid getting medical care if they are afraid of being judged because of their condition. As future nurses, we need to make sure our patients feel comfortable and respected no matter what health issues they are dealing with. Building trust and treating everyone without judgment can help patients feel safer asking for help and following their treatment plan.

Looking back at "Old 2", I find myself disagreeing with rmamamnbiba23's point upon these lines. They state "Perhaps it be that, human nature only really can exist ithrough that which is bad or erroneous. But in death, that which is bad is not what is remebered by others despite that it is essentially most important when facing religous judgement." Ultimatley, I find this viewpoint rather lacking, and not entirely what Elliot meant to display in this poem. While yes, much of this poem displays the erroneous nature of man, the poem also provides hope, that man can change and become better, proving that that is is not simply human nature which dictates people to be good or bad. As for their point that ones bad deeds are simply forgotten upon their death, I don't believe this is what Elliot intded to mean by this line. Rather, I think that Elliot is establishing that the only way one can ever live, is through giving to others, and being generous, and no matter how you are remembered in death, that is what truly matters. This is because he "That awful daring of a moments surrender which an age of prudence can never retract, by this and thus only, we have existed which is not to be found in our obituaries." Thus, Elliot is saying, when someone gives to others completely, which is a "daring surrender" they truly live, regardless of what may be recorded upon their tombstone.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

The current study is a follow-up to a previously published study by the same research group (Nold et al. 2025). In the previous study, the authors had included a set of exploratory analyses which assessed the effects of fitness level (denominated by a relative FTP), sex, and drug treatment (Naxolone versus placebo). In this previous study, the authors state that "exploratory analysis showed a significant main effect of fitness level on differences in pain ratings in the [saline] condition... suggesting increased hypoalgesia with increasing fitness levels, pooled across all stimulus intensities".

In the current study, the authors have recruited an additional 22 female participants (21 included in analysis) from local cycling clubs to assess if fitness level does indeed impact exercise-induced hypoalgesia responses to experimental thermal and pressure pain models.

Strengths:

The current study has the potential to present a convincing argument about the effect of fitness level and potentially other factors (e.g., sex) on exercise-induced hypoalgesia responses. Combining data across two of their primary studies would be highly fruitful to the research community interested in this area. Specifically, it has the potential to inform sports medicine practitioners and how they administer exercise protocols to help those experiencing pain with a further consideration for the fitness level (and maybe sex) of their patients.

Weaknesses:

However, the current study makes several bold claims about the role of fitness level and sex on exercise-induced hypoalgesia, which I do not believe that this study on its own - or in conjunction with the previously published study by the same authors - can make at present. Namely, the current study does not appear to conduct any specific analyses between the cohorts from either study (current and present). The results mention a difference in the group mean values in "fitness level" between cohorts, but the analysis itself on pain responses/exercise-induced hypoalgesia is limited only to the cohort from the current study. If the authors wanted to provide a convincing argument that fitness level has an effect on exercise-induced hypoalgesia, then the analysis of this study would have to include an analysis between the groups considered to be of "high" and "low" fitness level. I do not think the current study does this. Instead, it makes an assumption from the previous study (Nold et al. 2025) which only states that "exploratory analysis showed a significant main effect of fitness level on differences in pain ratings in the [saline] condition... suggesting increased hypoalgesia with increasing fitness levels, pooled across all stimulus intensities". The analysis of this study would have to include fitness level "high fitness" versus "low fitness" of participants across both studies in its statistical model to properly discern if fitness level has an impact on exercise-induced hypoalgesia.

A similar comment can be made with respect to sex differences, as these have not been assessed in the analysis of this study either.

Another area of weakness in this study is how "fitness level" has been demarcated across participants. One issue is how authors have assumed that the current cohort is 'fit', whereas the previous cohort was 'less fit', meaning that the authors could be coming to false conclusions about fitness level. In detail, figures within the current study show a large overlap between the 'fit' and 'less fit' cohorts, where some participants have a higher relative functional threshold power (FTP) in the 'less fit' cohort than the 'fit' cohort and vice versa. Therefore, I believe the authors should better demarcate between those that are in the 'more fit' and 'less fit' groups according to a validated and well-established criterion from the kinesiology and sport science literature. That being said, I think this may be problematic in some ways as FTP is considered a relatively poor measure to denote fitness levels, a limitation highlighted in the previous study's review.

Altogether, whilst I commend the researchers on their body of work across the two studies, the current methods and analysis provide an incomplete assessment of their primary research question, and therefore, I would urge the authors to reconsider some of their methods/analysis and the framing of their results to better reflect the main research question they have attempted to answer. Likewise, I would recommend that readers ensure they consider the current results with caution until the authors have addressed some areas of concern which currently limit their main conclusions.

We sincerely thank the reviewer for their thorough and insightful comments and for the time invested in reviewing our work. In response, we have made several important revisions, particularly to address the major concerns regarding fitness level and sex differences.

Specifically, we have:

(1) Conducted additional pooled analyses to directly evaluate fitness and sex effects.

We pooled the data from the previous and current studies and conducted linear mixed-effects models investigating the effect of exercise intensity between the subgroups, as well as specifically testing the effect of fitness level and sex across the pooled data. This allowed us to directly test the effects of fitness level and sex on a common scale rather than infer these effects from separate cohorts. To quantify evidence both for and against the presence of exercise-induced pain modulation and its moderation by fitness, sex, and study sample, we estimated Bayes factors comparing nested models of increasing complexity. In addition, we examined the posterior distributions of the regression coefficients (β) and subgroup- specific (males from previous study, females from previous study, females from current study) exercise effects to estimate the magnitude and uncertainty of these effects. The Bayesian analyses provided some evidence that fitness level moderated exercise-induced pain modulation, but sex did not. Importantly, these findings were consistent with the overall pattern of results obtained in the frequentist analyses. All corresponding statistics in the main manuscript and Supplementary Materials have been updated accordingly. To improve transparency, the pooled analyses are now presented in the dedicated Results subsections and accompanied by new figures (Figures 4 and 5). Furthermore, we have adapted the Title, Discussion and Conclusion to more closely reflect the results.

(2) Clarified the assessment of fitness level.

We expanded our consideration of fitness level and training status by discussing training volume as an additional indicator of training status. We also acknowledge that fitness is a continuous construct and that some overlap in FTP values exists between cohorts. To address this concern, we conducted pooled analyses using FTP as a continuous predictor rather than relying solely on cohort membership. For consistency and comparability with the previous study, FTP remained our primary indicator of fitness level, while analyses using training volume are now reported in the Supplementary Materials.

(3) Expanded the mechanistic background on the effect of fitness level and sex on EIH.

We expanded the mechanistic background in both the Introduction and Discussion to provide a clearer theoretical rationale for how fitness level and sex may influence exercise-induced hypoalgesia (EIH), drawing on relevant experimental and clinical literature.

Reviewer #2 (Public review):

This study addresses an important question regarding exercise-induced modulation of pain in women, but the conclusions appear to be based on relatively limited and selective evidence. The authors report an interaction between exercise intensity and stimulus intensity, which they interpret as evidence for exercise-induced hypoalgesia and conclude that fitness, but not sex, modulates this effect. However, this main result relies on a relatively small interaction that emerges only under specific conditions, with inconsistent findings across pain modalities and stimulus intensities, and an analysis approach that does not fully exploit the continuous pain ratings collected. The lack of a baseline condition further limits the interpretability of the findings as reflecting hypoalgesia, and overall, the data provide a rather constrained basis for drawing broader conclusions.

Strengths:

(1) The focus on women is important and timely, particularly given the ambiguity in prior findings and the historical bias toward male-dominated samples.

(2) The attempt to revisit previous findings in a new cohort is valuable in principle.

Weaknesses:

(1) The core interpretation may not be fully supported by the data

The central claim-that the results demonstrate exercise-induced hypoalgesia and its dependence on fitness but not sex-does not appear to be fully supported by the evidence presented.

(1.1) Lack of baseline condition

The absence of a no-exercise baseline substantially limits interpretation. The study compares high- and low-intensity exercise, but without a baseline, it is not possible to determine whether either condition produces hypoalgesia or hyperalgesia relative to calibration. The observed HI-LI difference, therefore, reflects only a relative contrast between exercise intensities, not an absolute reduction in pain. As a result, attributing the findings to "hypoalgesia" may be difficult to justify fully.

(1.2) Lack of internal replication across conditions

The reported effect is highly specific and does not clearly generalise across the experimental design. It emerges significantly only for heat pain at the highest stimulus intensity, with no clear effects for other intensities and for pressure pain. Moreover, the main statistical result is a relatively small interaction effect with a modest p value, which translates into a difference of approximately 6-8 VAS units on a 150 scale. This combination-a small effect size, limited statistical strength, and restriction to a single condition-substantially weakens the evidence for a robust or generalisable effect.

(1.3) Deviations from the original study and selective use of data

Although framed as a follow-up to previous work, the current study introduces substantial methodological changes, particularly in the acquisition and scaling of pain ratings (continuous vs post-hoc ratings, modified VAS with sub-threshold range). Despite collecting rich continuous data, the analysis focuses on peak responses to approximate the previous study. While this may aid comparability, it results in a strong emphasis on a single data point (highest intensity), rather than leveraging the full dataset. This limits both interpretability and comparability.

(1.4) Over-reliance on null results regarding sex differences

The conclusion that fitness, but not sex, modulates exercise-induced pain may not be directly supported by the data presented. The current study includes only highly fit women, and comparisons with men or less-fit women rely on non-significant differences in a previous cohort. The absence of a significant difference does not provide evidence for equivalence, and no formal statistical support for a null effect is provided. As such, conclusions about the absence of sex differences would unfortunately benefit from more cautious interpretation.

(2) Limited sample and lack of diversity

The dataset is narrow in scope, comprising a small sample (N = 21) of healthy, highly fit women. Key demographic characteristics (e.g. age range, BMI distribution) are not fully presented, explored or discussed. This limits generalisability and makes it difficult to draw broader conclusions about exercise-induced pain modulation in women, as the main focus of the study.

(3) Methodological choices limit the interpretability of the data

Several methodological decisions would benefit from stronger justification:

(3.1) The use of a non-standard VAS scale (0-150 with a fixed pain threshold at 50) is unconventional and may influence how participants report pain, while limiting comparability with related literature.

(3.2) Participants explicitly reported expecting exercise to reduce pain, introducing a potential confound that is not presently addressed.

(3.3) A more comprehensive use of the full time series of pain ratings would provide a stronger and more transparent basis for interpretation of the present findings.

We sincerely thank the reviewer for their time and effort invested in reviewing our manuscript and appreciate the comments. In response to the points raised by the reviewer, we have now updated our work. Specifically, we have:

(1) Pooled samples and strengthened inferential framework:

We pooled the current and previous datasets to provide a stronger basis for the primary interpretation of the findings. On this combined dataset, we conducted both frequentist linear mixed-effects models and complementary Bayesian analyses, allowing us to directly test effects of fitness level, sex, and exercise intensity within a unified framework and to quantify both effect sizes and evidence for/against key hypotheses. The Title, Results, Methods and Discussion have been adapted to more closely reflect the results.

(2) Addressed sample limitations through pooled analysis:

To mitigate limitations related to sample size and composition in the individual studies, we extended all primary inferential analyses to the pooled dataset. This approach increases statistical power, improves the stability of estimates, and enables a more reliable examination of between-group effects across fitness level and sex, thereby strengthening the generalisability of the findings.

(3) Expanded analyses of continuous pain ratings:

To address methodological concerns regarding the use of a summary pain metric, we supplemented the primary peak-based analyses with additional linear mixed-effects models on the full time-series data. Specifically, we modelled time × exercise intensity interactions for both heat and pressure pain, thereby capturing the dynamic structure of pain responses and ensuring that conclusions are supported by the richness of the continuous rating data. These analyses have been added to the Supplementary Materials.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Synopsis

The current study is a follow-up to a previously published study by the same research group (Nold et al. 2025). In the previous study, the authors had included a set of exploratory analyses which assessed the effects of fitness level (denominated by a relative FTP), sex, and drug treatment (Naxolone versus placebo).

In the current study, the authors have recruited an additional 22 female participants (21 included in analysis) from local cycling clubs to assess if fitness level impacts exercise-induced hypoalgesia responses to experimental thermal and pressure pain models.

All the analysis of this study seems to be specific to the "fit" cohort from this study. No analysis or figures seem to show differences between cohorts from the current and previous studies. For this study, the authors found that maximum pain ratings after application of a thermal stimulus and pressure pain stimulus were lower after a high-intensity exercise compared to a lower-intensity exercise. There was also an exercise intensity × stimulus intensity interaction when thermal stimulations were applied, suggesting that the exercise-induced hypoalgesia response varies across exercise intensities as the stimulus intensity increases/decreases. The same cannot be said for pressure pain according the statistical analysis outputs of this study, although inspection of Figure 3B (top row) does illustrate that at higher stimulus intensities, there is a difference between exercise intensities for maximal pain ratings, whereas there is no difference at lower stimulus intensities (30 and 50 VAS). However, observing the changes in maximum pain ratings (Figure 3C) does show similar changes across all stimulus intensities for pressure pain, unlike thermal pain. Therefore, the authors claim that there is an effect of fitness level on the exercise-induced hypoalgesia response.

Overall, the authors have completed a neat supplementary study to their previous study. However, there are several areas that I believe should be addressed within the current manuscript.

First, the authors regularly state "...the hypoalgesic response to exercise depends on fitness level but not on sex". As mentioned earlier, the results section of the previous study states that "exploratory analysis showed a significant main effect of fitness level on differences in pain ratings in the [saline] condition... suggesting increased hypoalgesia with increasing fitness levels, pooled across all stimulus intensities". In this study, the authors do not seem to have completed a direct comparison between the two study cohorts. The results for the current study only seem to discuss the effects of exercise intensity within this study cohort. If this study is to be treated as a stand-alone study, then the data that is presented should make it clear that the effect of fitness level is being assessed. Currently, the results and the figures only illustrate the effects of exercise intensity and stimulus intensity, not fitness level (or sex), which are mentioned in the title, abstract, and most discussions.

Second, on the topic of sex-related effects, as authors repeatedly state ""...the hypoalgesic response to exercise depends on fitness level but not on sex", I think it is worth noting that this statement would require an a priori assessment of sex differences on exercise-induced hypoalgesia responses. As the previous study (exploratory) and this study (no sex difference analysis) do not include this a priori assessment, I do not think they can conclude that sex is not a factor in the exercise-induced hypoalgesia response, though they can surmise that fitness level may have an influencing role if it was specifically tested in this study. If the authors wish to judge the role of sex, there ought to analysis on this specifically.

Third, whilst the authors have tested the effects of "fitness level", I urge the authors to consider how they have demarcated between fitness levels in this study and any other (validated) criterion that could be used in place of their current method to distinguish between "fit" and "less fit" participants. To explain the cohort of the current study is judged to be "fitter" than the previous study based on the group mean relative FTP. Yet, observing Figure 1, there are several participants with lower relative FTP in the "fit" cohort than the "less fit" cohort, and vice versa. I would recommend the authors to consult with some kinesiologists/sport scientists about this issue. As the central topic of this study is the effect of fitness level, this warrants careful consideration, as the current method to split the groups is problematic, especially as there is clear overlap between the two groups in the metric that the authors have used (relative FTP).

Fourth, I think it would be highly beneficial for the authors to add more discussion around the theoretical and mechanistic accounts about why fitness level (and sex) would impact exerciseinduced hypoalgesia responses. The current manuscript provides a nice account of the current literature in terms of the direction of each study's results, yet they do not explore why fitness level or sex has such effects. This would be highly valuable to a reader to set the tone of the study rationale in the introduction and provide more depth to the authors' discussion of their results.

Below I have highlighted all my comments that have been separated into MAJOR and MINOR comment sections.

I hope my comments are of use to the authors, and I would like to thank them and the journal for the opportunity to review their paper on a truly interesting and insightful topic.

We thank the reviewer for their insightful comments and appreciate the time invested in reviewing our work. In the following, we have addressed all comments raised by the reviewer and marked all changes in the manuscript.

Major Comments

(1) In my opinion, it would enhance the manuscript if the authors provided a theoretical or mechanistic account of why fitness levels or sex would impact the exercise-related hypoalgesia effects. Though some reasoning about the mechanisms of fitness level and sex is mentioned in the discussion of the previous study (Nold et al. 2025), and even if the overall research findings are mixed at present, I do not think it would be overkill to provide the rationale for why the authors do/do not predict a certain response in the current study after their analyses. On this note, the authors may argue that the manuscript content from L52-61 is an account of the previous literature. However, whilst this literature sets out the directions of previous research findings, as I read this, I do not think there is a theoretical framework to underpin why fitness level or sex would impact exercise-induced hypoalgesia (EIH). References already included in the manuscript should have some discussions around this (e.g., Sluka et al. 2018; Koltyn 2000; Koltyn et al. 2014).

We thank the reviewer for their comment. We agree that the mechanistic rationale for why fitness level and sex may influence EIH could be described in more detail. Accordingly, we have expanded the Introduction/Discussion to provide a more comprehensive overview of the potential mechanisms underlying these effects, drawing on previous EIH literature (e.g., Sluka et al., 2018; Koltyn, 2000; Koltyn et al., 2014) as well as evidence relating to changes in endogenous modulatory systems due to repeated exercise (Anderson & Shivakumar, 2013; Gajic et al., 2026; Matei et al., 2023; Saanijoki et al., 2022; Song et al., 2022) as well as sex differences in these neuromodulatory systems potentially contributing to sex differences in EIH (Blanton et al., 2021; Castelli et al., 2014; Fullerton et al., 2018; Levine et al., 2021; Loyd et al., 2008; Zubieta et al., 2002).

(2) The study sets out an aim, but I do not see any (a priori) hypotheses in the intro or methods. If no hypotheses were registered, this can be reported in the discussion and factored into the discussion about why certain results would/would not be expected.

The reviewer is correct that no formal, pre-registered hypotheses were specified for this study. As this study was designed as a follow-up to our previous study, which reported no exercise-induced pain modulation in relatively less fit females, the present investigation was primarily exploratory in nature and aimed to examine whether exercise-induced pain modulations would be observed in a sample of females with significantly higher fitness levels. We have now clarified this in the discussion and acknowledge the exploratory nature of the study when interpreting the findings.

(3) Is there a sample size justification, sensitivity analysis, or post-hoc calculation for the additional 21 participants to detect effects for fitness level and sex?

We thank the reviewer for this question. No formal a priori sample size calculation was performed for the recruitment of the additional 21 participants. The current study was designed as a follow-up to our previous work, in which female participants were, on average, slightly less fit than male participants. To better disentangle the effects of fitness and sex, we therefore aimed to recruit a comparable number of female participants with higher fitness levels. Accordingly, we targeted a sample size similar to that of the female subgroup in the previous study.

(4) I have a wider question about where there has truly been a test between fitness levels.

Definition and measurement of "fitness level".

Is there an appropriate rationale that relative FTP is an appropriate measure to distinguish between fitness levels? Understandably, this is done for consistency between the two studies, and there may be mention of the use of the FTP measure in the original study; however, it would be worth justifying the use of the relative FTP measure to categorise fitness level with previous literature to back this up.

We thank the reviewer for this very valid and important point regarding both the validity of FTP as a proxy for fitness and the distinction between fitness levels. Previous research has shown that the FTP and FTP20 tests are reliable and convenient methods to estimate approximate measures of VO2max (Denham et al., 2020) and that the FTP test is a useful test for performance prediction in moderately trained cyclists (Sørensen et al., 2019). Furthermore, we argue that FTP represents a continuous performance measure in our studies instead of a categorical variable distinguishing between fit and unfit individuals, and we have strengthened the manuscript by providing a clearer justification for its use as a field-based proxy of endurance fitness, supported by previous literature linking FTP to more direct physiological markers such as VO_2max (Denham et al., 2020). Since we have used FTP in the previous sample as a measure of fitness level, we maintained this for consistency in the current study.

We also acknowledge that, despite statistically significant group differences, there is meaningful overlap between the males of the previous study and the females of the current study and that “fitness level” should be interpreted as a continuum rather than a strict categorical separation. Accordingly, the labels “fit” and “unfit” should be interpreted relative to the samples included in the current and previous studies rather than as absolute classifications. To reflect this more accurately, we have revised the manuscript to refer to participants as having higher or lower fitness levels, which should be interpreted within the context of the pooled sample rather than as discrete fitness categories.

Classification of fitness level.

In L110-111 - The statistical analysis does show a difference between groups, but Figure 1A does show that there is a crossover with around half the sample from each study cohort. That is, the current study had ~16 participants who had a lower relative FTP than the highest relative FTP from the previous study. When removing the highest participant (outlier) in the previous study, there are still 7 participants (a third of the sample) with a lower relative FTP than participants considered of a 'lower' fitness level than the previous study.

Essentially, on the group level, there is a statistical difference in relative FTP, but there is notable overlap between the two groups.

We thank the reviewer for this observation. Our aim was not to create entirely non-overlapping fitness categories, but rather to recruit a female sample with significantly higher average fitness levels than the females included in the previous study. As shown in the revised manuscript, females from the current study had, on average, significantly higher relative FTP values than females from the previous study, whereas no significant difference was observed between females from the current study and males from the previous study. We also report training volume as an additional indicator of training status; however, because training volume was self-reported, we consider FTP to provide a more objective and sensitive measure of fitness. The partial overlap in FTP values between samples is not unexpected and, in fact, facilitates comparisons across studies by ensuring that the samples are not entirely distinct populations.

Could another distinction be made based on:

- A set value (e.g., 2.0 W/kg-1);

- Another value from previous literature, and the analysis be re-run with this classification of participants? The approach to use a set value is consistent with kinesiology literature that uses set values to demarcate fitness level for other more common, measures like VO2max (see ACSM guidelines and de Pauw et al. 2013);

- Or by dissociating between training volume and slightly tweaking the wording to "training status/volume" (although I am cognisant that this would introduce an incongruence in terminology between the authors' studies, but other studies that have been referenced [e.g., Geva and Defrin, do specifically test between training volume]).

We thank the reviewer for their suggestions. We would like to refrain from making another distinction based on a set value and dividing the group into “fit” and “unfit” individuals. Instead, we have pooled the samples and treated FTP as a continuous variable, which preserves statistical power and avoids the loss of information associated with dichotomising a continuous measure.

To address the reviewers' suggestion of including training volume as a measure of fitness level, we have repeated our new analyses, namely the LMER model using training volume as a predictor for difference pain ratings (LI – HI Exercise pain ratings), in the pooled sample. These analyses yielded no significant effects for training volume, the interaction of training volume x sex, or training volume x subgroup in either heat or pressure pain. Furthermore, the training volume is potentially influenced by outliers in the current study sample. For completeness, we have added these analyses and according visualisation to the Supplements (Fig. S6).

We believe that the FTP provides a more sensitive and objective measure of cardiovascular fitness level in our study, as it is not susceptible to recall bias, differences in training intensity and differences in training efficacy. We also note that other studies (Geva & Defrin, 2013) did not rely solely on self-reported training volume as a measure of fitness level, but recruited participants based on training history and athletic status (e.g. competitive triathletes vs. active controls).

For these reasons, we consider the FTP the most appropriate primary indicator of fitness level in the current (and previous) study, while still reporting training volume in the main manuscript to consider.

The above suggestions would also allow to select matched pairs from the male cohort when comparing effects between sexes. Altogether, though, I believe this comment to be the most important in my review of this paper, as the primary question depends strongly on how fitness level is defined and categorised by the researchers, and this requires careful consideration and validation from previous literature if such decisive conclusions are to be drawn from the results. Therefore, a clearer description of the reason why certain effects are expected (theory/mechanisms) and how participants have been categorised will be highly valuable for readers. It may be useful for the authors to reach out to kinesiologists/sport scientists within their peer groups to help with this comment.

To further address the concern regarding between-cohort comparability, we have now pooled the samples from the previous and current study and re-analysed the data fitness level as a continuous variable rather than relying on cohort-based comparisons. Specifically, we conducted regression analyses examining fitness level, sex, and their interaction, as well as subgroup analyses including males from the previous study, females from the previous study, and females from the current study. These analyses were complemented by Bayesian model comparison and posterior inference. The results are now reported in the Results section. We also acknowledge that fitness is best viewed as a continuum rather than a discrete characteristic and have revised the manuscript accordingly, replacing references to “fit” and “unfit” participants with descriptions of relatively higher and lower fitness levels within the pooled sample.

Finally, as mentioned in the previous comment (major comment #1), we have expanded the Introduction and Discussion to more clearly outline the mechanistic and theoretical rationale for expecting effects of fitness level and sex on exercise-induced pain modulation, drawing on relevant literature (see major comment #1). We believe these additions substantially strengthen both the conceptual justification and the analytical robustness of the manuscript.

(5) The abstract states that "...further investigation to determine if and to what extent exercise induced hypoalgesia depends on fitness level and/or sex." However, I cannot see any analysis relating to sex in the results of this study that takes the female sample of this study and the male sample of the previous study and then carries out another LNER model? I also see no report of results about sex in any of the figures/tables. If sex is part of the abstract and main research question, then I would argue it ought to be in the results and feature in figures within the main manuscript, not supplementary material.

We agree with the reviewer that, given the emphasis on fitness and sex in the Abstract and research aims, analyses directly examining sex effects should be presented in the main manuscript. In response, we pooled the samples from the previous and current studies and repeated the linear mixed-effects regression analyses used in the previous study to examine the effects of fitness and sex on exercise-induced pain modulation. We further complemented these analyses with Bayesian model comparison and parameter estimation to assess the moderating effects of fitness level and sex in the pooled dataset. The results of these pooled analyses are now reported in the corresponding Results section and are presented in the main manuscript as Figure 5. The Abstract, Results, Discussion, and Conclusions have been revised accordingly.

(6) The current abstract and main manuscript make it seem that this study completed an additional analysis on the effect of sex, but this does not appear to be the case. Statements like "together with our previous findings, this suggests that exercise-induced hypoalgesia depends on fitness level but not on sex" are quite decisive, although it does not seem that any analysis was completed between sexes in an a priori fashion. The only data I can see that assesses between sex effects is an exploratory analysis from the previous study, which was part of a larger exploration of sex - fitness level - and drug interactions.

Therefore could the authors either:

- Run this analysis between sexes;

- Or make it explicit that this study did not conduct any specific a priori analysis on sex differences in EIH at high and low intensities.

- And/or temper how decisive their conclusions on the (null) effects for sex, unless there are statistical analyses to support this.

We thank the reviewer for this suggestion. We agree that the manuscript did not include a dedicated analysis of sex effects in the combined dataset. In response, we pooled the samples from the previous and current studies and conducted additional frequentist (LMER) and Bayesian (Bayes Factor and posterior distributions) analyses examining the effects of fitness and sex on exercise-induced pain modulation. The frequentist analyses indicated an association between fitness and EIH, but not sex, while the Bayesian analyses similarly provided little evidence for sex-dependent effects. These new analyses have been added to the manuscript, and the Abstract, Results, Discussion, and Conclusions have been revised accordingly.

Section-specific Comments:

(1) Abstract

L38-40: See major comment #6 above.

As described above, we have now conducted additional analyses on the moderating effect of fitness level and sex using frequentist and Bayesian analyses and adapted the Abstract accordingly.

(2) Introduction

L68 - What is meant by "robust" in this sentence? Robust to describe the direction and magnitude of the differences in effects between sexes seems a little misrepresentative.

We thank the reviewer for their comment and agree that the wording is vague. To emphasise clarity, we have rephrased this to “[…] whereas others (Koltyn, 2000; Sternberg et al., 2001; Vaegter et al., 2014) suggest that hypoalgesia following exercise is more pronounced in females, but overall results remain inconclusive (Rice et al., 2019).”

(3) Results

L124 - What is the online rating scale? It is the word "online" in particular that is confusing here, as it is described in the methods, but just seems to be a standard handheld device with a cursor.

We thank the reviewer for their comment. In this case, “online” refers to the continuous ratings whilst the stimulus is ongoing, using a handheld rating device and using button presses. We clarified this further at the beginning of the Results and Methods sections to include “real-time (continuous) pain ratings” to avoid confusion.

L136 - I think there is a missing word here before the set of parentheses. RPE?

We thank the reviewer for detecting this and have added “RPE” before the parentheses.

L136-138 - I would amend to read something like... "This confirms the exercise intensity protocols elicited a different output, relative power, physiological demand (HR), and perceived demand (RPE)", just to be clear on what the differences have been physiologically and psychologically for the participants when exercising at the two intensities.

We agree with the reviewer and have rephrased the sentence according to their suggestion for clarity.

(4) Discussion

L190 - "results suggest that fit females show a hypoalgesic response to HI compared to LI exercise". I think there is a word missing in this sentence to make it clear what the results are.

We have revised the sentence in accordance with the new (pooled) analysis results.

L250-253 - The authors have given a fantastic account of the previous literature and the trends that each study has observed. However, in line with major comment #1, could the authors include some discussion to speculate why there are expected differences between training level/fitness level and sex (plus interactions)? Some studies that are referenced are theoretical papers, and even if the current literature is unsure about the likely mechanisms behind fitness and sex differences in EIH responses, stating this would also be useful to a reader but the authors could signpost them to specific references that would broaden their understanding after reading this study.

We have now provided a more detailed account of the potential mechanistic background on why fitness level and/or sex could influence exercise-induced modulation in the Discussion (see major comment #1).

(5) Limitations

L258-259 - If I have understood this sentence correctly and the content in L301-304, the heat stimulus (temperature of the thermal probe) that was applied to induce a 30 VAS pain intensity rating at rest actually induced no pain at all, as 30 VAS is considered below the pain threshold of "minimally painful". In retrospect, this seems like an odd choice of measurement.

It means that 30 VAS is simply a measure of warm (non-painful but detecting heat) and perturbation to the skin (pressure but not hurting) in the heat and pressure pain conditions, respectively. Therefore, to include the 30 VAS values in the analysis to dissociate whether HIGH or LIGHT intensities, fitness level, or sex have an impact on EIH seems misplaced, as there is no actual pain for which a hypoalgesia response can be tested at this intensity.

Making this clearer in the results or discussion would be worthwhile for the readers, in my opinion.

We thank the reviewer for highlighting this. In both the previous and current studies, participants were calibrated using the same procedure and rating scale (0 – 100) to identify painful stimulus intensities corresponding to VAS 30, 50, and 70. On the main experimental day, participants in the current study rated on a modified scale ranging from 0 to 150, with 50 marking the pain threshold, such that ratings below 50 reflected a non-painful rating. Importantly, the calibrated VAS 30, 50, and 70 stimuli refer to the target pain intensities established during the calibration procedure and not to the numerical values displayed on the experimental rating scale. Participants were familiarised with the scale and anchor points prior to testing and viewed only the visual analogue scale rather than numerical values during the experiment. We have adapted the wording, referring to VAS 30, 50, and 70 as intensities and not numerical ratings.

(6) Conclusion

L276-277 - Similar mention as before, can the authors please make it clear if there is a sex effect in their analyses or how this has properly been tested in a prior study through an a priori assessment to be certain that "fitness level rather than sex plays a central role in modulating EIH".

We have now tested the effect of sex in frequentist and Bayesian analyses in the pooled samples and revised the conclusion in accordance with the results.

(7) Methods

L284 - What denotes an individual being "physically active"?

We thank the reviewer for this question. “Physically active” was defined based on training volume, operationalised as regular participation in structured cycling training sessions (i.e., consistent engagement in planned cycling training units per week). This criterion was used to ensure that participants had an established and ongoing training routine relevant to the study context. We have clarified this in the referenced section.

Table 1 - Female participants in the current study are noticeably older than the other cohorts from the previous study. While all are considered "young" (<40 y.o.), if one were to take a matched pair of females from each cohort (previous vs current) in terms of relative FTP, then the years of experience and exposure to training are likely a strong influence on EIH responses, not "fitness level" as it is described in this study. Just a speculative thought.

The reviewer raises an interesting point. However, since we have not acquired any information on the years of training and volume, we are unable to answer this question in the current framework. Future research should investigate the effect of training years (which potentially strongly correlates with fitness level) on exercise-induced pain modulation.

L313-315 - For future reference, there are some nice papers on how to administer the RPE scales with clear instructions to be certain that perceived effort is being measured appropriately (Halperin & Emanuel 2020; Halperin & Visgotsky 2025; Malleron et al. 2023). I always have a habit of signposting to these studies with regard to RPE because it can often be misrepresented in many different areas of research where RPE scales are used.

We thank the reviewer for this suggestion and for highlighting these relevant papers. In the present study, participants were extensively familiarised with the rating of perceived exertion scale, and the instructions closely followed the original definition and recommendations provided by Borg (1998). The scale was presented in accordance with its intended anchor points to promote accurate reporting of perceived exertion. We have now added a citation (Borg, 1998) in the Methods section to clarify this procedure.

(8) Code Availability

Thank you for including open source code in your submission. I am very appreciative of researchers who champion open research principles.

We appreciate the reviewer’s comment and support of open research practices. We have updated the code containing the updated analyses and datasets.

Reviewer #2 (Recommendations for the authors):

(1) Core interpretation may not be fully supported by the data

We thank the reviewer for this comment. To investigate the role of fitness level and sex in exercise-induced pain modulation, we have now pooled the samples from the previous and current study and conducted frequentist (linear mixed effects models) analyses. Specifically, we tested for the effect of exercise intensity between the subgroups, as well as (consistent with those conducted in the previous study (Nold et al., 2026) testing the effect of fitness level and sex across the pooled data. This allowed us to directly test the effects of fitness level and sex on a common scale rather than infer these effects from separate cohorts. Furthermore, we conducted Bayesian analyses to quantify evidence both for and against the presence of exercise-induced pain modulation and its moderation by fitness, sex, and study sample, utilising the Bayes factors comparing nested models of increasing complexity. In addition, we examined the posterior distributions of the regression coefficients (β) and subgroup-specific exercise effects to estimate the magnitude and uncertainty of these effects. The Bayesian analyses provided some evidence that fitness level moderated exercise-induced pain modulation, but sex did not. Importantly, these findings were consistent with the overall pattern of results obtained in the frequentist analyses. All corresponding statistics in the main manuscript and Supplementary Materials have been updated accordingly. To improve clarity, the pooled analyses are now presented in dedicated Result subsections and accompanied by new figures (Fig. 4 and Fig. 5).

(1.1) Lack of baseline condition

We thank the reviewer for this important comment. We agree that, in the absence of a no-exercise control condition, our design does not allow us to determine whether either exercise condition produced hypoalgesia or hyperalgesia relative to no exercise. Rather, the observed differences reflect the relative effects of high- versus low-intensity exercise on pain ratings.

Our study was not designed to assess the overall effect of exercise compared with rest, but rather to investigate whether exercise intensity influences exercise-induced pain modulation. Specifically, we hypothesised that high-intensity exercise would produce greater pain modulation than low-intensity exercise. This approach was motivated by previous work demonstrating intensity-dependent differences in post-exercise pain responses (Jones et al., 2019; Vaegter et al., 2014).

In response to the reviewer's comment, we have revised the manuscript to clarify this distinction and have replaced several instances of "exercise-induced hypoalgesia" with the more neutral term "exercise-induced pain modulation" where appropriate. We also explicitly acknowledge in the Limitations that the lack of a no-exercise condition precludes conclusions regarding absolute hypoalgesic/hyperalgesic effects of either exercise condition.

(1.2) Lack of internal replication across conditions

We thank the reviewer for this comment. We agree that the observed effect was most pronounced for heat pain at the highest stimulus intensity and was not consistently observed across all stimulus intensities or pain modalities. Importantly, however, this pattern mirrors the findings of our previous study, in which exercise intensity effects were likewise evident for heat pain but not pressure pain. We therefore interpret the current findings as a replication of the modality-specific pattern observed previously rather than an isolated positive result.

To further address concerns regarding robustness and sample size, we have now pooled the data from the previous and current studies and conducted additional frequentist and Bayesian analyses examining the moderating roles of fitness level and sex on exercise-induced pain modulation. These analyses yielded converging evidence that fitness level contributes to variability in exercise-induced pain modulation, thereby strengthening confidence in the overall findings.

With respect to pressure pain, previous meta-analyses have reported comparable or even larger exercise effects for pressure pain than heat pain (Naugle et al., 2012). However, most studies included in these analyses employed handheld pressure algometry, whereas our study used cuff pressure stimulation. Consequently, the pressure pain measures used here may not be directly comparable to those reported in the broader literature.

(1.3) Deviations from the original study and selective use of data

We agree with the reviewer that we have adapted the rating scale to reflect a real-time pain rating. To provide a comprehensive account of participants’ pain experience, we have included analyses corresponding to the visualisations on how online ratings evolve over the course of the pain administered in Supplemental Figure S7 – S8. Specifically, we conducted LMER models with exercise intensity × time on heat and pressure pain ratings, separately (Supplemental Fig. S7). The results yielded a significant interaction of exercise intensity × time on heat (β = -0.13, SE = 0. 06, t(7577) = 2.12, P = 0.03) but not pressure pain ratings (β = -0.07, SE = 0.10, t(7956) = -0.71, P = 0.48). Furthermore, we conducted LMER models with exercise intensity × time × stimulus intensity on heat and pressure pain ratings (Supplemental Fig. S8), suggesting no significant interaction on pressure pain ratings (β = -0.0002, SE = 0.004, t(2353) = -0.06, P = 0.95) but a significant interaction on heat pain ratings (β = -0.01, SE = 0.003, t(2201) = -3.24, P = 0.001).

As the reviewer correctly notes, to facilitate comparison with the previous study, we conducted our primary analyses using peak pain ratings. We acknowledge that this approach does not fully capture the richness of the continuous data but allows for comparability.

(1.4) Over-reliance on null results regarding sex differences

We thank the reviewer for this important point regarding the interpretation of null effects, particularly in relation to sex differences. We agree that the absence of a statistically significant difference does not, in itself, provide evidence for equivalence between groups.

To address this issue, we have pooled the samples and supplemented our frequentist analyses with Bayesian analyses. Bayes factors were computed to quantify the relative evidence for the null versus alternative hypotheses, providing a continuous measure of support that complements frequentist inference, particularly in cases of non-significant effects where evidence for the absence of an effect is of interest. Furthermore, posterior distributions of the regression coefficient of interest (in this case, the moderating role of sex on exercise-induced pain modulation) provided no evidence for a moderating role of sex on exercise-induced pain modulation. This approach allows for a more nuanced interpretation of the data, especially concerning null effects. We have adapted the Methods, Results, and Discussion accordingly.

(2) Limited sample and lack of diversity

We thank the reviewer for this comment. The study was intentionally designed to include only female participants with significantly higher fitness levels compared to the females from the previous study, as our previous study included females who were slightly less fit than males, making it difficult to separate the effects of sex and fitness. We, therefore, aimed to examine exercise-induced pain modulation in a more homogeneous sample. However, much of the EIH literature has been conducted in highly trained male participants (Janal et al., 1984; Saanijoki et al., 2022; Scheef et al., 2012). As such, studies in women of higher fitness are important to improve our understanding of potential sex differences in exercise-induced pain modulation. While the present findings should be interpreted within the context of the sample studied, when analysed and considered alongside our previous work, they contribute to a broader understanding of exercise-induced pain modulation across sexes and fitness levels.

(3) Methodological choices limit the interpretability of the data

(3.1) The use of a non-standard VAS scale (0-150 with a fixed pain threshold at 50) is unconventional and may influence how participants report pain, while limiting comparability with related literature.

We thank the reviewer for their comment. Since we introduced real-time pain ratings in the current study, while the pain is ongoing, we aimed to introduce a scale that allowed us to pinpoint the period when a painful stimulus reaches painfulness (exceeds 50 on the scale). To allow for comparability between the studies, we have calculated the peak pain rating provided during the real-time pain ratings, as this corresponds to the instruction participants received in the previous study to rate the most painful point of the previous stimulation. Previous research (Koyama et al., 2004) has shown that, in heat pain, real-time ratings account for R² = 0.89 of the variability of post-stimulus rating, where much of the variability for the post-stimulus intensity pain rating is accounted for by the peak response during the online ratings (adj. R² = 0.3 – 0.4), suggesting good comparability of both pain measures. Furthermore, as we have now pooled the samples and conducted analyses, we rescaled the maximum pain ratings so that ratings below 50 (below the pain threshold) were set to 0, corresponding to VAS 0 in the previous study, resulting in pain ratings ranging between 0 and 100.

(3.2) Participants explicitly reported expecting exercise to reduce pain, introducing a potential confound that is not presently addressed.

We thank the reviewer for this comment. Indeed, participants reported expecting lower whole-body pain in response to acute aerobic exercise, but no changes in joint or muscle pain. In the context of exercise, previous research (Colloca et al., 2018) showed that exercise-unrelated expectations and exercise itself induce comparable hypoalgesic effects, though they might work through distinct mechanisms. Studies directly manipulating exercise-related expectations showed that education about EIH, compared with general education about exercise and pain, could induce hypoalgesia following aerobic exercise (Jones et al., 2017). Interestingly, another study (Vaegter et al., 2020) investigated the interplay of exercise-related expectations (through verbal instructions) and resistance exercise on pain perception and showed that only explicit negative instructions induced hyperalgesia, whereas positive or neutral exercise-related instructions did not change the magnitude of EIH.

Since participants in the current study reported highly specific positive expectations only for whole-body pain, but not for joint or muscle pain, expectations are unlikely to fully explain our findings. Consistent with this, in our previous study using the same prospective expectation questionnaire, we found no significant expectation effects for any pain domain (Nold et al., 2025), although we acknowledge that the samples differed, especially with respect to fitness levels.

Nevertheless, the current study was not designed to disentangle the effects of exercise and expectations, as expectation ratings were measured prospectively but not manipulated. Therefore, we cannot determine to what extent positive expectations of exercise have contributed to the observed effects, and we have now acknowledged this as a limitation in the Discussion.

(3.3) A more comprehensive use of the full time series of pain ratings would provide a stronger and more transparent basis for interpretation of the present findings.

We thank the reviewer for this suggestion. As noted in our response to Comment 1.3, we have included analyses and visualisations of the full time series of online pain ratings in the Supplementary Materials (Fig. S7–S8), providing a more comprehensive understanding of pain dynamics over time.

Figures are very low in quality - artefacts, small text, insufficient labelling.

We thank the reviewer for highlighting this and, indeed, rendering the PDF reduced the quality of the images. For the reviewed version, we have been specifically attentive to image quality by increasing font sizes and adding labels.

There was not enough detail in the methods section for the number of cycling blocks, and how low and high intensity were distributed throughout the session.

We thank the reviewer for their comment. Participants completed four cycling blocks in total, two HI and two LI exercise blocks, presented in a pseudo-randomised order in the session. To improve clarity, we have added the relevant details to the Methods section.

I never really thought about how something as simple as an address form could make people feel left out. If a website only accepts U.S. addresses, someone from another part in the world may have to enter false information just to use it. This makes me think designers should try to consider more people’s real experiences when they build applications.

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Reply to the reviewers

Reply to the Reviewers

We thank the editor and reviewers for their constructive assessment. The textual revisions and additions described in Section 3 have already been incorporated into the manuscript. The work planned in Section 2 comprises the statistical improvements and supplementary experiments or analyses specified under the individual reviewer comments.

Each comment is answered separately in the original reviewer order. Comments addressed by revising or qualifying the wording are classified as completed textual revisions. They do not create additional experimental commitments. Planned measurements and statistical reanalysis are described prospectively, and no new results or unchanged significance are assumed.

Reviewer 1

Major comment 1. Ciliary integrity is not yet established as the causal or unifying mechanism of microtubule-stabilizer-mediated recovery

A central conclusion of the manuscript is that preservation of ciliary integrity represents a shared structural checkpoint linking microtubule stabilization to spinal cord repair. The data clearly show that Noscapine treatment is associated with preservation of ciliary structures in ependymal cells and CSF-cNs, and that Paclitaxel produces similar cellular effects. However, I do not think the current experiments are sufficient to establish cilia as the causal mechanism underlying the functional benefits of these treatments. In particular, SANT-1 is a Smoothened antagonist and therefore interferes with Hedgehog/Smoothened signaling rather than specifically ablating cilia. Consequently, the partial loss of Noscapine-mediated recovery following SANT-1 treatment could reflect disruption of Hedgehog signaling rather than a specific requirement for ciliary structure. Conversely, Y-27632 is a ROCK inhibitor with broad effects on cytoskeletal organization and has previously been reported to improve recovery after SCI through cilia-independent mechanisms. Thus, while these pharmacological experiments are consistent with a contribution of cilia, they do not by themselves demonstrate that ciliary preservation is required for Noscapine-mediated repair.

The most direct way to test this model would be a temporally controlled genetic disruption of ciliogenesis in the relevant central canal-associated population, for example using the Foxj1-CreER;Ift88/Kif3a strategy already proposed by the authors, followed by assessment of whether Noscapine can still promote recovery. This would provide the strongest test of the central mechanistic claim, although it would represent a substantial experiment requiring several months depending on mouse-line availability. More tractable alternatives could nevertheless considerably strengthen the current evidence. First, the authors could test whether ciliary preservation is reproduced across the full panel of microtubule-targeting compounds used in the initial screen. At present, five compounds are used to support cross-chemotype convergence in functional recovery, whereas ciliary preservation is examined mainly for Noscapine and Paclitaxel. Demonstrating that Epothilone D, TPI-287 and TTI-237 similarly preserve ependymal and/or CSF-cN cilia would provide much stronger support for ciliary preservation as a shared downstream response. Second, if an appropriate primary spinal-cord ependymal or related culture system is available, genetic disruption of ciliogenesis through IFT88 or KIF3A depletion could be used to determine whether Noscapine-associated cellular effects are lost when ciliogenesis is impaired. Such an orthogonal genetic experiment would directly complement the current pharmacological evidence and could likely be completed within several weeks to a few months. Neither alternative would fully establish that ependymal cilia are necessary for functional recovery in vivo, but together they would substantially strengthen the proposed mechanism. If additional experiments are not feasible, the authors should instead moderate statements describing ciliary integrity as "required," a "shared structural checkpoint," or a "unifying downstream dependency," and restrict the conclusion to the evidence that microtubule stabilization is associated with ciliary preservation and that cilia-associated pathways may contribute to recovery.

Response:

We thank the reviewer for this thoughtful and constructive assessment. We agree that the current pharmacological evidence does not establish ciliary preservation as a causal requirement for Noscapine-mediated functional recovery.

To strengthen the evidence, we will first work to establish a suitable in vitro culture system using spinal cord ependymal or related cells. Once this system is established, we plan to compare the effects of the microtubule-targeting compounds used in our initial screen, including Noscapine, Paclitaxel, Epothilone D, TPI-287, and TTI-237, on ciliary structure and maintenance. This comparison will test whether the ciliary effects observed with Noscapine and Paclitaxel extend across the broader compound panel. We recognize that a shared structural response would strengthen evidence for convergence but would not, by itself, establish ciliary necessity.

In parallel, we have begun preparations for a Foxj1-CreER–based conditional Ift88 deletion mouse model for subsequent in vivo validation. Our aim is to determine whether Noscapine retains its beneficial effects when ciliogenesis is genetically disrupted in the targeted population.

Several mechanistic statements in the current preliminary revised manuscript have not yet undergone final coordinated revision, as we plan to validate these interpretations via the listed supplementary experiments. We have marked these relevant statements in red within the main text to indicate that these conclusions are pending revision. If the follow-up supplementary data cannot be obtained, yield inconclusive results, or fail to support the above inferences, we will qualify or remove the corresponding claims and retain only those observations directly supported by experimental data.

Major comment 2. Several conclusions extend beyond the experimental readouts

Several conclusions throughout the manuscript appear broader than the experimental readouts used to support them. I think these points should be addressed individually, either by providing additional quantitative analysis where this can reasonably be performed on existing material, or by revising the wording so that the conclusions more closely reflect what was directly measured.

a. Glial and fibrotic scarring. In the Abstract, the authors state that maintenance of ciliary architecture is associated with "reduced glial scarring" (line 31). However, the main quantitative assessment of scarring in Figure 2 is based on Laminin-positive area, which is described as evidence of reduced "ECM/fibrotic scarring" (lines 103-107). GFAP staining is shown, but glial scar formation itself does not appear to be qualitatively or quantitatively assessed. The claim of reduced glial scarring should therefore either be supported by further histological analysis (H&E staining, antibody staining for various ECM component, superficy of scar measurement and so on) or removed. Similarly, reduced Laminin deposition is consistent with altered ECM/fibrotic remodeling, but Laminin alone provides a relatively limited assessment of the fibrotic scar. If the authors wish to maintain the broader claim of reduced fibrotic scarring, additional characterization of the fibrotic compartment would strengthen this conclusion; otherwise, "reduced Laminin deposition" would more precisely describe the result.

Response____：

We thank the reviewer for pointing out our over‑interpretation of scar‑related results. We agree that Laminin staining alone is insufficient to support broad conclusions about glial and fibrotic scarring without additional histological quantification.

We have revised the manuscript to limit conclusions strictly to our available data. We replaced the claim of “reduced glial scarring” from the Abstract with “reduced Laminin deposition” (line 31). The expression of “reduced ECM/fibrotic scarring” throughout the text was also modified to use a more precise description of “reduced Laminin deposition”, matching our Figure 2 quantification (line 109, 125, 296 and 844).

b. Tissue continuity and circuit continuity. The Abstract states that treatment results in "improved tissue continuity" (line 31), but I could not identify a direct quantitative assessment of tissue continuity or lesion bridging. Figure 2 instead shows increased NeuN and SMI-312 labeling and Brainbow-positive "axon-like" or "tract-like" structures that appear to extend across the lesion (lines 107-115). The Results then conclude that these findings provide "structural substrates for cross-lesion circuit continuity" (lines 116-118). These anatomical observations are interesting, but they do not directly demonstrate tissue continuity or functional circuit reconstruction. If tissue continuity is an important outcome, a quantitative measurement of lesion/bridge dimensions could potentially be performed using the existing histological material. The Brainbow findings should otherwise be described as evidence of anatomical fiber continuity across the lesion rather than circuit continuity, unless additional evidence of synaptic or functional connectivity is provided.

Response____：

We thank the reviewer for this valuable comment on our interpretation of anatomical tracing results. We agree our original wording overstated evidence for tissue and circuit continuity without direct synaptic or functional validation.

Although we performed trans synaptic AAV tracing and observed labeled neuronal cell bodies caudal to the lesion core, these observations alone are insufficient to firmly establish genuine circuit reconstruction. We have revised the manuscript to moderate our conclusions. We replaced the claim of “improved tissue continuity” from the Abstract with “improved fiber continuity across the lesion” (line 31). The conclusions drawn from Brainbow tracing are now described as “evidence of anatomical fiber continuity across the lesion”, instead of “cross lesion circuit continuity” (lines 117-118, 284, 286 and 780-781).

c. Ciliary structure versus ciliary function. The authors directly demonstrate preservation of ciliary morphology, including a greater proportion of ciliated ependymal cells, more continuous ciliary arrays, increased cilia-associated gene expression, and increased ciliation in RPE-1 cells (lines 198-214). However, they subsequently conclude that Noscapine "protects ciliary structure and function" and suggest that this preservation maintains CSF flow, environmental sensing, and lineage competence (lines 215-218). None of these physiological functions are directly measured. This distinction is particularly clear because the authors themselves state in the Discussion that measurements of ciliary beat coordination, CSF flow, and IFT dynamics will be required to link structural preservation to physiological function (lines 337-340). I therefore suggest consistently referring to preservation of ciliary structure or ciliation rather than ciliary function unless functional measurements are added.

Response____：

We thank the reviewer for this important distinction between ciliary structure and ciliary function. We agree that our original text drew inferential conclusions about ciliary related physiological functions without direct experimental measurements.

Following the reviewer’s suggestion, we have revised the manuscript to consistently refer to preservation of ciliary structure/ciliary integrity throughout the text and removed all claims regarding preserved ciliary function (lines 227-230, 245, 256-258, 274-275).

d. CSF-cN survival. The manuscript repeatedly describes Noscapine as enhancing or preserving CSF-cN survival. For example, lines 175-179 state that PKD2L1 immunostaining "verified that Noscapine enhanced the survival of CSF-cNs," and similar language is used for Paclitaxel and SANT-1 experiments (lines 224-225 and 246-249). However, the presented readout appears to be the abundance or proportion of PKD2L1-positive cells at individual time points rather than a direct assessment of cell survival or cell death. The increased abundance of PKD2L1-positive cells is consistent with enhanced preservation of CSF-cNs but does not directly demonstrate increased survival. This conclusion could be strengthened relatively straightforwardly by assessing cell death specifically within PKD2L1-positive CSF-cNs, for example using TUNEL and/or cleaved caspase-3 staining at an appropriate early post-injury time point. Alternatively, the authors should describe the result as increased preservation or abundance of PKD2L1-positive CSF-cNs rather than enhanced survival.

Response____：

We thank the reviewer for pointing out this critical distinction. We agree that our PKD2L1 positive cells quantification reflects cell abundance at fixed time points, rather than a direct measurement of cell survival or cell death.

Following the reviewer’s advice, we have revised the manuscript and replaced statements about enhanced CSF-cNs survival with increased abundance of CSF-cNs (lines 188-190, 236, 254, 258-260, 272, 288, 320, 339, 348-350, 356).

Major comment 3. The proposed ependymal-to-astrocyte differentiation is not directly demonstrated

A second important component of the proposed central canal repair mechanism is that Noscapine promotes differentiation of ependymal cells toward a reparative astrocytic state. This conclusion is mainly based on the decrease in ependymal cells and increase in astrocytes between 2 and 3 wpi, Monocle pseudotime trajectories connecting these populations, and the increased proportion of GFAP+Foxj1+ cells following Noscapine treatment (lines 149-165). While these observations are consistent with a relationship between ependymal and astrocytic states, they do not demonstrate a lineage transition. Pseudotime analysis orders transcriptionally related cell states but cannot establish the developmental origin of individual cells, and GFAP expression in Foxj1+ cells could alternatively reflect activation or phenotypic changes within ependymal cells rather than their differentiation into astrocytes. Nevertheless, the manuscript subsequently refers to "lineage progression," "lineage-associated transition," and the emergence of ependymal cell-associated astrocytes as a component of the proposed mechanism (lines 180-183, 241-246, 303-305 and 327-329). The authors appropriately acknowledge at lines 163-165 that formal demonstration of an ependymal-to-astrocyte transition would require lineage tracing, but the stronger lineage interpretation is retained elsewhere in the Results and Discussion.

The most direct way to address this point would be lineage tracing of Foxj1-expressing ependymal cells, for example using a temporally controlled Foxj1-CreER reporter activated before injury, followed by SCI +/- Noscapine and assessment of whether labeled progeny acquire astrocytic identity. This would provide a clear test of whether Noscapine truly increases ependymal-derived astrocyte formation and would likely require several months depending on mouse-line availability. If such an experiment is beyond the scope of revision, I do not think an entirely new lineage-tracing study should necessarily be required. Instead, the authors should consistently limit their interpretation to what is directly supported-for example, that Noscapine is associated with an increased GFAP+Foxj1+ population and with transcriptional states connecting ependymal and astrocytic populations-rather than presenting these observations as demonstrated ependymal-to-astrocyte differentiation. Additional computational approaches such as RNA velocity could provide supporting evidence for directional state transitions, but would still not substitute for lineage tracing.

Response____：

We thank the reviewer for this important clarification. We agree that pseudotime analysis and GFAP/Foxj1 co-expression do not establish ependymal-to-astrocyte differentiation, and that the observed changes could alternatively reflect activation or phenotypic remodeling of ependymal cells.

Following the reviewer’s suggestion, we will make every effort to perform lineage-tracing experiments using Foxj1-CreER mice crossed with an appropriate Cre-dependent reporter line. We plan to induce labeling before injury, followed by SCI with or without Noscapine treatment, and assess whether lineage-labeled cells acquire astrocytic identity using appropriate markers. This experiment will help determine whether Noscapine increases the formation of astrocytes derived from Foxj1-expressing ependymal cells.

Completion will depend on establishing and validating the tracing system. If reliable experimental results cannot be obtained, we will revise all lineage-related statements throughout the manuscript to only describe the increased GFAP-positive/Foxj1-positive cell population and the transcriptional association between ependymal and astrocytic cell states. The final conclusions will be revised in accordance with the experimental evidence. If the additional evidence is unavailable, inconclusive, or does not support these interpretations, we will qualify or remove the corresponding claims and restrict the conclusions to the observations directly supported by the data. We highlighted these statements that remain subject to revision in red in the manuscript.

Minor comment 1. Statistical analysis should be reconsidered for several experiments

The Methods state that two-tailed Student's t-tests were used for statistical comparisons (lines 544-551). This does not appear appropriate for several datasets, particularly the longitudinal BMS measurements, experiments containing more than two groups, and repeated measurements at 4 and 8 wpi. The authors should clarify the statistical test used for each comparison and account for repeated measurements and multiple comparisons where appropriate. The experimental unit should also be clearly defined. For example, in the RPE-1 cilia-length experiments, individual cilia should not necessarily be considered independent biological replicates when multiple cilia are measured from the same culture or experiment.

Response____：

We thank the reviewer for highlighting this issue. We agree that two-tailed Student’s t-tests are not appropriate for all experimental designs in this study. We will systematically review and revise the statistical methods throughout the manuscript and reanalyze the data where necessary.

For longitudinal BMS measurements, we will use an appropriate repeated-measures or mixed-effects approach that accounts for observations from the same animal over time. Comparisons involving more than two groups will use an appropriate overall test followed by comparisons with correction for multiple testing. For measurements at 4 and 8 weeks post injury, the analysis will distinguish repeated observations from the same animals from measurements obtained from independent cohorts.

We will also clarify the experimental unit and distinguish biological replicates from technical measurements for each analysis. For RPE1 cilia length experiments, we carried out three independent culture experiments. Individual cilia obtained from the same culture were not treated as independent biological replicates. The Methods and figure legends will specify the tests used, biological sample sizes, treatment of repeated measurements, and multiple-comparison corrections where applicable. Statistical annotations and the corresponding conclusions will be updated according to the reanalysis.

Minor comment 2. The biological replication and sample structure of the single-cell RNA-seq experiment should be described explicitly.

The manuscript states that 51,117 cells were retained across the conditions analyzed at 2 and 3 wpi, but it is unclear how many independent animals contributed to each condition, whether spinal cords were pooled before library preparation, and how many independent sequencing libraries were generated per group (lines 123-128). The authors should report the number of biological replicates per condition, the number of animals contributing to each replicate, and whether samples from different animals were processed independently or pooled.

Response____：

We thank the reviewer for this constructive comment regarding the reporting of our scRNA-seq experimental design. For each experimental condition, tissues were collected from 8-10 independent animals. Tissue samples were pooled prior to library construction, and only one independent sequencing library was generated per group. We have explicitly supplemented these details about animal numbers, sample pooling strategy and library information within the “Single cell suspension preparation” and “Single cell RNA sequencing” subsections of the Methods in lines 565-609.

Minor comment 3. Statistical inference from the single-cell dataset should account for biological replication.

*The manuscript reports substantial differences in cell composition, including a reduction of microglia from >60% of recovered cells in control samples to Response____：

We thank the reviewer for this important reminder about statistical considerations for scRNA-seq data.

Each sequencing library in our study was generated from pooled tissues of 8‑10 independent mice. While we consider each library representative of its corresponding experimental group, we acknowledge that only one library was available per condition, and our differential‑expression analyses lack independent library‑level biological replication.

Following the reviewer’s suggestion, we now present the differential-expression analysis for our scRNA-seq dataset as descriptive/exploratory findings, rather than formal statistical comparisons supported by biological replicates. We have updated the manuscript text in Results.

Minor comment 4. Several in vivo drug-treatment details required for reproducibility are missing.

The Methods state that mice received daily injections of saline, Noscapine, Paclitaxel or SANT-1 after crush injury, but the in vivo dose, vehicle and formulation are not clearly provided for all compounds. In addition, Y-27632 is not included in this treatment description despite being used in Figure 6 (lines 424-428). The dose, vehicle, injection route, treatment duration, and timing relative to injury should be explicitly reported for each pharmacological treatment.

Response____：

We appreciate the reviewer’s valuable comment regarding the completeness and reproducibility of our in vivo pharmacological treatment protocols. We have thoroughly revised and supplemented all drug administration details in the revised manuscript to fully address this concern.

First, we have removed the previous ambiguous description of drug injection for crush injury models. Furthermore, we have explicitly and comprehensively reported the complete treatment regimens for both the crush SCI model and the complete transection SCI model, including drug dosage, formulation, vehicle solvent, injection route, treatment duration, and post-injury intervention timing for all compounds. Notably, we have supplemented the detailed in vivo administration parameters of Y-27632, which was previously omitted in the text but applied in Figure 6. All revisions are presented in lines 460-476 of the manuscript text.

Minor comment 5. The administration strategy used in the initial microtubule-stabilizer screen should be clarified.

Figure 1C reports concentrations in µM and describes microtubule stabilizers in combination with the LOCS, whereas later Noscapine experiments use systemic treatment in mg/kg (lines 755-766). It should be made clear which compounds were locally delivered through the scaffold, which were systemically administered, and how the concentrations used for the different compounds were selected.

Response____：

We greatly appreciate the reviewer’s insightful suggestion to clarify the administration strategies applied in our microtubule stabilizer screening and subsequent functional validation experiments. We have now comprehensively supplemented the detailed drug delivery regimens and dosage selection rationale in the revised manuscript.

Specifically, we explicitly distinguished local scaffold-based delivery and systemic intraperitoneal administration for different compounds. In the initial microtubule stabilizer screening assay shown in Figure 1C, all candidate drugs were locally delivered via LOCS incubation at the indicated micromolar concentrations. The dose-ranging experiment of noscapine combined both local and systemic administration. Follow-up validation experiments used systemic intraperitoneal injection at mg/kg doses, with doses selected according to published in vivo therapeutic ranges. The detailed administration regimens were further supplemented in the Methods (lines 445-476).

Minor comment 6. The description of the EB1 experiment appears inconsistent between the Results and Methods.

The Results state that all five compounds reduced EB1-positive comet density "in vivo" (lines 88-90). However, the Methods describe treatment of HeLa cells with these compounds specifically to assess microtubule dynamics (lines 385-392). The authors should clarify whether the EB1 experiment was performed in vivo or in vitro and correct the corresponding text.

Response____：

We have corrected the misused term “in vivo” to “in vitro” in line 89 to align with our experimental setup described in Methods.

Minor comment 7. The title of Figure 6 overstates the experiment presented.

Figure 6 is entitled "Ciliary integrity is a key factor in regulating the functional recovery from SCI," yet the figure assesses ciliation, GFAP/Foxj1-positive cells, and PKD2L1-positive CSF-cNs and does not include a functional recovery measurement (lines 872-892). Unless functional data are added, the title should be revised to reflect the cellular phenotypes actually examined.

Response____：

Following the reviewer’s suggestion, we have revised the Figure 6 title to “Y‑27632 maintains ciliary structural integrity of central canal-associated cells”, which accurately reflects the cellular phenotypes examined in this figure.

Minor comment 8. Randomization, blinding, sample-size determination and exclusion criteria should be reported more completely.

The authors appropriately state that BMS scoring was performed by two observers blinded to experimental groups (lines 429-432). However, it is unclear whether animals were randomized to treatment groups, whether histological quantification was performed blinded, how sample sizes were determined, or whether any animals or samples were excluded from analysis. These details should be provided.

Response____：

We have supplemented the details of randomization, blinding, sample-size determination and exclusion criteria within the “Quantification and statistical analysis” subsection of the Methods (lines 596-609).

Minor comment 9. The exclusive use of young female mice should be acknowledged as a limitation.

All experiments were performed using 6-8-week-old female C57BL/6J mice (lines 350-354). This does not invalidate the findings, but given the translational framing of the manuscript, the authors should briefly acknowledge that possible sex- and age-dependent differences in treatment response were not evaluated.

Response____：

We thank the reviewer for raising this important consideration. All experiments in this study were conducted using 6-8 weeks old female C57BL/6J mice. We acknowledge that potential sex and age dependent differences in treatment response have not been evaluated in the current work. We have added this limitation in the “Animals” subsection of the Methods section.

Minor comment 10. Availability of processed single-cell data and analysis code would improve reproducibility.

The raw sequencing data are deposited, but several downstream analyses are described as being performed using "custom R scripts" (lines 534-543). Providing the processed Seurat object, cell annotations and relevant analysis scripts would make the single-cell results considerably easier to reproduce and independently evaluate.

Response____：

We thank the reviewer for this helpful suggestion. In the final fully revised submission, we will make available the processed Seurat object, cell annotations, and relevant analysis scripts, including the custom R scripts used for downstream analyses. We will also provide accompanying documentation and software version information to facilitate reproducibility and independent evaluation. The Data and Code Availability statement will be updated with the corresponding repository links and access details.

Reviewer 2

Major comment 1. The statistical analysis needs to be revised throughout the manuscript

This is my main concern, as it may affect many of the conclusions in the paper. The Methods state that two-tailed Student's t-tests were used, but many experiments have designs for which pairwise t-tests are not appropriate. Examples include the multi-group screen in Figure 1C, longitudinal BMS measurements, experiments with three or four groups, the factorial Noscapine × SANT-1 experiment, and measurements of multiple cells or cilia from the same biological replicate.

Figure 1C requires an omnibus test followed by corrected post-hoc comparisons. Repeated pairwise t-tests across so many groups increase the risk of false-positive results, particularly given the small and unequal sample sizes.

BMS measurements are longitudinal and should be analyzed using a repeated-measures or mixed-effects model that accounts for animal and time. Similarly, Figure 5 is a 2 × 2 design, and the claim that SANT-1 attenuates the effect of noscapine requires testing the Noscapine × SANT-1 interaction. Showing that one comparison is significant and another is not is not sufficient.

There is also a risk of pseudoreplication. For example, Figure 4 reports measurements from 100 individual cilia per treatment, but individual cilia from the same experiment are not independent biological replicates. The analysis should either use replicate-level values or account for the nested structure of the data.

For each experiment, the authors should also clearly report the biological n, technical/cellular replicates, randomization, blinding, exclusion criteria, statistical test and multiple-comparison correction.

I consider a full statistical reanalysis essential before the quantitative conclusions of the manuscript can be properly evaluated. Importantly, the conclusions throughout the manuscript should then be revised according to the outcome of this reanalysis.

Response____：

We thank the reviewer for this detailed assessment. We agree that the statistical analyses must reflect the experimental designs and that a full statistical reanalysis is necessary to evaluate the quantitative conclusions. We will use appropriate omnibus tests with multiplicity-adjusted comparisons for multi-group experiments and repeated-measures or mixed-effects models for longitudinal BMS data, distinguishing repeated observations from independent cohorts for measurements at 4 and 8 weeks. We will directly test the Noscapine × SANT-1 interaction in the factorial experiment.

For RPE1 cilia length experiments, we carried out three independent culture experiments. Individual cilia obtained from the same culture were not treated as independent biological replicates. All quantifications were performed blinded.

We will clearly report the biological sample sizes, experimental units, statistical tests, and multiple-comparison corrections for each analysis. Following reanalysis, we will update the figure annotations, statistical results, and corresponding interpretations throughout the manuscript, qualifying or removing any conclusions that are no longer supported.

Major comment 2. Appropriate vehicle and baseline controls are missing or unclear in several experiments

The control groups need to be clarified throughout the paper.

In Figures 1D-I, the relevant comparison for showing a noscapine effect is vehicle versus noscapine, rather than untreated control versus noscapine.

More importantly, several crush experiments appear to lack a vehicle-treated SCI group. For example, Figures 3H-I compare uninjured, crush SCI and crush + noscapine animals, but there is no crush + vehicle group. If noscapine is administered in a vehicle with possible biological effects, untreated SCI is not an adequate control. The vehicle group should be shown if it was performed.

Figures 4C-D would also benefit from an uninjured baseline. Crush versus crush + noscapine shows a treatment-associated difference in ciliation, but without baseline values it is difficult to conclude that noscapine preserves normal ciliation rather than simply increasing it after injury.

The paclitaxel experiment in Figure S8 is also unclear. The manuscript appears to use saline-treated animals as controls, but conventional paclitaxel is poorly soluble in saline. Since both paclitaxel and paclitaxel liposomes are listed in the Methods, the authors should clarify which formulation was used and what the corresponding vehicle control was.

More generally, formulation, vehicle, dose, route and treatment duration should be clearly reported for every drug.

Responses____：

• We thank the reviewer for this thorough evaluation of our control groups and drug administration details. We will revise the statistical analyses for Figures 1D-I, Figure 2 and Figure S1 following updated statistical approaches. As suggested, comparisons will be performed between the vehicle treated group and the noscapine treated group. For our crush SCI model, Noscapine and other compounds were delivered via intraperitoneal injection using saline as the solvent with no biologically active excipients. Our existing crush SCI group received intraperitoneal saline injection, which serves as the corresponding vehicle control for drug treated groups.

We will add an uninjured control group to Figures 4C–D, including representative Arl13b/Foxj1 staining and quantification of the proportion of Foxj1-positive cells bearing Arl13b-positive cilia.

• We thank the reviewer for this thorough evaluation of our control groups and drug administration details. In Figure S8, we used paclitaxel liposome for intraperitoneal injection, which is soluble in saline. The corresponding control group received intraperitoneal saline injection. Complete information regarding drug formulation, vehicle, dosage, administration route and treatment duration for all compounds has been supplemented within the “Spinal cord injury surgery” subsection of the Methods.

  Major comment 3.____ The current pharmacological experiments do not establish that cilia mediate the effects of noscapine

This is the main mechanistic issue in the manuscript.

Figure 5 is entitled "Ciliary integrity is required for the functional recovery mediated by Noscapine." However, SANT-1 is a Smoothened antagonist that blocks Hedgehog signaling; it is not a specific tool to remove or disrupt cilia. Hedgehog signaling can itself affect proliferation, differentiation, inflammation, survival and tissue repair. Therefore, the fact that SANT-1 reduces ciliation and attenuates some noscapine-associated effects does not show that these effects are caused by loss of cilia. It shows that the response to noscapine is sensitive to Smoothened/Hedgehog inhibition.

The Y-27632 experiment has the same problem in the opposite direction. Y-27632 is a ROCK inhibitor with well-established effects on axonal growth, astrocytes and scar formation after SCI. Therefore, the observation that Y-27632 increases ciliation and reproduces some noscapine-associated phenotypes does not demonstrate that increased ciliation is responsible for these effects. Both could simply be parallel effects of ROCK inhibition.

This also leaves open an alternative explanation for the overall findings: cilia may be better preserved because noscapine reduces tissue damage, rather than cilia preservation being the mechanism that drives repair.

For this reason, the current data support an association between ciliary preservation and improved outcome, but do not establish that cilia are necessary or sufficient for recovery. Statements such as "ciliary integrity is required," "critical structural dependency," "structural checkpoint" and "cilia-dependent regenerative niche" should therefore be toned down.

Interestingly, the authors themselves state in the Discussion that cell-specific genetic approaches such as Foxj1-CreER with Ift88/Kif3a would be needed to test ciliary necessity. I agree. If the authors wish to retain the strong causal conclusions, such an experiment would be required. Otherwise, the claims should be revised to reflect the current pharmacological evidence.

Figure 6 should also be retitled, as it refers to regulation of "functional recovery" even though no behavioral or electrophysiological endpoint is shown.

Response____：

We thank the reviewer for this careful assessment. We agree that the current pharmacological experiments do not establish that ciliary preservation is necessary or sufficient for Noscapine-mediated recovery.

To address this mechanistic question, we have already begun preparing Foxj1-CreER;Ift88 conditional knockout mice for subsequent validation experiments. We plan to use temporally controlled Ift88 deletion in Foxj1-expressing cells and assess whether Noscapine retains its beneficial effects following disruption of ciliogenesis. Several mechanistic claims in the preliminary revised manuscript await final coordinated validation through our planned supplementary experiments. These passages are highlighted in red in the main text to flag conclusions subject to revision.

We have revised the Figure 6 title to “Y‑27632 maintains ciliary structural integrity of central canal-associated cells”, which accurately reflects the cellular phenotypes examined in this figure.

Major comment 4. The data do not yet support a shared cilia-dependent mechanism across all microtubule-targeting compounds

Figure 1 screens noscapine, epothilone D, TPI-287, TTI-237 and paclitaxel, and the authors suggest that these drugs converge on a common downstream mechanism. However, the only common outcome examined across all compounds is locomotor performance. Scar formation, axonal growth and ciliation are not studied across the full panel.

The cilia experiments are mainly performed with noscapine and, to a lesser extent, paclitaxel. The data may therefore support a shared response between these two drugs, but they do not establish a "unifying" mechanism across all five compounds. It is also unclear why the other compounds are included in the initial screen if they are not followed up mechanistically.

The terminology should also be more precise. Paclitaxel and epothilones are classical microtubule stabilizers, whereas noscapine mainly suppresses microtubule dynamics and does not act in the same way. I suggest using "microtubule-modulating compounds" when referring to the drugs collectively.

Finally, the Results state that the compounds reduce EB1-positive comet density "in vivo," whereas the Methods describe this experiment in HeLa cells. This should be corrected. Reduced EB1 comet density also indicates reduced growing microtubule plus ends, but does not by itself prove equivalent microtubule stabilization by all compounds.

Responses____：

• We thank the reviewer for this constructive assessment. We agree that the current data do not establish a shared cilia-dependent mechanism across all five compounds. To extend the mechanistic comparison, we will first work to establish a suitable in vitro culture system using spinal cord ependymal or related cells. Once established, we plan to compare Noscapine, Paclitaxel, Epothilone D, TPI-287, and TTI-237 for their effects on ciliary structure and maintenance. This will test whether the ciliary responses observed with Noscapine and Paclitaxel extend across the broader compound panel.

In parallel, we have begun preparations for a Foxj1-CreER–based conditional Ift88 deletion mouse model. Following establishment and validation of this model, we plan to investigate all five compounds to determine whether disruption of ciliogenesis in Foxj1-expressing cells alters their effects on recovery. By comparing treatment responses in conditional knockout mice and appropriate littermate controls, we aim to test whether these compounds share a dependence on cilia in the targeted population.

The final conclusions will be revised in accordance with the experimental evidence. If the additional evidence is unavailable, inconclusive, or does not support these interpretations, we will qualify or remove the corresponding claims and restrict the conclusions to the observations directly supported by the data. We highlighted these statements that remain subject to revision in red in the manuscript.

• As the reviewer noted, these agents have distinct molecular actions: paclitaxel and epothilones are classic microtubule stabilizers, whereas noscapine primarily suppresses microtubule dynamics. To avoid misrepresentation, we have changed “Microtubule stabilizing agents” to “microtubule modulating compounds” at lines 25 and 49. The EB1 comet‑density assay was performed in HeLa cells. We have corrected “in vivo” to “in vitro” at line 89 to resolve inconsistency between Results and Methods. EB1 comet density marks growing microtubule plus‑ends and reflects microtubule growth and catastrophe cycles. Reduced EB1 comet density indicates suppressed microtubule dynamics, which we present as preliminary evidence of microtubule stabilization.

Major comment 5. Ciliary structure and ciliary function should be clearly separated

Figure 4 contains some of the most interesting data in the study, but the conclusions go beyond what was measured.

The authors show changes in cilium number, cilium length and ciliary markers, but they do not directly measure ciliary function. There are no measurements of ciliary beating, CSF flow, cilia-dependent signaling, mechanosensory responses or PKD2L1-dependent function in CSF-cNs.

Therefore, statements about preserved CSF flow, environmental sensing, lineage competence or "ciliary function" are speculative. The manuscript should refer to ciliary structure, architecture or integrity unless a functional readout is provided.

In Figure 4F, the authors also state that a greater proportion of CSF-cNs retain intact cilia after noscapine treatment, but I could not identify a corresponding quantitative analysis. This result should be quantified at the biological-replicate level.

The State 1/State 2 nomenclature also appears inconsistent between Figures 3 and 4 and should be clarified.

Response____：

• We thank the reviewer for these careful comments on the interpretation of ciliary observations and the state nomenclature in pseudotime analysis. We agree that our measurements of ciliary markers only assess ciliary structural features, and statements about preserved CSF flow, environmental sensing, lineage competence and ciliary function are speculative without direct functional assays. We have removed all claims related to ciliary function throughout the manuscript and revised the text to describe only the preservation of ciliary structure/ciliary integrity (lines 227, 245, 256-258, 274-275).

• We thank the reviewer for pointing out the lack of quantitative support for this statement. PKD2L1-positive CSF-cNs are very sparse in the sampled tissue, which has limited the number of cells available for analysis. In the forthcoming experiments, we will make every effort to obtain sufficient sampling across independent animals to quantify the proportion of PKD2L1-positive CSF-cNs bearing identifiable acetylated-tubulin-positive ciliary structures. The final conclusions will be revised in accordance with the experimental evidence. We highlighted these statements that remain subject to revision in red in the manuscript.

• For the State 1/State 2 nomenclature inconsistency between Figures 3 and 4: State 1 and State 2 represent cell states derived from pseudotime analysis, combined with cell-type annotation. Specifically, we defined the ependymal cells at state 1 as “State 1 Ependymal cells” and the astrocytes at state 2 as “State 2 Astrocytes”. We have supplemented this definition at lines 177 and 199 of the manuscript to eliminate ambiguity.

  Major comment 6. The severity of the crush injury needs clarification

The BMS scores in the crush experiments, particularly Figure 5E, appear unexpectedly low. The authors report BMS scores around 2 after complete transection, yet the crush animals show similarly poor recovery at four weeks despite a crush injury normally preserving considerably more spinal cord tissue.

This raises questions about injury severity and reproducibility across the different experiments. The authors should explain why recovery is so limited in the crush controls and provide evidence that the injury was comparable between experimental groups.

This is particularly important because most of the mechanistic experiments in Figures 3-6 rely on the crush model.

Response____：

We thank the reviewer for this important question regarding injury severity and the limited BMS recovery observed in our crush model.

The thoracic crush spinal cord injury was performed using ultra-fine tip forceps to achieve spinal cord transection. During injury induction, the forceps were closed to a gap of 0 mm to achieve complete compression of the spinal cord, yielding a lesion of approximately 0.5 mm in length. Unlike conventional contusion injury, this crush model severs the spinal cord parenchyma, while the injured tissue segment is kept in place without tissue removal. This explains the poor locomotor recovery in crush SCI animals, which resembles the outcome of complete transection. Representative histological evidence of the lesion core after crush injury is provided in Figure S6B. We have supplemented the detailed injury procedure and instrument information in the “Spinal cord injury surgery” subsection of the Methods to clarify this specific crush model (lines 434-439).

Minor comment 1.

The opening statement that "microtubule-stabilizing agents consistently improve functional recovery after SCI" is too strong. The literature is not completely consistent. I suggest "have been reported to improve functional recovery after SCI."

Response____：

We thank the reviewer for this suggestion to moderate the opening statement. We agree that the original claim overstated the consensus in the published literature, as previous studies on microtubule-targeting compounds for SCI are not universally consistent. We have revised the sentence at lines 25–27 to state that “microtubule-modulating compounds have been reported to improve functional recovery after spinal cord injury”, which better reflects the existing literature.

Minor comment 2 and 3.

The description of paclitaxel and epothilones as binding "the taxane pocket within the β-tubulin lumen" is inaccurate. A clearer formulation would be "the taxane-binding pocket on the luminal surface of β-tubulin."

I would therefore revise the full sentence to: "Compounds such as paclitaxel and epothilones, which bind to the taxane-binding pocket on the luminal surface of β-tubulin, have been shown to promote axon regeneration, reduce fibrotic scarring, and improve locomotor outcomes in preclinical models of SCI."

Response____：

We thank the reviewer for correcting the description of the binding site on β-tubulin. We agree that the original wording was imprecise. Following the reviewer’s recommendation, we have updated the sentence to: “Compounds such as paclitaxel and epothilones, which bind to the taxane-binding pocket on the luminal surface of β-tubulin, have been shown to promote axon regeneration, reduce fibrotic scarring, and improve locomotor outcomes in preclinical models of SCI.” (lines 50-52).

Minor comment 4.

The hindlimb range-of-motion analysis in Figure 1 is unusual and relies on manually selected video frames and manually drawn angles. The authors should state whether frame selection and measurements were performed blinded and how reproducibility of this measurement was assessed.

Response____：

We thank the reviewer for this careful comment on the hindlimb range‑of‑motion analysis. All video frame selection and angle measurements for hindlimb range of motion in Figure 1 were performed by researchers blinded to experimental group assignments.

Measurement reproducibility has not yet been formally assessed. To address this, we will have a second blinded observer independently repeat the frame selection and angle measurements for a subset of videos and evaluate agreement between observers. The assessment will include both steps to capture variability arising from manual frame selection as well as angle measurement. The procedure and results will be reported in the fully revised manuscript.

Minor comment 5.

Laminin-positive area alone should not be described as fibrotic scar. Laminin is also present in vascular basement membranes and other ECM structures. Either additional markers should be included or the result should be described as reduced laminin/ECM deposition.

Response____：

We agree that laminin staining alone cannot specifically define fibrotic scar, as laminin also exists in vascular basement membranes and other extracellular matrix structures. In accordance with the reviewer’s suggestion, we have revised the relevant text and replaced statements describing “ECM/fibrotic scarring” with “laminin deposition” at lines 109, 125, 296 and 844.

Minor comment 6.

Increased NeuN-positive cells should be described as increased neuronal presence or survival unless neuronal replacement/neurogenesis is directly demonstrated.

Response____：

We thank the reviewer for this valuable suggestion to refine our description of NeuN-positive cells. We agree that greater NeuN-positive signal alone cannot confirm neuronal replacement or de novo neurogenesis. Following the reviewer’s recommendation, we have revised the corresponding text in the manuscript to describe this finding as “increased neuronal presence” at lines 110-112.

Minor comment 7.

Similarly, an increased proportion of PKD2L1-positive cells does not necessarily demonstrate increased CSF-cN survival. Absolute numbers or densities would provide stronger evidence.

Response____：

We thank the reviewer for this thoughtful comment on the interpretation of PKD2L1-positive cell proportion. We agree that a change in the proportion of PKD2L1-positive cells cannot directly prove improved survival of CSF-cNs. We have revised the manuscript and replaced statements claiming enhanced CSF-cNs survival with descriptions of increased CSF-cNs abundance at lines 188-190, 236, 254, 258-260, 272, 288, 320, 339, 348-350, 356.

Minor comment 8.

The rationale for selecting noscapine for the mechanistic part of the study could be explained more clearly. If CNS accessibility and safety are important reasons, these points should be appropriately referenced and related to the dose used here.

Response____：

We thank the reviewer for suggesting we clarify the rationale for selecting noscapine for mechanistic studies, and we have added this information together with references 13 and 20-22 in the manuscript at lines 94-98.

Minor comment 9.

The use of "chronic phase" for tissue collected three weeks after SCI should be reconsidered or justified.

Response____：

We thank the reviewer for pointing out the ambiguous use of “chronic phase” for tissue harvested at 3 weeks post‑SCI. According to references 1 and 26, secondary injury is categorized into acute (6 months) phases, with distinct pathological characteristics for each stage. The 3-week post-injury time point belongs to the intermediate phase, so we replaced the original “chronic phase” wording throughout the manuscript (lines 131-134, 171 and 823).

Minor comment 10.

The manuscript would benefit from careful editing of the causal language. In several places, association, structural preservation and causal mechanism are presented almost interchangeably. Keeping these concepts separate would make the conclusions clearer and better supported.

Response____：

We thank the reviewer for this suggestion. We will carefully revise the language and conclusions throughout the manuscript in light of the new experimental results, ensuring that all claims remain proportionate to the supporting evidence.

Several mechanistic claims in the preliminary revised manuscript await final coordinated validation through our planned supplementary experiments. These passages are highlighted in red in the main text to flag conclusions subject to revision. Should follow-up data be unavailable, inconclusive, or inconsistent with these interpretations, we will qualify or delete these statements and limit our conclusions to data-supported observations only.

Reviewer 3

Major comment 1.

One of the key conclusions is the CSF-cNs are preserved. Such as is stated: "At 4 weeks after complete transection SCI, CSF-cNs were detected in the noscapine group (Figure S7C), indicating that CSF-cNs may serve as a key responsive neuronal subtype contributing to functional recovery following treatment with Noscapine. We further performed immunostaining for PKD2L1 at 1 week post crush SCI, and the statistical results verified that Noscapine enhanced the survival of CSF-cNs (Figures S7D and S7E)." However, you state that for complete transection, spinal tissue is removed and replaced with a loaded biomaterial; are you referring to neurons adjacent to the lesion site? This should be quite clear. I do believe that the crush model is different, but for the transection, this is hard to understand and also relates to the RNA-seq as well (mentioned below). It could still be preservation from secondary damage, but this should be stated.

Response____：

We thank the reviewer for this thorough and insightful comment regarding the interpretation of CSF cNs signals in the complete transection SCI model. We appreciate the opportunity to clarify the anatomical location of these PKD2L1-positive cells and the biological interpretation of this result.

In Figure S7C, the CSF-cNs detected at 4 weeks post complete transection SCI in the Noscapine-treated group are located within the lesion core. All corresponding immunostaining images were acquired from tissue sections sampled at the lesion core (Figure 5, 6, S7, S8). Although a segment of spinal tissue was removed and substituted with biomaterial in this transection model, residual endogenous cells including CSF-cNs can persist within the lesion core region.

We have supplemented these clarifying statements in the manuscript at lines 185-188 to avoid confusion between the complete transection and crush injury models.

Major comment 2.

In Figure 2E, it is unclear where these pics are taken from; it seems to be adjacent to the biomaterial, as it is unlikely to be in the lesion core where the spinal tissue was removed. Please clarify, as this is quite an important point for this and other statements made.

Response____：

We thank the reviewer for this careful comment regarding the sampling location of images shown in Figure 2E. We apologize that our original description was ambiguous and caused confusion. The tissue sections used for Figure 2E were collected from the lesion core, corresponding to the region marked by the red dashed box in the schematic diagram in Figure 2B. Although part of the spinal tissue was resected and replaced with biomaterial in the complete transection model, this defined lesion-core region still contains residual cells that we assessed by immunostaining. We have clarified this sampling location at lines 110-112 in the manuscript text and figure legend to eliminate ambiguity.

Major comment 3.

In Figure 5, there is a great deal of supportive data, including cilia integrity with functional recovery after crush SCI, especially with the SANT-1 work. Why was axonal regeneration not examined in this SCI model as was done in Figure 2? Is this due to the sectioning of the cords coronally? This should be mentioned in the methods. It should still be possible to see if cilia integrity relates to axonal regeneration and functional recovery, or if it is due to something else. Correlative analysis between the different components or PCA would be helpful here. Additionally, were laminin levels examined here? It would be nice with the SANT-1 work to see if this has an effect on the fibroglial scar.

Response____：

We thank the reviewer for this thoughtful comment and valuable suggestions. We agree that examining axonal regeneration, laminin deposition and fibroglial scar formation in the crush SCI model of Figure 5, together with correlative analyses across multiple readouts, would deepen our mechanistic understanding.

As suggested by other reviewers, to more directly clarify whether ciliary integrity in Foxj1-positive cells is required for Noscapine-mediated functional recovery, we are preparing Foxj1-CreER;Ift88 conditional knockout mice. This genetic strategy enables temporally controlled, cell-specific disruption of ciliogenesis in Foxj1-expressing cells, overcoming the limitation of SANT‑1, which inhibits Smoothened/Hedgehog signaling rather than specifically ablating cilia. After verifying successful disruption of ciliogenesis in the target cell population, we will test Noscapine’s reparative effects in these conditional knockout mice and matched littermate controls using the crush SCI model. These genetic experiments will provide more direct evidence to evaluate the causal contribution of cilia to the repair response. The final conclusions will be revised in accordance with the experimental evidence. We highlighted these statements that remain subject to revision in red in the manuscript.

Major comment 4.

In Figure 6 was BMS not performed? It would be useful to compare to Figure 5 as all the other parameters are quite similar.

Response____：

We greatly appreciate the reviewer’s valuable suggestions. In follow-up experiments, we will perform relevant motor function assessments using the Foxj1-CreER;Ift88 conditional knockout mouse model. The final conclusions will be revised in accordance with the experimental evidence. We highlighted these statements that remain subject to revision in red in the manuscript.

We fully recognize that the absence of functional recovery data limits the conclusions we can draw for this figure. Accordingly, we have revised the Figure 6 title to “Y‑27632 maintains ciliary structural integrity of central canal-associated cells”.

Minor comment 1.

The linear-ordered collagen scaffold (LOCS) was used to span the distance of the removed tissue following the spinal transection. The authors should be clearer about whether 1 mm or 2 mm was removed. In the given span of axonal growth and cell infiltration into this area, it is necessary to know the size and what would be possible in a 4-week timeframe. Further, please provide a picture of the LOCS, as the panels in Figure 2 appear to show channel structure, and knowing its origin is important for understanding the work.

Response____：

We thank the reviewer for this thoughtful and important inquiry regarding the length of resected spinal tissue and the physical characteristics of the LOCS scaffold. This information is indeed critical to interpret the extent of axonal growth and cellular infiltration within the lesion gap over the 4-week experimental window.

The implanted LOCS scaffold, visible in the lower panel of Figure 1A at the injury site, has a length of approximately 1.5 mm, corresponding to the 1.5 mm segment of spinal cord tissue that was resected. The LOCS possesses a channeled structure and remains incompletely degraded at 4 weeks post-injury, which explains why these structures can be observed in the fluorescent images in Figure 2. We have supplemented these details about the resection length, scaffold features and degradation profile in the manuscript for clarity (lines 112-115 and 432).

Minor comment 2.

I am a bit unclear about the use of the Brainbow mice, is this mono- or trans-synaptic tracing? Are the different color specific for different tracts or the primary vs the secondary neuron or completely unspecific?

Response____：

We thank the reviewer for this thoughtful question regarding the Brainbow mouse strategy used in our study.

The Brainbow system labels individual neurons such that each neuron is assigned a distinct color; these colors do not distinguish neuronal subtypes, tracts, or primary versus secondary neurons. Importantly, the Brainbow mouse itself lacks trans synaptic activity. In addition, fluorescent protein expression in the Brainbow system requires Cre recombinase for activation. As shown in Figure 2I and S2, we delivered AAV-hSyn-cre to drive Brainbow fluorescent protein expression, and the trans synaptic property originates from the AAV serotype we employed, rather than the Brainbow mouse strain. We have supplemented these relevant descriptions in the manuscript at lines 116–120.

Minor comment 3.

It is stated that for the whole-cell single-cell RNA sequencing (scRNA-seq), the lesion core is taken, but in these experiments there is a biomaterial in the lesion core, so please state how much material and from exactly where it was taken. It seems unlikely this was only where the biomaterial was placed but also included surrounding tissue involved in secondary damage.

Response____：

We thank the reviewer for this careful and important question regarding the tissue harvesting strategy for our whole-cell single-cell RNA sequencing (scRNA-seq). For scRNA-seq, tissue samples were harvested from the lesion core region containing the implanted LOCS scaffold. The harvested spinal tissue was symmetrically dissected centred on the lesion core, with a total length of approximately 1.5–2 mm. We acknowledge that the harvested samples inevitably contained the adjacent surrounding regions undergoing secondary injury responses. We have added these precise sampling details in the manuscript to clearly define the anatomical region and sampling procedure (lines 547-549).

Minor comment 4.

On page 8 it is written, "intraflagellar transport (Ift122, Ift46)" and later IFT is used in the discussion, but it would be helpful to define it again, as it was hard to remember what this stood for from this reference on page 8.

Response____：

We thank the reviewer for this helpful suggestion regarding the definition of IFT. We agree that redefining the abbreviation in the Discussion will improve readability, since the first mention of intraflagellar transport (Ift122, Ift46) appears earlier on page 9. We have added the full term “IFT (intraflagellar transport)” at its first occurrence within the Discussion section at line 331 to remind readers of this abbreviation.

Minor comment 5.

It is stated that Paclitaxel is injected intraperitoneally; however, it isn't known to cross the BBB, so how was this possible? Please add more details to the methods.

Response____：

We thank the reviewer for this important question regarding the intraperitoneal administration of paclitaxel and its delivery across the blood spinal cord barrier (BSCB). In our study, we used paclitaxel liposome for intraperitoneal injection. While free paclitaxel exhibits limited penetration across the intact blood-spinal cord barrier (BSCB), liposomal formulation improves its tissue delivery profile. Furthermore, spinal cord injury causes substantial disruption of the BSCB at the lesion site, which facilitates extravasation of paclitaxel liposome into the injured spinal parenchyma. We have supplemented these details, including the formulation information and dosing regimen, within the Methods (lines 445-476).

Minor comment 6.

For the thoracic crush SCI, the type of forceps should be mentioned in the methods, as the width will determine the severity and lesion length.

Response____：

We thank the reviewer for this valuable suggestion regarding our thoracic crush spinal cord injury model. The crush injury was performed using ultra-fine tip forceps (Easybio, BE6129; minimal tip width: 0.1 mm). During injury induction, the forceps were closed to a gap of 0 mm to achieve complete compression of the spinal cord, yielding a lesion of approximately 0.5 mm in length. We have added these forceps specifications and injury parameters to the Methods section (lines 433--438).

Minor comment 7.

In Figure 1C to 1D, could you present the data in molarity or concentration (1mM vs 100mg/kg) so it is easier to compare from one panel to the next.

Response____：

We thank the reviewer for this helpful suggestion regarding the units presented in Figure 1C and 1D. We apologize that our original description did not explicitly distinguish the two drug delivery strategies, which caused confusion.

The different units originate from our distinct treatment designs. In Figure 1C, the drug was loaded onto LOCS, so experimental groups were labelled by drug concentration (μM/mM). In Figure 1D, the drug was administered via intraperitoneal injection, with doses reported as body weight based dosage (mg/kg). Given these fundamentally different delivery modes, it is not appropriate to unify them under a single type of unit. To help readers readily interpret this difference, we have added this rationale in the figure legend (lines 819-828).

Minor comment 8.

It is unclear how the number of animals were picked for each experiment, sometimes there are more and sometimes only 3 per group. Was a power analysis performed to determine this? It seems a bit underpowered.

Response____：

We thank the reviewer for this important comment regarding sample size selection across our experiments. We acknowledge the reviewer’s concern that some groups have only n=3 animals, which may appear underpowered.

Sample sizes in our study were selected based on our prior experience with this spinal transection/crush injury model and the expected variability of each assay. For histological measurements, we used at least n=3 per group; for behavioral BMS assessments, we increased the sample size to reduce variability. A formal power analysis was not performed before starting these in vivo experiments, which is a limitation of our work. We have noted this limitation explicitly in the methods at lines 604-609. We have labelled the number of animals (n value) for every experiment within the corresponding figure legends, and we have taken care not to overinterpret our findings.

Minor comment 9.

In Figure 2C, the boxes of the laminin staining are sometimes closer to the edge of the biomaterial and sometimes central; this could have an effect on the analysis. Was there a method for where this box was placed?

Response____：

We thank the reviewer for this careful observation regarding the selection of regions of interest (ROIs) for laminin staining analysis in Figure 2C. The ROIs in Figure 2C simply mark representative regions selected for magnification and visualization, and these boxes **do not define the regions used for quantitative analysis. For the quantitative measurement of laminin-positive area fraction shown in Figure 2D, we analyzed the entire lesion core region. Therefore, the quantification results were not affected by the position of these dashed boxes. We have added this clarification in the figure legend to avoid misinterpretation by readers (809-811).

Minor comment 10.

In Figure 2G, it is unclear where these pics are taken from; are they from the center of the biomaterial or from the edges? The axons don't look linear as the LOCS looked earlier in the figure. Does the LOCS degrade? When? This is important to understand the work shown here.

Response____：

We thank the reviewer for this important question regarding the images shown in Figure 2G. The tissue imaged in Figure 2G was harvested from the center of the biomaterial, corresponding to the area marked by the red dashed box in the schematic diagram (Figure 2B). The implanted LOCS undergoes degradation after injury. However, within our maximum 4-week observation window, the LOCS does not degrade completely. This explains some linearly arranged structures observed in our tissue samples. We have clarified these descriptions at lines 110-115 in the manuscript text to help readers interpret the axonal morphology and tissue architecture.

Minor comment 11.

Is it possible that the Paclitaxel Figure 2J picture on top right is turned upside down? The reason I ask is that the EGFP staining is so strong in what is the caudal region of a full transection, and this seems quite odd 4 weeks after SCI and doesn't really relate to the lesion core, which is where these axons must be coming through to end up on the caudal side.

Response____：

We thank the reviewer for this critical observation regarding the upper-right image in Figure 2J. We apologize for insufficient anatomical orientation description in our original manuscript, which caused confusion.

We have carefully rechecked the original image files of the Paclitaxel group and confirmed that this micrograph was not flipped or rotated upside down. Under our anterograde trans-synaptic tracing strategy, the intense EGFP signal indicates greater axonal transmission across the lesion site. This finding is consistent with previous literature demonstrating that paclitaxel and LOCS treatment effectively promote spinal cord injury recovery. Meanwhile, the paclitaxel group also displayed more nerve fiber signals within the lesion core compared with other treatment groups. We have added a clear explanation of the rostrocaudal orientation in the figure legend to help with understanding (lines 860-862).

Minor comment 12.

In this same Figure 2J, the caudal pics are the neurons that are shown here stained with something, or is this from trans-synaptic staining? Are they lower motoneurons?

Response____：

We appreciate the reviewer’s question about the identity of caudal signals and labelled cells in Figure 2J. No additional markers were used in this panel. Only three fluorescent proteins were detected. Importantly, this tracing strategy cannot distinguish neuronal subtypes. We have supplemented descriptions of the labelling strategy and characteristics of the Brainbow system at lines 116-120 of the manuscript.

Minor comment 13.

I really appreciate the clear marking of the timepoints and timelines in the figures. For Figure 3, the RNA-seq is from the full transection at 2 or 3 weeks. Why were these timepoints chosen? The following immunohistochemistry in the figure is crush SCI at 1 wpi, and while it is a less severe injury, it is unclear to me why this timepoint was chosen for this staining work. Please clarify.

Response____：

We thank the reviewer for this valuable question regarding the selection of time points for scRNA-seq and immunohistochemistry experiments in Figure 3.

For the scRNA-seq experiment, samples from the complete transection SCI model were collected at 2 weeks post-injury to represent the subacute phase and at 3 weeks post-injury as an intermediate phase. These two time points capture the transitional state of cellular responses following spinal cord injury.

For immunohistochemical analysis, we selected the 1-week time point after crush SCI in Figure 3H. This choice was based on the dynamic properties of ependymal cells; at 1 wpi, active cellular dynamics of ependymal cells can be clearly visualized at the histological level. We have clarified the rationale for the selection of injury models and time points in the manuscript (lines 134-135 and 168-170).

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Reply to the reviewers

General Statements

We want to thank the Reviewers for both their positive comments and their constructive criticisms.

We are happy that Reviewer #1 found that “The manuscript examines very interesting topics - the molecular mechanism of action of Sephin1 as a potential therapeutic, its impact on autophagy, and a potential direct effect on the actin cytoskeleton” and that - “ *The authors performed numerous diverse experiments. “. *

Similarly, Reviewer #2 recognizes that “The study presents a large body of data and attempts to connect several major cellular pathways, including actin dynamics, Golgi organization, the integrated stress response, and mTORC1-TFEB signaling. “ and that “The topic is important and timely, particularly given the ongoing debate regarding the specificity and mode of action of sephin1 and related compounds.”

Indeed, they identified several flaws that we are more than willing to address along our revision.

Considering the additional experiments already performed plus the ones planned for the near future, we are confident that our manuscript will gain more support.

Description of the planned revisions

Reviewer #2

*Q: The data supporting a direct interaction between sephin1 and actin are not quantitatively documented, and the potential involvement of known actin-associated complexes, including PPP1R15 proteins and PP1c, is not addressed. *

A: Our department has recently acquired the WAVE system (Creoptix), an advanced technological platform allowing the determination of the affinity between a small molecule and its target. Thanks to such technology, we will test sephin1-actin affinity as requested.

Q: The analysis of Golgi organization is also limited. The use of GFP-based markers rather than established Golgi markers such as GM130 reduces confidence in the interpretation of Golgi morphology.

A: We will perform the experiment suggested : we will assess Golgi morphology upon sephin1 treatment by using Golgi markers. In the meantime, we invite the Reviewer to take in consideration our EM analysis. We showed the regular occurrence of massive Golgi alterations at the ultrastructural level by using samples quick frozen within milliseconds, thus, free of fixation artifacts. Formal quantification will be provided as a complement.

*Q: The evidence supporting modulation of mTORC1 signaling is not fully convincing. The quality of the 4EBP1 immunoblots is insufficient for reliable interpretation, and appropriate controls using established mTOR inhibitors such as rapamycin or Torin1 are missing. *

Additional readouts, including phosphorylation of S6, should be included.

A: We will complement our biochemical analyses as requested by the reviewer.

In the meantime, we have specifically verified that sephin1 increases lysosomal activity via TFEB by assessing DQ-BSA signals in the TFEB KO HeLa line described in (XX). The cells were previously incubated overnight with 10 μg/mL of DQTM Red BSA added in normal medium. Then we treated HeLa cells with sephin1 (100 μM, 2 hours). After the wash-out ( 8 hours) we processed the cells for imaging. In TFEB KO cells, sephin1 did not increase DQ-BSA signals, a proxy for lysosomal activity. These data further support our hypothesis that sephin1 triggers lysosomal activity via the mTOR-TFEB pathway. These results are included in the new Supplementary figure 12F-G and reported also here for Reviewer’s convenience (Rebuttal figure 6A-B).

Q: It remains unclear which events are primary and which are secondary consequences of cellular stress or cell death, in particular TFEB translocation, which should be shown with the endogenous protein.

A: We are more than willing to test TFEB translocation upon sephin1 treatment by staining the endogenous protein

Q: In addition, the study does not address the functional consequences of these pathways, such as the clearance of protein aggregates, which would be important to demonstrate, since it is the proposed model for the clinical application in which sephin 1 is tested as a therapeutic agent.

A: We will include new data from EM morphometry on human fibroblasts carrying the LRRK2 E193K mutation which provide strong indication for the therapeutic effect of sephin1. We have recently thoroughly characterized the autophagic impairment in this genotype. Among others, we observed the massive accumulation of any kind of autophagic and catabolic organelles in E193K cells under normal, steady state conditions [1]. In the present study, we treated E193K fibroblasts (and age-matched wild-type controls) with sephin1 (100 μM, 2 hours) and after 6 hours wash-out we documented ultrastructural patterns, including autophagy by EM. Sephin1 acute treatment induced subcellular alterations as documented in HeLa. Upon a 6 hours wash-out, we noticed also in those fibroblasts the disappearance of any waste-loaded, jammed catabolic organelles. Representative images are already included in the revised manuscript and (New supplementary figure 15A) and in this rebuttal (Rebuttal figure 11C), quantification is planned as well.

Description of the revisions that have already been incorporated in the transferred manuscript

REVIEWER # 1

Q: 1. The cellular LC3 analyses are fraught with inconsistencies.

--Fig.1 shows that in response to Sephin1, LC3-I and LC3-II levels are similar; Fig.2 shows that LC3-I is more abundant than LC3-II; Fig.3 shows that LC3-II is way more abundant than LC3-I. This dramatic variability and inconsistencies make it impossible to draw solid conclusions about the effect of Sephin1 on LC3 lipidation or autophagy.

A: We are sorry for this inconvenience. However, it is well known that LC3 detection by western blotting is problematic due to the inherent susceptibility of microtubule-associated protein 1 light chain 3 to degradation and structural instability. LC3-I, for instance, may be detected with lower efficiency by some anti-LC3 antibodies and is intrinsically less stable than LC3-II (see for example Rebuttal Figure 10A). Accordingly, the guidelines report that LC3B-II levels, and not LC3B-I, correlated with elevated levels of autophagic vesicles monitored either by electron microscopy or rat GFP-LC3 transfection in response to autophagy-inducing stress, Furthermore, a key recommendation is that LC3-II levels should be normalized to a housekeeping protein such as actin or tubulin rather than to LC3-I [2, 3]. In all our experiments we included the proper internal control and we mainly relied on LC3B-II/tubulin values to draw our conclusions. Altogether, we are confident that our data support our hypothesis.

Q: In Fig.S1B, the LC3B blot has 8 lanes but the tubulin loading control shows 11 lanes. This also does not make sense.

A: We are sorry for that. It was merely a clerical error that occurred during the pictures handling. We replaced it with the right picture.

Q: LC3B is shown above and below a "23kDa" marker. But LC3-I should appear just above a 15kDa marker and LC3-II just below a 15kDa marker. In Fig.1A (and really, all the figures), LC3 species should not be >20kDa. Is the placement of the MW markers incorrect?

A: Indeed, the reviewer is right. We indicate now the proper marker ( 15 kDa)

Q: Why do Figs.S1E-F not show any actual data points? What are the bases of these curves? LC3-I and -II values are again all over the place in multiple supplemental data panels.

A: Supplementary figures 1E-F show the D/R curve describing sephin1 effect. The Y axis shows LC3-II/tubulin and LC3II/I levels, respectively, while the X axis reports sephin1 concentration, expressed as Log. We fitted the experimental data to the logarithmic variation of the Hill equation. New figures report now also the actual data points.

1. • The actin biochemistry assays involving Sephin1 are also problematic. --First, what does actin "precipitation" mean? Is actin misfolding and/or aggregating and therefore pelleting upon centrifugation? Or is it polymerizing and/or bundling and therefore pelleting upon centrifugation? Or (depending on the experiment) is it binding to beads that pellet upon centrifugation? This is all unclear.*

A: We experienced that actin does not remain soluble in the buffer even at 1g room temperature when exposed to sephin1, at least in vitro. “Protein precipitation” is a common laboratory term referring to any strategy to separate proteins from a liquid sample. Generally, it works by making proteins insoluble so they clump together and sink to the bottom of a test tube. Given our experimental setting, we do think that precipitation is an acceptable term to describe the phenomenon.

Coming to the other points raised by the Reviewer, we did try to characterize the nature of the actin found in the pellet by crystallography but we failed. Therefore we moved to a low resolution biochemical strategy , namely the limited proteolysis approach. Limited proteolysis is a technique where low amounts of proteases cleave only exposed and flexible peptide bonds in a native protein, leaving the core structure intact. It maps higher-order protein conformation, domain boundaries, and conformational changes upon ligand binding.

More in detail, 850 ng of human platelet non-muscle actin (Cytoskeleton Inc., APHL99-C) was incubated overnight with 350μM sephin1 or DMSO in the following actin buffer [5 mM Tris-HCl pH 8.0, 0.2 mM CaCl2, 0.2 mM ATP, 5% (w/v) sucrose, and 1% (w/v) dextran] in presence of Triton-X100 (0.01%). The following day the samples were preheated at 25°C for 10 minutes and then proteinase K (Bio Basic) was simultaneously applied to samples (enzyme: substrate at 1:100 mass ratio) that were subjected to a further incubation at 25°C for 5 minutes. Proteinase K activity was quenched by heating samples at 98°C for 5 minutes. After the addition of 5% sodium deoxycholate (Sigma Aldrich), samples were incubated at 98°C for 3 minutes and reduced by using 12 mM DTT at 37°C for 30 minutes. An alkylation step was performed using 40 mM IAA for 30 minutes in the dark. Next, proteins were digested with 0.5μg Lys-C (Wako Chemicals) at 37 °C for 4 hours. Subsequently, samples were diluted with 100 mM ammonium bicarbonate to obtain a final 1% concentration of sodium deoxycholate, then digested with 1μg of Trypsin (Thermo Scientific) at 37 °C overnight. The following addition of 1.5% formic acid and centrifugation at 16 000 rcf for 10 minutes provoked sodium deoxycholate precipitation. Digests were desalted on in-house–packed StageTips, lyophilized in a Speed-vac and resuspended in 20 μL of 0.1% formic acid for LC-MS/MS analysis. Peak intensities of peptides were transformed into log2 space and data were normalized by the average of peak abundance within each sample [4]. Log2 normalized intensities of single peptides were averaged through the replicates. By subtracting the averaged values of Actin- DMSO samples to Actin-sephin1 samples, the fold-change was calculated for each peptide. Significant abundance differences between conditions were determined using a t-test (two-tailed, two-sample unequal variance). Our low-resolution structural analysis suggests that sephin1 reduces the solvent accessibility of two peptides located in subdomain 1 and 3, respectively . The mapped binding site is relatively far from these peptides, indicating that this outcome may be due to a different structural organization of that region, rather than steric hindrance. In particular, our data nominated the peptide 7-18, encompassing the phosphate binding loop 1 and an hydrophobic sequence ( aa 297-312) in the subdomain 3. The P1 loop (amino acids 11–16) is a flexible segment that binds ATP. The hydrophobic loop in subdomain 3 and 4 is crucial for the stabilization of G-actin and supports the monomer addition in the growing actin filament. Existing literature does not suggest that the P1 loop may engage subdomain 3 in either lateral or longitudinal interactions [5]. As such, sephin1 may affect G-actin folding and trigger the formation of yet to be described supramolecular actin complexes involving P1 loop-subdomain 3 interaction. Our data suggest that such structures encompass at least 3 G-actin monomers, as they are recognised by phalloidin, and interact with Arp2/3. Furthermore, in vitro, such actin structures precipitate already at 16K g, while F-actin is classically sedimented at 100K g, suggesting the peculiar nature of the actin assembly induced by sephin1. We are still figuring out how to gain a more detailed understanding of actin folding upon sephin1 binding. We included in this rebuttal the data gathered so far (Rebuttal figure 10B-C).

Q: It is also unclear how the experiments in Fig.4 were performed, because the legend for Fig.4 is uninformative, and the methods sections for the actin experiments were fairly thin. Data-wise, the pulldown blots in Fig.4A and Fig.4F are inconsistent with one another. Is Sephin1 pulldown of actin dose-dependent or not? Where are the actual data points in Fig.4G? Is the dose of Sephin1 used in Fig.4H higher than that in Fig.4F?

A: We did our best to improve the description of the experiments and the relative figure legends.

Figure 4A shows a representative blot of an in vitro pull-down experiment. Briefly, we gathered protein samples from HeLa cells, exposed that to either naive sephin1 or biotinylated sephin1 (FG08) and then we immobilized biotinylated sephin1 and the potential interacting proteins on streptavidin agarose beads. Eventually, we resolved the interacting protein by SDS-PAGE. Figure 4F reports a completely different experiment, i.e. actin precipitation ( see the answer above) upon sephin1 exposure. Probably the reviewer meant Figure 4C. That is indeed a pull-down, but here we incubated either purified β- or ∝- actin with biotinylated sephin1. We now included the data point in figure 4G and we reported that actual concentration of sephin1 used for the experiment in Figure 4H (150 uM).

Q: CytoD binds to the + ends of actin filaments to prevent elongation and eventually promote depolymerization - what is the explanation for how this decreases the "precipitation" of actin in the presence of Sephin1 in Fig.4H-I?

A: Cytochalasin-D binds both G- and F-actin, albeit with largely different affinity (Kd F-actin: 2 nM; Kd G-actin 20 μM). Our molecular dynamics analysis suggests that the predicted sephin1 binding pocket on actin overlaps with binding sites reported for other actin ligands, including cytochalasin D (supplementary figure 5E), suggesting potential competition between cytochalasin D and sephin1 for β-actin binding 51–53. Consistent with this hypothesis, when we tested actin biochemical behavior in vitro by means of our precipitation assay, cytochalasin D significantly reduced β-actin precipitation induced by sephin1. We modified the relative result section to better convey our working hypothesis.

Q: The differences in actin "pulldown" by Sephin1-coated beads in Fig.S3D could possibly be explained by differences in input, and do not appear to be significantly outcompeted by soluble Sephin1.

A: The graph in Figure S3E reports the yield of actin recovery by pulldown expressed as bound /input. Therefore, any potential difference in the input level would not affect the final data.

Q: The amount of alpha-actin pulled down by Sephin1 appears to be proportional to the amount of albumin pulled down by the same beads in Fig.S4, showing that the proposed interaction of actin with Sephin1 is not specific. The complete absence of actin in lane 10 of Fig.S4 is difficult to reconcile with the amount in the pellets in lanes 4-5.

A: Figure S4 does not report the results of a pull-down experiment. Instead, it includes representative blots of sedimentation assays for ∝ actin and albumin. As such, we cannot comment further about the point raised by the Reviewer

Q: Fig.S6C/E appear to show pyrene-actin polymerization assays, but what do the different colored curves represent? What were the concentrations of Sephin1? Do the curves reach similar or different steady state levels of fluorescence? Does steady state occur at similar or different times? In other words, does Sephin1 increase or decrease the critical concentration of actin, polymerization rates, or other properties of actin?

A: We realised that graph labeling was poor: we are really sorry for that. Different colors show different experimental conditions, namely pyrene-actin polymerization assays run in presence of F-buffer, DMSO, or sephin1. Figure C and D show the outcome of sephin1 added at time 0, while figure E-F describe the kinetics of the polymerization of actin pre-incubated with sephin1.

In both cases, plateau levels are different, suggesting that sephin1 reduces the pool of g-actin.

Regarding the time to reach the plateau, we stopped our analyses after 3600 seconds. In our hands, 1 hour incubation was enough to reach a plateau only for the condition including F-buffer.

Q: The biological effects of Sephin1 on actin filaments in cells is unclear and inconsistent.

--Fig.5 relied on LifeAct overexpression, whereas preliminary data on the more important endogenous F-actin was relegated to the supplement. For the data with LifeAct in Fig.5B, what do the authors mean by "actin dots" (presumably LifeAct dots)? Examples of actin dots (with arrows and magnifications) should be highlighted in Fig.5A so the reader can understand what structures the authors are referring to.

A: In 2008 Riedl et. al. published LifeAct as a novel actin-binding probe. Lifeact is a 17 amino acid long peptide and binds preferentially to F-actin [6]. Since its publication, Lifeact has been fused to a variety of fluorescent proteins to label actin in vitro and in vivo [7]. It has been extensively demonstrated that transient expression of Lifeact in cell culture did not alter actin dynamics [8]. Super-resolution imaging of Lifeact and phalloidin in HeLa cells showed comparable results for imaging quality, filament thickness and length [9]. Accordingly, we consider LifeAct signal a reliable proxy for F-actin structures. As suggested, we included higher magnification insets with proper labelling.

Finally, please note that in Fig. 5 immuno-EM from cryofixed cells does show the subcellular localization of endogenous actin upon sephin1 treatment.

Q: --How does Sephin1 treatment quantitatively affect phalloidin staining of endogenous F-actin? Is this dose-dependent? This experiment is fundamental to understanding whether Sephin1 affects the cytoskeleton.

A: We now include data describing the impact of sephin1 50, 100, 200, and 250 µM (new supplementary figure 8C-D and Rebuttal figure 11A-B). Indeed we noticed a partial D/R effect. We did not quantify actin structures upon 250 uM, a condition where we noticed toxicity and a quite odd cytoskeletal organization.

Q: In Fig.S8, why do no phalloidin-stained actin "dots" appear in panel A, but several clumps of phalloidin-stained material appear in panel C? Panel B says n=8-10, but 8-10 what? Cells? Experiments? Experiments examining how many cells?

A: We now offer more representative pictures (see new supplementary figure 9A). The number (n) refers to the number of independent experiments, each one including at least 4 cells. We clarified this information in the material and method section. We now write “For imaging data, N reflects the number of independent biological replicates (coverslips), ensuring a minimum of 4–5 cells were sampled per experiment”

Q: As stated above, the jumping around on numerous pathways (e.g., autophagy, Golgi stress, GCN2 signaling, eIF2/PPP/CHOP, actin assembly, mTOR/TFEB signaling) throughout the figures was just too difficult to follow as currently written.

A: We improved the figures description.

Q: If the authors are specifically interested in following up on actin polymerization at the lysosome and mTOR signaling, they should begin with the Priya et al., 2023 Science Advances paper.

A: We now comment the paper suggested by the reviewer

REVIEWER # 2

Q: A central concern is the lack of robust and quantitative evidence supporting the regulation of autophagy. The use of sephin1 at concentrations up to 100 µM raises concerns about non-specific effects and cellular toxicity, especially in light of previous studies using substantially lower concentrations around 5 µM.

A:We have assessed cell viability upon 2 hours of sephin1 treatment at different concentrations. Our data indicate that 2 hours sephin1 is not overtly toxic at both 50 and 100 µM (Supplementary figure 1A). Instead, we registered slight toxicity at both 5 and 100 µM concentrations upon O/N incubation (Rebuttal figure 1A-B). By EM imaging of quick frozen samples, we did not notice toxicity upon sephin1 administration, considering global parameters such as cell density, membrane integrity, or organelle and nuclear morphology (Rebuttal figure 1C). In particular, the transient effects of 2 hours sephin1 treatment are less pronounced at 50 µM as compared to 100 µM. Longer incubation with 50 µM Sephin (4 hours and even overnight) did not visibly harm the cells either (Rebuttal figure 1C). We would like to remind here that in the original paper describing sephin1 [10], the authors performed several in vitro experiments using sephin1 at concentrations higher than 5 µM (as high as 50 µM, see for example the experiments included in figure S1 and S2).

Q2: The absence of dose-response and time-course analyses limits the interpretation of the observed effects. * Measurements of LC3 dynamics over time and across different concentrations are needed, together with analysis of established autophagy substrates such as p62 and NBR1.*

A: Dose-response and time-course analyses have been already included in the original submission. Please, see Supplementary figure 1B-F, where we explore D/R relationship and Supplementary figure 11A-I where we describe the time-course analyses of the molecular changes happening upon 100 µM Sephin1.

Furthermore, we tested the long term effect of a 2 hours pulse with sephin1 50 µM. In detail, we treated HeLa cells with sephin1 (50 μM, 2 hours). After the wash-out ( 8 hours) and the treatment with DMSO or bafilomycin (100 nM, 2 hours), we measured by western-blotting LC3-II. We did not notice a major effect on LC3-II, suggesting that the initial pulse at 50 µM is not sufficient to elicit subsequent autophagy. The output of such analysis is included in this rebuttal (New supplementary figure 14A-B and Rebuttal figure 2A-B ).

Prompted by Reviewer 2, we assessed the amount of p62. In particular, we analyzed the level of insoluble p62 in our experimental condition. In fact, the detergent insoluble fraction of p62 is a bona fide proxy for aggregated, polyubiquitinated protein complexes that eventually are cleared by selective autophagic clearance. More in detail, we treated HeLa cells with sephin1 (100 μM, 2 hours). After the wash-out ( 8 hours) and the treatment with DMSO or bafilomycin (100 nM, 2 hours), we solubilised the cells in a mild detergent buffer (1% Triton-X100, 50 mM Tris-HCl pH 7.4, 150 mM NaCl, 1 mM EDTA). Upon centrifugation (15K g, 4°C), we collected the pellet and measured by western-blotting p62 levels. As shown in Rebuttal figure 2C–D, sephin1 treatment did not induce the accumulation of insoluble p62-positive aggregates.

While p62 is a classic marker of autophagic flux under steady-state conditions, interpreting total p62 levels in our model is fundamentally confounded by transcriptional regulation. As we demonstrate in Figure 8D and Supplementary figure 13A–B, sephin1 strongly upregulates p62/SQSTM1 mRNA via TFEB (and likely ATF4/CHOP) during the washout phase. As highlighted in the autophagy guidelines [2, 3, 11], when p62 transcription is actively induced by cellular stress pathways, its protein levels cannot be reliably used as a readout for autophagic degradation, because de novo synthesis masks lysosomal turnover.

To overcome this, we relied on functional readouts of autophagic and lysosomal clearance capacity: (1) DQ-BSA dequenching (Figure 8E–F), (2) BafA1-sensitive LC3-II flux following the washout (Figure 9A–D), and (3) new ultrastructural data in human LRRK2 E193K fibroblasts (New Supplementary figure. 15A / Rebuttal figure 11C). These diseased fibroblasts suffer from massive baseline accumulation of jammed catabolic organelles; a sephin1 pulse followed by a 6-hour washout successfully clears this pathological waste, providing definitive morphometric proof of functionally enhanced autophagic clearance

Q: The study is largely restricted to HeLa cells, which are known to display particular features in their integrated stress response. This raises concerns about the general applicability of the findings.

A: Following the Reviewer’ s suggestions, we measured the impact of acute Sephin1 treatment (100 μM, 2 hours) in different cell lines, including human HEK293 and DIV14 primary murine neurons ( obtained from E15.5 C56BL/6 mice embryos). In both the models, acute sephin1 treatment induced LC3B-II accumulation. These results are included in the revised manuscript (new supplementary figure 2A-D) and in this rebuttal for the Reviewer convenience (Rebuttal figure 2E-H)

*Q: The lack of detectable increase in eIF2α phosphorylation in response to thapsigargin treatment is unexpected and should be clarified, as it may reflect suboptimal experimental conditions or timing. *

A: Indeed the choice of the exemplificative blot included in the original submission was poor. We apologize for this issue. However, the quantification did report that thapsigargin elicit eIF2 phosphorylation ( about 1.7 fold over control, see Figure 2D). We now include a more representative blot (new Figure 2B).

Q: The manuscript does not provide data on the expression or activity of PPP1R15A and PPP1R15B, despite their central role in regulating eIF2α phosphorylation and potentially Sephin's effect.

A: First, we apologize for a nomenclature error in the original Figure 3 legend. Sephin1's originally proposed specific target is PPP1R15A (GADD34). PPP1R15B (CReP) is the constitutive, sephin1-insensitive subunit. We ectopically overexpressed PPP1R15B as a genetic bypass to force constitutive eIF2α dephosphorylation even in the presence of sephin1. We have corrected the text and legends to reflect this. We have now included the western blots confirming that PPP1R15B overexpression effectively abolishes Ssphin1-induced eIF2α phosphorylation (New Figure 3D; Rebuttal figure 3C–D). We have also added qRT-PCR data showing that sephin1 induces PPP1R15A mRNA (a known ISR target) but not PPP1R15B mRNA (New Supplementary figure 2E–F).

Crucially, the Reviewer astutely points out the necessity of discussing the PPP1R15-PP1c-actin complex. The active eIF2α holophosphatase is a tripartite complex requiring G-actin for substrate specificity [12]. In the crystal structure of this holophosphatase (PDB: 4V0U), PPP1R15 binds G-actin directly at the hydrophobic cleft between subdomains 1 and 3. Remarkably, this is the exact same pocket where Cytochalasin D binds, and the very same interface where our PAL-MS and molecular docking localize Sephin1 binding (Figure 4B). We hypothesize that Sephin1 binding at the subdomain 1/3 cleft directly competes with or allosterically distorts the assembly of the active PPP1R15-PP1c-G-actin tripartite complex. During the revision, we will test the affinity of sephin1 to G-actin using the Creoptix WAVE platform, and we have expanded the Discussion to formally integrate the structural overlap between the sephin1 binding site and the holophosphatase G-actin interface.

Q: In particular in Figure 3, there is absolutely no demonstration provided, that the ectopic expression of PPP1R15B is sufficient to down-regulate or prevent eIF2 phosphorylation, while leaving LC3 processing intact.

A: We assessed eIF2 phosphorylation upon ectopic expression of PPP1R15B. As expected, PPP1R15B overexpression prevented sephin1 induced eIF2 phosphorylation. These data are included in the manuscript (new Figure 3D and Rebuttal figure 3C-D).

*Q: The specificity of GCN2 involvement is also not convincingly demonstrated, as other eIF2α kinases are not excluded experimentally. *

A: Indeed other pathways may link lysosome physiology and eIF2 phosphorylation. eIF2α phosphorylation acts as the central molecular switch that pauses general translation during lysosomal stress. For example, lysosomal membrane damage triggers the leakage of calcium from the punctured lysosomal lumen into the cytosol. This localized spike in calcium is sensed by the scaffolding protein ALIX. ALIX recruits and activates the kinase PKR. This physical sensor complex directly drives the phosphorylation of eIF2α. However, our data exclude lysosomal damage (Supplementary Figure 1G-H , plus ultrastructural observations) or any major role of Ca2+ (Supplementary Figure 12A-B). Another major pathway initiates on lysosomes. Lysosomal damage hampers the organelle's role as an amino acids recycling hub. Alteration in lysosome membrane potential slows down membrane transporters like SLC38A9, stopping the efflux of recycled amino acids into the cytosol. This scarcity reduces tRNAs loading with amino acids. The accumulation of uncharged tRNAs is intercepted by the metabolic sensor kinase GCN2. Upon activation, GCN2 phosphorylates eIF2α. To explore such a scenario, we monitored eIF2 phosphorylation and LC3-II accumulation in cells treated with sephin1 ( 2 hours, 100 μM ) and cultured in normal media or upon essential amino acids extra supplementation (5X). Noteworthy, essential amino acids supplementation did not prevent either sephin1 induced eIF2 phosphorylation or LC3II accumulation, suggesting another mechanism is involved. These data are included in the revised manuscript (New supplementary figure 2G-I and Rebuttal figure 3E-G). We deem that the minor/no role played by an hypothetical lysosomal damage or amino acids starvation , together with our pharmacological evidence of the implication of GCN2, strongly support our initial hypothesis that GCN2 senses actin cytoskeleton remodelling

Q: Although the manuscript emphasizes actin as a primary target of sephin 1, the supporting evidence remains incomplete. The proteomic analysis from FG08 pull-down experiments is not fully reported, and a comprehensive list of interacting proteins is missing.

A: To identify bona fide sephin1 interactors, we performed a pull-down followed by a SDS-PAGE. Upon silver stain, we selected the prominent band at ∼42kDa for the follow-up MS/MS analysis. Actin with more than 1370 identified peptides was by far the most abundant protein in the FG08 pull-down sample. We now added the full list of the identified proteins (New supplementary table 1).

Q: The imaging of actin structures could also be improved, as the observed punctate signals may correspond to focal adhesions or other actin-based structures that are not characterized here.

A: We agree with the reviewer that a characterization of the actin punctate signals was missing.

The actin cluster observed upon acute sephin1 treatment localized mainly in the perinuclear zone. Rather than focal adhesions ( that are normally present on the cell membrane), we focused on actin comet tails, an actin structure propelled by WHAMM protein and related to autophagosome biogenesis [13]. To this aim, we transfected HeLa cells with GFP-WHAMM (kindly provided by Campellone’ s lab). The day after, we treated cells with sephin1 (2 hours, 100 μM). Upon fixation, we processed the cells to visualize actin structure via phalloidin. We did not report an evident colocalization between actin cluster and GFP-WHAMM signal, suggesting that actin punctate signals nature is different from comet tails. These results are included in the new Supplementary figure 9D and reported also here for Reviewer’s convenience (Rebuttal figure 4A).

Q: Additional functional assays, such as analysis of actin repolymerization dynamics or cell migration, would help establish the relevance of the observed phenotypes.

A: We monitored the impact on cell migration by the wound healing assay. In particular, we grew HeLa at full confluency, then created a physical gap within the cell monolayer. We treated the cell for either vehicle or sephin1 2 hours and then we monitored cell migration into the gap by taking photos at different time points (6, 12, 18, 24, 30 hours). Interestingly, we noticed that the sephin1 pulse did not significantly alter cell migratory behaviour. These results are included in the new Supplementary figure 8E and reported also here for Reviewer’s convenience (Rebuttal figure 4B-C). Altogether, our data suggest that our treatment (sephin1 100 μM 2 hours) does not permanently affect actin dynamics.

Q: Quantitative analysis is lacking, and the mechanistic relationship between actin disruption and Golgi disorganization is not explored in depth. No experimental strategy to determine if protein secretion or glycosylation are affected by sephin1 was provided in the current manuscript. As a result, the connection between these observations and the proposed signaling cascade remains unclear.

A: As suggested we analysed the glycosylation pattern of Negr1, an adhesion protein that undergoes glycosylation in six different sites. By western-blotting, fully glycosylated Negr1 runs at the apparent MW of 50 kDa and the naive protein at 30 kDa [14]. We treated cells with sephin1 (2 hours and 6 hours, 100 μM), monensin (6 hours, 500 nM), and vehicle. To appreciate the extent of Negr1 glycosylation we computed the ratio between the isoforms at 50 and the one at 30 kDa. We found that sephin1 treatments did not overtly affect Negr1 glycosylation. These results are included in the Rebuttal figure 4D-E. Altogether, our data suggest that our treatment (sephin1 100 μM 2 hours) does not overtly affect Golgi physiology.

Q: The use of classical actin-polymerizing and -depolymerizing agents and genetic deletion of PERK has previously demonstrated that eIF2α phosphorylation can be modulated by the state of actin polymerization. In this context, the effects observed upon Sephin1 treatment on eIF2α could plausibly arise as a consequence of altered actin dynamics. Although the manuscript discusses a potential increase in globular actin levels, the functional consequences of this rise are not explored by direct experiments. Furthermore, while the discussion highlights the role of actin in Golgi organization and autophagosome formation, the study lacks a detailed and mechanistic analysis of these processes.

A: We did our best to clarify the connection among sephin1, actin cytoskeleton, Golgi integrity , and autophagy. In particular, we investigated more in detail the impact of the ARP2/3 inhibitor CK-666. In fact, we already showed that CK-666 (250 μM, 2 hours) prevents the acute effect of sephin1 in terms of formation of actin clusters (Figure 5A-C) and LC-3II accumulation (Figure 5D-F). However, it does not prevent Golgi fragmentation (Figure 5H and Rebuttal figure 5C ) nor TFEB translocation induced by sephin1 (Rebuttal figure 5A-B). Still, CK-66 co-administration prevented late stage autophagy (Figure 9). Actually, we found that the ARP2/3 inhibitor CK-666 ( 250 μM, 2 hours) by itself affects Golgi integrity (Rebuttal figure 5C), induces CHOP mRNA (Rebuttal figure 5D) and elicits TFEB translocation (Rebuttal figure 5A-B).

However, a pulse with only CK-666 ( 250 μM, 2 hours) is not sufficient to trigger late stage autophagy (Supplementary figure 14C-D and Rebuttal figure 5E-F).

Altogether, these data suggest that Golgi integrity signals directly to the mTOR-TFEB pathway, as recently suggested also by PMID: 42115886. Our new data clearly indicate that TFEB is instrumental for sephin1 driven increase in lysosomal activity (New supplementary figure 12F-G and Rebuttal figure 6A-B). Therefore, we deem that TFEB translocation associated with Golgi fragmentation is necessary but not sufficient to induce late stage autophagy. We included in this revision new data describing that the co-administration with Cytochalasin D (1 μM) and sephin1 (100 μM) prevents late-stage autophagy ( New supplementary figure 14E and Rebuttal figure 6C). Given that Cytochalasin D impairs sephin1 binding to actin (figure 4H-I), we are confident that the actin alterations observed upon acute sephin1 treatment play a major role in orchestrating a full autophagic response.

*Q: The evidence supporting modulation of mTORC1 signaling is not fully convincing. The quality of the 4EBP1 immunoblots is insufficient for reliable interpretation, and appropriate controls using established mTOR inhibitors such as rapamycin or Torin1 are missing. *

Additional readouts, including phosphorylation of S6, should be included.

A: We will complement our biochemical analyses as requested by the reviewer. Furthermore, we specifically verified that sephin1 increases lysosomal activity via TFEB by assessing DQ-BSA signals in the TFEB KO HeLa line described in [15]. The cells were previously incubated overnight with 10 μg/mL of DQTM Red BSA added in normal medium. Then we treated HeLa cells with sephin1 (100 μM, 2 hours). After the wash-out ( 8 hours) we processed the cells for imaging purposes. Sephin1 did not increase DQ-BSA signals, a proxy for lysosomal activity, in TFEB KO cells. These data further support our hypothesis that sephin1 triggers lysosomal activity via the mTOR-TFEB pathway. These results are included in the new Supplementary figure 12F-G and reported also here for Reviewer’s convenience (Rebuttal figure 6A-B).

Q: Finally, the manuscript does not sufficiently address the broader pharmacological context of sephin1. Given the ongoing discussion regarding the specificity of this class of compounds, it would be important to compare sephin1 with related molecules such as guanabenz or other derivatives (Raphin 1?).

A: Guanabenz acts as a highly potent α2-adrenergic receptor agonist, which confounds its cellular effects and limits its clinical utility due to severe hypotensive activity. To rigorously assess the structure-activity relationship (SAR) of this chemical class without adrenergic confounding, we synthesized three novel structural analogues of sephin1: DG161, EC190, and PF03 (Rebuttal Figure 7–9). Strikingly, these novel derivatives recapitulate the exact mechanism of sephin1—including actin cluster formation, CK-666-sensitive LC3-II accumulation, TFEB nuclear translocation, and enhanced lysosomal DQ-BSA activity—but achieve these effects at 4- to 20-fold lower concentrations (5 µM for DG161; 25 µM for EC190) compared to Sephin1 (100 µM). This analogue data definitively confirms that the MoA we describe is an on-target property of the pharmacophore, rather than a non-specific artifact of 100 µM dosing. These SAR data will form the basis of a follow-up manuscript, but we will gladly include a summarized discussion of this in the revised text to address the Reviewer's broader pharmacological question.

Description of analyses that authors prefer not to carry out

Reviewer 2

Q: Alternative mechanisms, including effects on protein folding activity of the ribosome of these compounds (https://doi.org/10.1021/cn5001588), which could directly impact ribosome collision leading to GCN2 and subsequent mTORC1 activation, are not explored experimentally. This limits the ability to assess whether the observed effects are specific to actin modulation or reflect a more general stress response.

A: The ribosome collision hypothesis is indeed intriguing, but technically challenging and far beyond the scope of this manuscript. Still, we deem that our existing data can partially address it . A direct effect on the ribosome causing translational stalling/collision would immediately halt global protein synthesis. However, our puromycin incorporation assay (Supplementary Figure 3A–B) shows no global translation elongation block at 2 hours. Furthermore, our time-course kinetics (Figure 6C–D, Supplementary Figure 11) demonstrate that robust actin clustering occurs within just 10 minutes of sephin1 exposure, whereas GCN2-dependent eIF2α phosphorylation does not peak until 120–240 minutes. This temporal hierarchy strongly positions cytoskeletal remodeling upstream of the ISR, rather than the reverse. Finally, treating cells with Cycloheximide—a classic translation inhibitor that stalls ribosomes—fails to induce the acute LC3-II accumulation (Supplementary Figure 3C–H) or the late TFEB-target transcription (Supplementary Figure 13D) seen with Sephin1.

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Author response:

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

eLife Assessment:

This useful study employs optogenetics, genetically-encoded dopamine and serotonin sensors, and patch-clamp electrophysiology to investigate modulations of neurotransmitter release between striatal dopamine and serotonin neurons - a topic of interest to neuroscientists studying the basal ganglia. The results suggest that the dopamine and serotonin systems operate largely in parallel, with the activation of serotonin neurons resulting in a small, transient dopamine release. The authors suggest that this interaction occurs via glutamate release in the ventral tegmental area, findings that are closely related to previous work. Some conclusions are incomplete requiring larger samples-sizes and controls.

We sincerely thank the editor and reviewers for their thoughtful and constructive comments. Addressing their concerns required extensive additional experimental work and the involvement of new personnel. We increased sample sizes, completed previously missing experimental groups, generated a largely new dataset, and performed additional anatomical experiments and analyses. We also removed the patch-clamp electrophysiology experiments to sharpen the study’s focus and extensively revised and reorganized the manuscript to address methodological and interpretative inconsistencies. Although the central concept remains unchanged, the revised manuscript provides a substantially more rigorous and consistent account of the limited and directionally asymmetric circuit-level coupling between striatal dopamine and serotonin release.

Public Reviews:

Reviewer #1 (Public review):

Summary:

In this study, Liu et al use optogenetics and genetically encoded neuromodulator sensors to test the extent to which dopamine neuron stimulation produces striatal serotonin release, and vice versa. The study is timely given growing interest in dopamine/serotonin interactions and in the context of recent work showing bidirectional and dynamic regulation of striatal dopamine by another neuromodulator, acetylcholine. The authors find that striatal dopamine and serotonin afferents function largely independently, with dopamine neuron stimulation producing no striatal serotonin release and serotonin neuron stimulation producing minimal striatal dopamine release. This work will inform future work seeking to dissect the contributions of striatal dopamine, serotonin, and their interactions to various motivated behaviors. While the paper's main conclusions are adequately supported (see Strengths), additional controls and experiments would significantly broaden the paper's impact (see Weaknesses). Finally, this draft of the work is poorly presented with numerous errors, omissions, and inconsistencies evident throughout the text and the figures that should be addressed.

Strengths:

The study employs optogenetic stimulation simultaneously with fiber photometry recording of dopamine or serotonin release measured with genetically encoded sensors. These methods are state-of-the-art, offering tighter temporal control compared to pharmacological methods for manipulating dopamine and serotonin and improved selectivity over techniques like electrochemistry and microdialysis used to record neuromodulator release in previous studies on the subject. As a result, the paper's main conclusions are well supported.

Weaknesses:

(1) The electrophysiology experiments in Figure 3 are only tangentially related to the focus of the study, and their findings are almost entirely irrelevant to the paper's main conclusions. The results of these experiments are also not novel. Glutamate corelease from 5-HT neurons has been previously shown, including in the OFC and VTA (Ren et al, 2018, Cell, McDevitt et al, 2014, Cell Rep, Liu et al 2014, Neuron; and others). The authors should explain more clearly what they think these data add to the manuscript and/or consider removing them altogether.

We thank the reviewer for their insightful comments regarding the patch-clamp electrophysiology data. We acknowledge the concerns raised by multiple reviewers and have therefore removed these data from the revised manuscript to improve clarity and focus.

(2) Related to the point above, as far as I can tell, the only value the electrophysiology data add is to suggest that perhaps activation of serotonin neurons may drive minimal striatal dopamine release via glutamate corelease in the VTA. The evidence provided in this version of the manuscript is insufficient to support that claim, but the manuscript would be significantly strengthened if the authors tested this hypothesis more directly. One way to do that could be to stimulate serotonin axons in the striatum (as opposed to the serotonin cell bodies) and record striatal dopamine release.

This is an interesting approach. However, given the divergent projection of serotonin fibers and the need for a strict spectral separation between excitatory opsin and transmitter sensor fluorescence, we retained the current approach, which allows us to investigate circuit-level interactions while minimizing technical confounds.

A complementary anatomical approach would be to use retrograde tracing to test whether the DR 5-HT neurons projecting to the striatum are the same or different from the VTA projecting population.

We performed the suggested experiment and have included the new data in the revised manuscript (Figure 1F–H). This approach revealed a clear topographical organization. These results indicate that the identified neuronal populations are largely segregated.

(3) The findings would be strengthened by the addition of a fluorophore-only control group lacking opsin expression in all experiments in Figures 1 and 2.

We thank the reviewer for this important suggestion. We requested authorization to add an opsin-negative control cohort, but this request was not approved under the applicable animal-welfare regulations. We therefore cannot fully exclude nonspecific physiological effects of light delivery and now acknowledge this limitation in the Discussion. Nevertheless, the stimulation-locked response was confined to the biosensor channel and absent from the isosbestic channel, arguing against direct optical contamination. Moreover, application of the same optical stimulation protocol in the VTA did not generate a detectable stimulation-locked 5-HT signal. Although these observations do not fully replace an opsin-negative control, they support the interpretation that the response reflects a biological signal rather than direct optical interference.

(4) The experiment of stimulating serotonin neurons and recording serotonin release in the NAc was not performed. It would be useful to be able to compare the magnitudes of evoked serotonin release in these two striatal regions, though it is not central to the main claims of the paper.

This point has now been addressed with additional experiments, and the figure has been reformatted accordingly in the revised manuscript.

(5) The interpretation of the results from Figure 2 is described inconsistently throughout the manuscript. The title implies there is significant crosstalk between the dopamine and serotonin systems. The abstract calls the crosstalk "transient", which is a description of its temporal dynamics, not its magnitude. Then the introduction figures and discussion all suggest the crosstalk is minimal. I suggest the authors describe the main findings - minimal crosstalk between the dopamine and serotonin systems - clearly and consistently in the title, abstract, and main text.

We agree with the reviewer and have revised the title, abstract, Results, figure legends, and Discussion to describe the magnitude and directionality of the interaction consistently. The revised manuscript now emphasizes that striatal dopamine and serotonin release operate largely in parallel, with limited and asymmetric crosstalk: activation of VTA dopamine neurons did not produce detectable serotonin release, whereas activation of dorsal raphe serotonergic neurons induced only a weak, stimulation-locked dopamine signal without a sustained increase in dopamine amplitude. The revised title, “Asymmetric Circuit-Level Crosstalk Between Dopamine and Serotonin Release in the Striatum,” and the corresponding changes throughout the manuscript now more accurately reflect these findings.

Reviewer #2 (Public review):

Summary:

This brief communication aims to clarify interactions between the dopamine (DA) and serotonin (5-HT) systems of mice. The authors use optogenetic stimulation of DA neurons in the VTA or of 5-HT neurons in the DRN, while monitoring the fluorescence of DA and 5-HT sensors in the nucleus accumbens (NAc) and dorsal striatum (DS) using fiber photometry. The authors report on a small release of DA in the NAc following DRN stimulation, which they attribute to glutamate co-release onto VTA DA neurons using slice electrophysiology. The authors also report on cocaine-induced 5-HT release in the striatum.

Strengths:

This is a topic well worth studying.

Weaknesses:

In its current form, this is an incomplete and underpowered study that does little to clarify the complicated relationship that exists between DA and 5-HT in the mammalian brain under physiological conditions or during cocaine use.

We appreciate the reviewer’s thorough evaluation and constructive efforts. We acknowledge that the original manuscript did not meet the expected standards and have therefore undertaken a complete revision. We hope that the revised version addresses the concerns raised and provides a clearer and more rigorous presentation of our findings.

Reviewer #3 (Public review):

The authors suggest that the small release of DA may be due to a release of glutamate from DRN 5-HT neurons to the VTA that stimulates weakly and in a transient fashion the VTA DA neurons, which in the end, produce a transient and small release of DA in the NAc.

Their findings give more information on the previously reported complex and partial known crosstalk between 5-HT and DA in the NAc.

I only have some minor concerns about the manuscript:

(1) In Figure 2F, there is a missing curve for 5-HT in NAc. Besides, the legend shows n=2, making it difficult to perform statistical analysis with that data.

We repeated the experiments and analysis with a new and expanded dataset. We believe this revised dataset now provides sufficient power for robust statistical analysis.

(2) In Figure 3, the use of NBQX/AP5 is shown, but it is not mentioned either in the methodology or in the discussion. What is the meaning of those results?

Based on the reviewers’ suggestions, we have removed this figure entirely from the revised manuscript.

(3) Line 98 compares results from two different places of stimulation. The results are related to stimulation in the VTA, but the comparison indicates that the stimulation was made in the DRN.

The manuscript has been extensively revised, and all relevant sections of the text have been updated accordingly.

(4) If the release of 5-HT in Nac does not occur, it needs to be precise in the abstract that 5-HT is released in the dorsal striatum (DS) but not in the NAc (line 19).

We performed an additional set of experiments and confirmed the presence of 5-HT release in the NAc.

(5) Be consistent with the way you mention the 5-HT neurons. For example, in lines from 106 to 119, SERT neurons are used. Previously, 5-HT neurons were used.

We have carefully considered this issue throughout the revised manuscript and have taken steps to ensure consistency, as highlighted by the reviewer.

(6) There are several points of confusion when referring to the figures, making the text difficult to follow because the text explains something that is not shown in the figure cited.

We have carefully considered this issue throughout the revised manuscript and have taken steps to ensure consistency, as highlighted by the reviewer.

Recommendations for the authors:

Reviewing Editor Comments:

Additional comments from the reviewers recommend that the authors increase sample sizes, carry out control experiments to exclude non-specific effects, and modify the title and abstract to reflect the minimal cross-talk observed between dopamine and serotonin. Finally, we note that the text of the manuscript does not meet minimum standards in the field for clarity, interpretability, or reproducibility.

We acquired a new experimental cohort, and performed additional experiments suggested by the reviewer. The manuscript has been revised and reformatted, incorporating all reviewer comments. We hope that this new version now meets the expected standards for clarity, interpretability, and reproducibility in the field.

Reviewer #1 (Recommendations for the authors):

(1) For angled stereotactic injections, the direction of the angle (ML, AP, etc) is not defined.

Added to the revised manuscript.

(2) The manuscript is full of grammatical errors and is very difficult to follow in some places, especially the results section for Figures 2 and 3. The following is an incomplete list of the most obvious errors to give examples of what I mean, but I strongly urge the authors to thoroughly revise the entire text.

(a) There appear to be photometry traces copied and pasted by mistake over the x-axis labels in the bar graph in Figure 1E.

(b) Line 41 states that fiber photometry recordings were used in reference 17, which is a human study that used voltammetry.

(c) Figures are referenced out of order throughout.

(d) Acronyms are used without being defined on the first usage.

(e) Lines 54-56, missing references.

(f) Line 82, the crosstalk reported in this paper is unidirectional, not bidirectional.

(g) Line 92 describes the virus as AAV-dLIGHTX.XX, where presumably the exes are placeholders for numbers that were never replaced.

(h) The text of the results section for Figure 2 in some cases directly contradicts the data it describes, and likely has some mistaken figure panel references.

(i) Line 123 is missing a reference and just has the placeholder REF.

(j) Lines 182-183 are a copy-paste mistake from lines 185-186.

(k) Scalebars in figure legends are in units of micromolar, not micrometers.

The manuscript has been extensively rewritten to address and incorporate the reviewers’ comments.

Reviewer #2 (Recommendations for the authors):

This is one of the least impressive and compelling manuscripts I have ever been asked to review. It reads in many ways like a first draft, not like a document that was meticulously prepared and proofread prior to submission. The data and analyses are shockingly light (with some conclusions supported by an N of 1 or 2) yet frustratingly difficult to interpret. The text and figures are full of typos, inconsistencies, and factual errors in interpretation. Most concerningly, this study does little to clarify the complicated relationship that exists between DA and 5-HT, including providing compelling evidence for their key finding of 'crosstalk' between both modulators or mechanistically implicating glutamate co-release. In fact, it might add to the noise. It is therefore unclear what the value is of this study in its current form.

We thank the reviewer for their detailed and thorough comments, which we saw as an opportunity to substantially improve the manuscript. We have therefore undertaken a comprehensive revision to improve clarity, coherence, and overall quality. As part of these revisions, we have removed the original Figure 3 presenting the in vitro patch-clamp electrophysiology data. We hope that the extensive changes implemented in the revised manuscript adequately address the reviewer’s concerns and significantly strengthen the study.

General comments:

(1) Limited scope: the design of the experiments performed offers very few opportunities for identifying 'crosstalk' between DA and 5-HT:

(a) To most, such cross-talk might best be imagined at the level of cells expressing receptors for both modulators, yet this is not studied. Cross-talk may also manifest in complex circuit-level interactions, downstream of brain areas directly targeted by DA and 5-HT. This is not studied either. Instead, only one type of experiment is performed: optogenetically stimulating cell bodies in the midbrain while monitoring DA/5-HT levels in the striatum. Opportunities for 'cross-talk' in this preparation are exceedingly limited. For example, the only way that optogenetically-evoked DA release may impact 5-HT levels (assuming classical, direct projections from DA neurons to the striatum) is via presynaptic modulation of 5-HT release from axons. Though potentially interesting, it is not exhaustive.

We agree that many types of crosstalk can be investigated; however, we chose to first adopt a broader approach that integrates neuronal circuit-level mechanisms. We believe that an important discrepancy remains in the literature that needs to be addressed. While our findings do not exclude the involvement of other forms of crosstalk, they aim to clarify whether crosstalk already exists at the level of neuronal circuits, which our results support.

(b) Any negative modulation of DA or 5-HT release would require a baseline tone of either modulator within the dynamic range of the sensor, which is not demonstrated. Thus, in both cases, a negative influence cannot be excluded, limiting any finding to 'positive' modulation. This is problematic for a study set on setting the record straight on 'cross-talk' between DA and 5-HT, given that prior studies pointed to antagonistic influences.

Previous studies using the same type of sensor have already demonstrated inhibitory crosstalk. For example, the study “Opponent Control of Reinforcement by Striatal Dopamine and Serotonin” successfully used this approach to reveal opposing interactions between dopaminergic and serotonergic signalling. Therefore, our findings are consistent with the possibility of circuit-level crosstalk and further contribute to resolving this ongoing question.

(c) Only one stimulation paradigm is tested, and its biological (ir)relevance is not discussed.

The stimulation paradigm used in this study has been extensively validated in multiple publications from our laboratory and has consistently been shown to promote reinforcement. Our recent review provides a comprehensive overview of this approach and its established behavioral effects. (Lüscher et al, Neuron, 2026, PMID: 42462721).

(d) Only one brain region is investigated (striatum), with little justification for omitting other regions where both modulators coexist (e.g., amygdala, cortex, DRN).

Not all brain structures can be investigated within the scope of a single study, and we acknowledge this limitation in the Discussion section.

(e) The suitability of the chosen behavior and cocaine administration to reveal interactions is not mentioned.

We have now clarified the use of i.p. cocaine injection to study the different temporal dynamics of 5-HT and DA release.

(2) Scarcity of data and questionable analyses and interpretation:

We thank the reviewer for the detailed comments listed below (a-m). In response, we repeated many experiments, increased sample sizes, completed the experimental groups, fully reanalysed the dataset, and removed the patch-clamp electrophysiology data. The manuscript has been extensively rewritten and reformatted based on a largely new dataset. In addition, we now focus specifically on one form of crosstalk and have expanded the discussion to address other potential mechanisms, as suggested by the reviewer. We hope this revised version adequately addresses the concerns raised. Because of the many changes in the text, the concerns listed below were addressed.

(a) Conclusions for Figures 3B and C are based on a N of 1 whole cell recording each.

(b) The relevance of data in Figures 3D and 3E to test the proposed hypothesis is unclear.

(c) Figure 2F is an average of N=2 recordings.

(d) Lines 98-100: Concluding statement not supported by experiment performed.

(e) Apparent contraction: Lines 112-113 indicate that 5-HT neuron stimulation failed to evoke 'any significant change in DA', while lines 117-118 talk about a small but significant increase in DA in response to the same manipulation.

(f) Line 114: conclusion not supported by data; Figure 2E points to DA, not 5-HT, and Figure 2F-H only shows 5-HT in DS, not NAc. Legend specifies that only 2 recordings are averaged in Figure 2F, and n=4 are quantified in Figures G and H, despite the plot containing 5 data points. What is going on?

(g) The key finding of this study is a transient, barely-detectable increase in NAc DA for ~1s during the 10s stimulation of 5-HT neurons in N=4 mice (Figure 2D). It is not clear if a significant increase was observed in all mice tested, or if this increase is significantly different from what is seen in DS. Was this effect seen in multiple testing sessions?

(h) Concerningly, the authors do not exclude the possibility of a 'startle' response to strong light delivery in mice expressing tdTomato-only. This is an essential control that is missing.

(i) Very few details regarding this DA response are offered. How soon does it appear following DRN stimulation? If mediated by glutamate co-release, it ought to appear with the very first light stimulus.

(j) The physiological significance of this stimulation paradigm is not established. Comparing it to cocaine-evoked DA release is not satisfactory, as cocaine elevates DA beyond levels encountered physiologically.

(k) Correlative evidence to implicate glutamate is insufficient. Does co-release depress when driven with the same stimulus train as that applied in vivo? Is it strong enough to drive DA neuron firing? Does it not affect DS-projecting DA neurons? Does this DA 'blip' disappear in mice genetically deficient in glutamate co-release (using SERT-Cre vglut2-floxed mice, which are commercially available)?

(l) The authors don't find evidence for DA stimulation affecting 5-HT release in the striatum. Is this sufficient to exclude any influence of DA on 5-HT? Isn't the fact that cocaine evokes 5-HT release evidence of an interaction? As such, it is unclear if the experiments performed significantly advance our understanding of whether and how DA and 5-HT influence one another.

We respectfully disagree with this statement. Cocaine directly binds to the serotonin transporter (SERT), thereby blocking serotonin reuptake into the presynaptic terminal and increasing extracellular 5-HT levels in the synaptic cleft. Furthermore, dopamine and serotonin release exhibit distinct temporal dynamics, suggesting that their release is mediated through different molecular mechanisms and neural circuit pathways rather than through a single shared process.

(m) The evidence that 5-HT stimulation alters DA release in the striatum is not compelling, but also not sufficient to exclude or support cross-talk between both modulators. The evidence provided is simply insufficient to strongly validate or challenge earlier studies.

(3) Minor:

In this revised manuscript, we have carefully implemented the reviewers’ suggestions and addressed the concerns they raised. We believe that this revised version addresses a significant proportion of the reviewers’ concerns and hope that these fundamental improvements are fully recognized during the evaluation.

Because of the many changes in the revised manuscript, the concerns listed below do no longer apply or were addressed.

(a) In the intro paragraph, line 19, specify that you are monitoring DA/5-HT in the striatum of mice.

(b) In the results section, indicate the preparation: in vivo, awake, what were the mice doing...

(c) Inconsistent nomenclature: VTA dopamine neurons are referred to as 'VTA DA', while dorsal raphe serotonergic neurons are referred to as 'DRN SERT' or 'DR SERT'. Why the difference? Is there any reason to believe that SERT-Cre mice label non-serotonergic neurons? Please adopt a consistent nomenclature and/or justify your choice. Also, if neurons are optogenetically stimulated, specify the word 'neuron' (e.g., line 118 refers to 'DR SERT stimulation', which could be interpreted to suggest the transporter is being activated).

(d) Line 103 and elsewhere: Confusing terminology referring to VTA DA neurons stimulation as 'modulating' or 'altering' DA release in the striatum. Isn't it directly evoked by the stimulation of DA-releasing neurons? Please change the terminology so as not to make it unnecessarily vague.

(e) Lines 111-112: comparison between DA and 5-HT fluorescence devoid of biological meaning. Relative increases in the fluorescence of 2 sensors that are molecularly distinct and separately-expressed in different cohorts of mice cannot be meaningfully compared.

(f) The timeline in Figure 1A suggests that the optogenetic stimulation protocol is initiated 5 min prior to cocaine injection. Figure 1D (right) plots this 5 min baseline, yet little/no DA release can be seen, despite Figure 1F indicating peak DA ratios of 0.5-1. Please explain. Since both sets of recordings were performed back to back and are directly compared, make sure to show them both on the same graph for direct comparison.

(g) Figure 1E contains 2 misplaced data traces.

(h) Figure 2D. Please repeat for the full stimulation window, not just for the few seconds where a tiny change in DA is seen.

(i) Figure 2E is misleading. It suggests that the peak extracellular DA concentration in NAC following DRN stimulation is approximately half of what cocaine evokes and similar to what VTA DA stim evokes (Figure 1F). But this is simply not true. There must be an error in calculation, and one should wait more than 20 minutes to properly estimate peak DA concentration in cocaine.

(j) What is the value of comparing optogenetically-evoked neuromodulator release to cocaine-evoked release? Can the authors be sure that the DA levels reached in cocaine are not saturating the DA sensor? Wouldn't this be required to permit comparison?

(k) Line 123: Please include a citation. Rephrase the sentence to avoid sounding dismissive.

(l) Line 124: Vague/confusing sentence. What is meant by 'optogenetic projection targeting' and 'parsing the synaptic currents in identified regions'?

(m) Figures 1D, 1G, 2C, 2F: confirm y-axis unit of measure. Are DA transients really only 0.2% in amplitude?

(n) Figure 3B, 3C: number of recordings performed in DA and NAcSh, anterior not specified. Only one trace showed, and no summary plot. Insufficient data presented to draw conclusion.

(o) How does the presence of EPSCs in OFC or NAc help support the author's finding of a brief elevation of DA upon DRN stimulation?

(p) Line 358: Wrong unit.

Reviewer #3 (Recommendations for the authors):

Some minor concerns are the following:

(1) In line 31, define what DS is.

(2) In line 57, the word "neurons" is missing in the phrase ".....decreases 5-HT neuron spontaneous firing in DRN,...".

(3) In line 111, the comparison needs to be between 5-HT release due to optogenetic stimulation with the 5-HT release due to cocaine infusion, not with DA release due to cocaine infusion.

(4) In line 112, it should be Figure 2F.

(5) In line 114, instead of 5-HT, it should be DA. In addition, it is not Figure 2E, but 2C.

(6) In line 123, add the appropriate reference instead of "REF".

(7) In lines 182 and 183, the text is out of context.

(8) In lines 250 - 251, the text is out of context.

(9) Why was Rabit anti-GFP if you do not use GFP in the procedures?

While the manuscript underwent a complete comprehensive revision to improve clarity, coherence, and overall quality, we have carefully implemented the reviewers’ suggestions and addressed the concerns they raised.

Reviewer #2 (Public review):

Summary:

In their manuscript "Penumbria: Advanced 3D cell segmentation for biomedical imaging", the authors describe their 3D nuclei segmentation pipeline and compare it against state-of-the-art methods for nuclei and cell segmentation.

The introduction is clear, with state-of-the-art methods, for instance, segmentation of cells from microscopy images, and motivates the method with science that can be done with cell segmentation. Related work is appropriately mentioned with the caveat that it conflates cell and nuclei segmentation, and some related work is missing.

The Results section describes the loss, the architecture novelties, and evaluation results on nuclei segmentation, not cell segmentation. Here it becomes clear that Penumbria addresses 3D nuclei segmentation, i.e., instance segmentation of medium-sized, mostly convex-ish and well-separated objects in single-channel 3D volumes.

Penumbria combines several choices and innovations:

- loss: boundary distance regression<br /> - architecture<br /> - 3D U-VixLSTM<br /> - Zernike Layer<br /> - SGG<br /> - combine multiple scales in SGG<br /> - sampling strategy to look for bright and dark objects.

The authors show on four nuclei segmentation benchmarks from confocal images that Penumbria outperforms CellPose-SAM (in either zero-shot or fine-tuned mode) and Stardist-3D in most cases, except for some where Stardist-3D performs better. They report results of an IoU threshold sweep to measure instance segmentation performance.

Penumbria is available on GitHub under a non-commercial license. I have not tested it yet, and therefore assume that the code is in full working condition and reproduces the reported results.

Strengths:

(1) The method may outperform state-of-the-art methods for cell segmentation as shown in three of four 3D benchmarks.

(2) The code is available.

Weaknesses:

Major

(1) Similar to the established confusion across the literature, all the authors' evaluation datasets do not label cells, but cellular nuclei. This is important to understand because the methods they compare against, CellPose-SAM and Stardist-3D, demonstrate their performance on a variety of datasets, some of which label cellular membranes instead of nuclei. The cell segmentation task is often considered harder than the nuclei segmentation task, because objects consistently touch each other, the separation may have noise-induced holes, and object shapes may be more diverse than for nuclei.

(2) The addition of U-VixLSTM, SGG, multi-scale input, Zernike layers, and distance transform regression sounds great, but a comparison to architectures or conventional losses used to train any combination is missing. Five innovations/choices combined simultaneously without an attempt to attribute.

(3) There is no clear delineation of 2D and 3D approaches. E.g. CellPose-SAM is not 3D, but sequential 2D execution with optional averaging of doing this along all axes.

(4) For the 3-fold cross-validated evaluation: It sounds like they were all trained for each benchmark independently? Did Stardist-3D and CellPose SAM start from their existing 'general' weights or from scratch (not possible with SAM, I know). Not described at all.

(5) Experiments to evaluate generalization performance are missing (train on all datasets, compare across datasets, ...).

(6) The Zernike layer optimizes only coefficients {3,4,12}; the evaluation could be described as rudimentary. Table 3 is missing cross-validation. Since mouse_skull is (a lot) different and differences for the others are minor, I would be curious how significant these results are. The following text is unclear: "This reflects how we developed these modifications in turn." How so?

(7) Training and inference: input and output block size missing, GPU memory requirements undefined, discuss block size vs. batch size. 50% overlap block-inference with feathering not compared to other overlap ratios, just "works best". Test-time augmentation 8x rotation (what are those rotations? Why 8? How much does it contribute? Compare the cost for 8xs test time augmentation against skipping "background" heuristic.)

Minor

(1) What is the incoming contrast range and bit depth?

(2) Stardist-3D's weakness is not that it requires convexity (it requires star-convexity) but that it picks one hypothesis leading to low-resolution outlines. This has been overcome by Starfinity (https://linkinghub.elsevier.com/retrieve/pii/S0092867421013398; https://github.com/multiFISH/EASI-FISH).

(3) Heatmap regression is not the same as distance regression; the manuscript does not explain what it is and uses terms interchangeably. This should be clarified. The reference for heatmap is 14; for distances, there are others, e.g. doi:10.1007/978-3-030-00934-2_36.

(4) Only one evaluation example compares against CellPose-SAM zero-shot; I would add this to all of them. The mentioned place switch would be interesting to see in a plot instead of text.

(5) "We replicated this failure on multiple machines." How does the machine matter here? Did the authors do cross-validation across different computers, instead of different random seeds? This sounds expensive!

(6) Brightness-based sampling could be achieved by augmentation?

(7) In the text "We use the following bicubic upsampling factors[...]", I think the authors mean tricubic, or cubic (because they upscale only one axis). Bicubic makes no sense, but people say this in the literature; we can do better. Why integer upscaling factors instead of exact ones? Are the authors concerned about that one incomplete border pixel?

(8) "Furthermore, it is not confined to Linux-based environments such as Segmamba [32], an important consideration given that biologists often work with Windows machines."<br /> This is confusing. Is this a comment about somebody's publicly available repository? This is not relevant to evaluate the method and should be discussed separately. Does it work in WSL?

(9) Downsampling by factors >2 with bicubic interpolation sounds wrong; should the authors use averaging?

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

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Reply to the reviewers

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

Summary:

In this manuscript, Sherman Foo and Buzz Baum report the development of a tryptophan auxotrophy-based selection system in S. acidocaldarius. Using classical pop-in and pop-out methodology, the authors isolated a strain ΔtrpBA using a rich medium BDN medium (Brock medium supplemented with NZ-amine, Sucrose and uracil and an uracil auxotroph. To get stringent selection, they developed a defined medium BDN, based on analysis of amino acid composition of NZ-amine A and other related substrates. They then analyzed the possibility to use 5-FAA for counterselection and found that 5-FAA did not appear to function as an effective counterselection agent. Next, they successfully constructed a tryptophan complementation system using the pSVAara plasmid backbone, replacing the pyrEF cassette with the trpBAD genes from Saccharolobus solfataricus (sso0888 -sso0890).

Exploiting both uracil and tryptophan auxotrophies, the authors further demonstrated the use of this system by dual-plasmid co-transformation and co-expression of the surface layer proteins and a dominant-negative mutant of the AAA-ATPase Vps4 and confirmed that the accumulation of surface layer lattice forming protein SlaA at the midzone of division-arrested cells together with its membrane anchor SlaB. The localization of SlaA and SlaB at the midcell was in agreement with the observations previously reported by the same group.

This is a good summary of our paper.

Major comments:

1) The dual plasmids differ only at the selection markers, pryEF and trpBA. The stability of them in one cell needs to be addressed.

Thank you for raising this point. We have now addressed plasmid stability by following the maintenance of both plasmids during growth under selective and non-selective conditions. As shown in our new figure Fig. S4C, a strain carrying both plasmids was first grown in selective BCS medium and subsequently transferred to BCS, BCS ura+, BCS trp+, or BCS ura+ trp+. Cultures were sampled after 10 and 20 generations and plated on selective medium to quantify plasmid maintenance.

As expected, the two plasmid were efficiently maintained under selection. When selection for either plasmid was relaxed by supplementation, plasmid loss increased progressively with the number of generations as expected. After 20 generations, approximately 5% of the initial CFU remained under BCS ura+, approximately 21% under BCS trp+, and approximately 14% under BCS ura+ trp+. Thus, both plasmids can be maintained together under selection, while their maintenance is reduced at a similar rate only when the corresponding selective pressure is removed. The presence or loss of one plasmid does not appear to affect the stability of the other.

2) Relevant to the above, the authors should test the plasmid stability after culture with reasonable generations. Is it possible to construct a stably transmitted dural plasmid with different ori?

We agree that an alternative plasmid architecture with a different origin of replication could potentially improve long-term plasmid maintenance. However, constructing and validating such a system would require the identification and testing of additional compatible origins of replication, including screening of available native or cryptic plasmids, followed by construction and characterization of new plasmid backbones in S. acidocaldarius. This would constitute a substantial plasmid-development study beyond the scope of the present work.

Importantly, the dual-plasmid experiment was intended primarily as a proof-of-concept demonstrating that the two selection systems can be combined in the same cell, rather than as a requirement for all applications of the toolbox. Where long-term maintenance of both selectable markers is required, an alternative strategy would be to incorporate the second selection marker stably into the genome. This is addressed in the discussion. We have therefore focused the present study on demonstrating the functionality and compatibility of the two selection systems, while experimentally characterizing the stability of the dual-plasmid configuration under selective and relaxed selection conditions (Fig. S4C).

3) Lines 214-223, I am curious why the authors used ΔtrpAB as the auxotroph instead of using ΔtrpF directly, because the latter could be easily subject to 5-FAA counter selection test.

Thank you for this question. As described earlier in the Results (revised manuscript line 120), we initially selected trpBA as the deletion target because we wanted to establish tryptophan auxotrophy without disrupting the production of upstream metabolic intermediates generated by other genes in the tryptophan biosynthetic pathway, such as trpF, trpE and trpD. In particular, indole-3-glycerol phosphate and other intermediates of this pathway can serve as precursors for the biosynthesis of secondary metabolites, including benzoxazinones and indole diterpene alkaloids.

More generally, the principle of the selection system is not restricted to trpBA or trpF. Other genes in an amino acid biosynthetic pathway could in principle be targeted, provided that the selected gene is non-redundant and its deletion produces the desired auxotrophic phenotype.

Minor comments:

1) Lines 71-84, please add an important reference, Zhao et al., Rational design of unrestricted pRN1 derivatives and their application in the construction of a dual plasmid vector system for Saccharolobus islandicus, 2024.

We thank the reviewer for this excellent suggestion. We agree that this study is highly relevant to our discussion of archaeal genetic tool development. We have now included this reference in the indicated section, highlighting the recent development and of a second stably maintained vector system for Sc. islandicus.

2) In the title, the spatial organization of S-layer assembly during cytokinesis has already been reported by the authors previously. The title could be improved by slight modification.

We have now updated the title to avoid overstating this aspect as a completely novel finding and to shift the focus to the selection system instead.

Reviewer #1 (Significance (Required)):

Archaea of the order Sulfolobales are model microbes for studying the biology of archaea and the origin and evolution of eukaryotic-like characteristics. Lack of sufficient selection markers has been a limitation for genetic analysis of these organisms. Although dual selection system has been developed in Saccharolobus islandicus, another model archaeon of Sulfolobales, there is no such system for Sulfolobus acidocaldarius.

The study by Foo and Baum explored a method for the formulation of defined Brock-based dropout medium, which enables stringent selection not only for trypan auxotrophic selection, but also will be potentially useful for other amino acid-based selection in general. Therefore, this study expanded the genetic toolkit available for S. acidocaldarius and provided additional evidence for spatial regulation of S-layer assembly during archaeal cytokinesis. The dual selection system was based the same plasmid backbone which could have problem in plasmid stability. Use of different compatible plasmid could improve the dual selection system. In general, the developed system will facilitate the study of cell biology and molecular biology using the model archaeon Sulfolobus acidocaldarius.

We appreciate the reviewer's clear summary and are glad that this new selection method will be a valuable asset to the archaeal cell biology community.

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

In this manuscript, the authors develop a new selection method in the model thermoacidophilic archaeon S. acidocaldarius that allows the simultaneous expression of two proteins of interest. Namely, they expressed either the S-layer proteins SlaA or SlaB fused to an HA tag simultaneously with a dominant negative Vps4 protein point mutant tagged with a His6 tag that allows cell cycle arrest. Using this technique, they go on to show that S-layer proteins accumulate at division site in dividing cells. The paper is well written, the data well presented, and the novel selection method will likely be a useful new tool in this model species for archaeal cell biology. However, a few points should be addressed to further support some of the claims made, convince readers of the usefulness of the new strain, and increase the overall clarity of the manuscript.

Thank you for this summary of our results. Below, we address each of the specific points raised to further support our claims and enhance the manuscript's overall clarity and utility.

Major points: - Line 115: Was any RT-qPCR or transcriptomics done to confirm that the expression of the downstream genes in the operon remained the same? - Line 227: Why express the trpBAD cassette if you only deleted trpBA? Does this mean you disrupted the expression of the downstream trpD gene (saci_1423) in the tryptophan biosynthesis operon?

To address both points, yes, RT-qPCR was performed to test the expression of the downstream trpD gene. We have now included this result in Fig. S3D.

We found that trpD expression was reduced but not abolished in the ΔtrpBA strain when compared to the wild-type strain DSM639. However, we also note that this is similar to the commonly used MW001 (ΔpyrE) strain, where the downstream pyrF gene expression was reduced compared to the wild-type strain. In both cases, complementation with the corresponding Sa. solfataricus gene(s) and the downstream gene (trpD or pyrF) was used to rescue its auxotrophic phenotype.

• Line 227: Why did you choose to complement with the genes from Sa. solfataricus instead of using the native genes from S. acidocaldarius? Please clarify.

This was done to minimize the risk of unwanted homologous recombination events between the expression vector and the host genome. Because the trpB 5’ UTR and trpD sequences are present on the plasmid backbone, using the native S. acidocaldarius sequence could lead to unintended recombination at these genomic flanking regions, destabilizing the system. We have now included this information in the text at line 230.

• Line 236: Why is the promoter so much leakier on pSF251-SlaA-HA vs. pSVAaraFX-SlaA-HA? pSF251 is a derivative of pSVAaraFX-HA so it seems strange that the promoter would behave so differently on the two plasmids. While the arabinose promoter is somewhat leaky, it should not be this leaky according to reference 22 and in comparison to the non-induced controls of pSVAaraFX-SlaA-HA. The high level of expression in the non-induced control suggests the slaA-HA gene is being constitutively expressed. This could potentially be driven by the promoter of trpBAD cassette you introduced if you did not add a transcription terminator downstream.
• Line 238: Why is the expression of SlaA-HA so much higher in BDM when using the pSF251-SlaA-HA plasmid vs. the pSVAara-Fx-SlaA-HA plasmid? It appears to express just as well as SlaA-HA did in BSN media when expressed on pSVAara-Fx-SlaA-HA. Do you think the promoter controlling the trpBAD casette is somehow driving stronger and more constitutive expression of genes downstream trpBAD?
• Line 243: The authors may want to re qualify this. While the system can support inducible protein expression, the existing plasmid seems to express genes constitutively even when they are placed under inducible promoters. While the expression does increase upon induction, it goes from "high" to "very high" rather than "low" to "high" which may not be readily useful in typical applications of inducible promoters.

Thank you for these comments. We have repeated and re-quantified the SlaA-HA expression experiments and believe that the apparent difference between pSF251-SlaA-HA and the parental pSVAaraFX-SlaA-HA construct is partly due to differences in Western blot presentation in the original manuscript.

Firstly, pSF251 is progressively lost when cells are propagated in the absence of the corresponding selection in BNS. This is also supported by our observation in Fig. S4C, following supplementation of tryptophan in BCS. Thus, reduced SlaA-HA signal in both the uninduced and induced BNS samples in Fig. 3D is likely to reflect loss of the pSF251 plasmid rather than intrinsically low expression from the construct.

Secondly, direct visual comparison of the original Fig. 3D with Fig. S2C is complicated by differences in Western blot exposure and contrast. In particular, the presentation of Fig. 3D was adjusted to make the relatively weak BNS signal visible, due to the point raised above. This more saturated presentation results in the impression that uninduced SlaA-HA expression with pSF251 in BDM may seem much higher than it actually is.

We therefore consider the quantified values to provide a more appropriate comparison than direct visual comparison of band intensities between the two figures. To further support this, we have now included re-quantified data using triplicate experiments to show the quantified relative expression with means ±SD indicated in Fig. 3D and S2C. The re-quantified data show that SlaA-HA expression from pSF251 increases approximately two-fold following arabinose induction, confirming that the construct remains arabinose responsive. Furthermore, the blot in Figure 3D has been replaced with a more representative image featuring lower saturation levels.

We also note that the magnitude of basal expression and the induction response can depend on the gene of interest and the properties of the encoded protein. The LacS protein used in previous characterization of the arabinose-inducible system is distinct from SlaA and may differ substantially in abundance and stability. A demonstration of this effect can be found in Fig. S4D, where the expression of SlaA and SlaB are significantly different, despite being expressed from the same plasmid. We have therefore avoided interpreting the basal expression observed with SlaA-HA as a universal property of the promoter system.

With respect to the possibility of transcriptional read-through from the introduced S. solfataricus trpBAD cassette, we did not include a transcriptional terminator downstream of the cassette and therefore cannot exclude a contribution from transcription originating at the trpBAD promoter. However, we have not directly tested this mechanism and have therefore avoided attributing the observed basal expression specifically to trpBAD promoter read-through.

Importantly, the primary purpose of pSF251 in this study is to introduce trpBAD as an alternative selectable marker, rather than to systematically characterize or optimize the arabinose-inducible promoter. Our data demonstrate that the resulting vector retains arabinose-responsive expression, while also highlighting that basal expression can be substantial and should be considered when selecting and optimizing constructs for individual applications. Alternative regulatory systems, including copper-, maltose- or xylose-responsive promoters, may provide additional options where tighter regulation is required, but systematic comparison of promoter systems is beyond the scope of this study. This caveat has now been included in the discussion.

We have therefore edited the relevant text to state that pSF251 supports arabinose-responsive protein expression, rather than implying that it provides a tightly regulated low-to-high induction system.

• Line 275: Since both plasmids have the same replication strategy as well as possessing extended regions of homology, one could wonder whether there are any issues with plasmids undergoing recombination with one another? Or if there are any issues with inheritance of the plasmids? While we certainly see cells that are positive for both proteins being expressed (an HA tagged S-layer protein and a His6 tagged Vsp4 protein), what is the percentage of cells that are positive for both? And how stable is this?

This concern was also raised by Reviewer 1. We have now included new data in Fig. S4C to show the co-maintenance of both plasmids under selective and non-selective conditions. These experiments demonstrate that both plasmids can be maintained together under selection, while plasmid loss occurs progressively when the corresponding selective pressure is relaxed. Please see our response to Reviewer 1 above for a detailed description of these experiments.

We have also examined simultaneous protein expression from the two plasmids at the single-cell level by flow cytometry. Specifically, we analysed strains overexpressing either SlaA-HA or SlaB-HA together with Vps4WkB-His6 (Fig. S4D). These experiments demonstrate that proteins encoded by the two plasmids can be expressed simultaneously in individual cells. However, the proportion of cells expressing each protein is dependent on the particular gene of interest. For example, SlaA expression is readily detected in the SlaA-HA/Vps4WkB-His6 strain, whereas SlaB expression is substantially lower in the corresponding SlaB-HA/Vps4WkB-His6 strain. Thus, the proportion of double-positive cells reflects gene-specific expression properties and cannot be considered a general characteristic of the dual-plasmid system.

Importantly, the flow cytometry measurements report protein expression at the single-cell level and do not directly establish the presence or integrity of both plasmids in each individual cell. We therefore consider the plasmid stability experiment in Fig. S4C to be the appropriate assay for assessing inheritance of the two plasmids, while the flow cytometry and Western blotting experiments (Fig. S4D, Fig 4A) demonstrate that simultaneous expression from the two plasmids is possible in individual cells.

• Line 379: Figure 3D actually shows the contrary (cells start to lose the pSF plasmid if grown in BSN). Please correct accordingly.

Thank you for pointing this out. Indeed in the original Results (line 238), we also explicitly noted that lower expression levels were observed in BNS, potentially due to loss of the pSF251 vector in the presence of tryptophan in the rich medium, which relieves selection pressure. This limitation is further clarified with the addition of the plasmid stability data in Fig. S4C.

Our intention in the statement at line 379 was not to suggest that pSF251 plasmids can be stably maintained during prolonged growth in BNS without selection. Rather, we intended to highlight the flexibility provided by having independent trpBAD and pyrEF selection systems. For example, the trpBAD marker can be used to select for genome-engineering events, while a pyrEF-based plasmid can subsequently be used for plasmid-based overexpression under conditions where higher protein yields are required. Conversely, the two selection systems can also be combined where simultaneous selection for a genomic modification and plasmid-borne construct is desirable.

To avoid confusion, we have now edited this section to, “The availability of independent trpBAD and pyrEF selection systems provides flexibility for combining genome engineering and plasmid-based approaches. For example, auxotrophic strains can first be selected under defined conditions using trpBAD, while pyrEF-based plasmids can subsequently be used for overexpression experiments requiring higher protein yields. The two selection systems can also be combined to enable simultaneous selection of genomic modifications and plasmid-borne constructs.”

• Line 407: How does SlaB contribute to the recruitment or stabilization of SlaA if SlaA is also enriched in the portion of the extended division bridge that SlaB is absent from? Please discuss.

We agree that our original wording could be interpreted as implying that SlaB is required for recruitment or stabilization of SlaA at the division midzone, which is not directly supported by our observations.

Our data show enrichment of SlaA or SlaB at the division midzone in division-arrested cells, consistent with the possibility that SlaB contributes to SlaA recruitment or stabilization, as suggested previously by the accumulation of exogenously added SlaA at the division bridge (Foo et al., 2025). However, as the reviewer points out, SlaA remains enriched within portions of extended division bridges where SlaB signal is reduced. Thus, SlaB is unlikely to be the sole determinant of SlaA localization at the division midzone.

One possibility is that SlaB is dynamically remodelled during division-bridge maturation. In cells with extended division bridges, SlaB signal appears reduced at the bridge midzone but enriched at the flanking regions, while SlaA remains enriched within the bridge. Alternatively, additional S-layer anchoring components, including Saci_1846 identified previously (Foo et al., 2025), could contribute to SlaA retention or organization independently of SlaB. Distinguishing between these possibilities will require further experiments.

We have therefore revised the text to present the contribution of SlaB to SlaA localization as a model rather than an established mechanism, and to acknowledge the possibility of additional or dynamically regulated S-layer anchoring mechanisms in the discussion.

Foo, Sherman, Ido Caspy, Alice Cezanne, Tanmay A. M. Bharat, and Buzz Baum. “A Self-Assembling Surface Layer Flattens the Cytokinetic Furrow to Aid Cell Division in an Archaeon.” Proceedings of the National Academy of Sciences 122, no. 25 (2025): e2501044122. https://doi.org/10.1073/pnas.2501044122.

-Figure 4: It is unclear what the sample size is for microscopy. If only N=10 cells were imaged in one single experiment for each strain, then this does not fit standard criteria for scientific reproducibility. Unless N=10 cells were imaged across multiple independent experiments (e.g. 3 or 4 cells in three independent experiments)? Either way, one would expect that more cells could be imaged and added to this analysis, especially given that the authors enriched for dividing cells in their assays. It is also important that cells be selected in a blinded fashion.

Thank you for raising this point. We have repeated the microscopy analysis and increased the sample size to 25 cells per strain, with three independent experiments performed. The revised analysis and corresponding figure have been updated accordingly.

Because the purpose of this analysis was specifically to examine S-layer organization at the division site, dividing cells were selected according to its morphology. Importantly, cells were first identified and selected using an the independent channel (ConA staining) without assessing SlaA/SlaB localization. Only after the cells had been selected were the SlaA/SlaB fluorescence channels examined and quantified. Thus, selection of cells for analysis was based on an independent marker of cell morphology rather than the S-layer localization phenotype being quantified. This approach also resulted in inclusion of cells with both short and extended division bridges. Consequently, the midzone enrichment of SlaB is less distinct in the population-level profile shown in Fig. 4E than for SlaA, reflecting heterogeneity in division-bridge morphology rather than selection based on the S-layer localization phenotype.

We have clarified this procedure in the revised Materials and Methods.

• Figure 4: "endogenous S-layer at the midzone": Here the authors image the localization of tagged, overexpressed copies of SlaA and SlaB, not endogenous proteins. Please correct.

We have now edited this phrase accordingly.

Minor points: - Line 145: While the cells clearly grow in the absence of added tryptophan, it appears that they have a more severe/noticeable growth defect when grown on solid vs. liquid media. Is there a reason why this might be so?

The more pronounced growth defect observed on solid media compared to liquid media may be due to differences in pH between the two cultivation formats, dictated by technical constraints in solid media preparation. Gelrite, the gelling agent used, fails to polymerize at the acidic pH of 3.0 at high temperatures, and is thus kept at a pH of 5.0, which imposes an additional stress on Sulfolobus cells.

• Line 153: have been > has been

We have corrected this typo accordingly.

• Line 216: Would 5-FAA not be expected to just abiotically isomerize into the product of trpF under the acidic media conditions?

This is an interesting hypothesis. However, the literature and our experimental data demonstrate that this is unlikely to be occurring.

Firstly, an older study has shown that anthranilic acid derivatives do not undergo spontaneous skeletal or positional isomerization in acidic environments. At highly acidic values (approximating pH 2), anthranilic acids are remarkably stable against complex structural modifications (Stevens et al., 1952). The introduction of a highly electronegative fluorine atom at the C-5 position is expected to further exert a powerful electron-withdrawing inductive effect on the benzene ring, protecting the aromatic ring against the electrophilic intermediates required for skeletal or positional rearrangements.

Second and more importantly, if 5-FAA were abiotically converting into a functional downstream tryptophan intermediate, this shortcut would bypass the genetic block in our ΔtrpF strain, rescuing its growth. Instead, we observe that 5-FAA is uniformly toxic to both the wild-type and the ΔtrpF strain (Fig. S3C). This lethality rules out abiotic conversion into a tryptophan intermediate or thermal degradation of 5-FAA. Instead, it indicates that 5-FAA possesses a toxicity mechanism in S. acidocaldarius that operates independently of the TrpF pathway. This phenomenon is precedented in hyperthermophilic archaea; for example, in Pyrococcus furiosus, deletion of downstream tryptophan biosynthesis genes similarly failed to yield 5-FAA resistance (Farkas et al., 2012).

Stevens, W. H., J. M. Pepper, and M. Lounsbury. “The Decarboxylation of Anthranilic Acid.” Canadian Journal of Chemistry 30, no. 7 (1952): 529–40. https://doi.org/10.1139/v52-065.

Farkas, Joel, Karen Stirrett, Gina L. Lipscomb, et al. “Recombinogenic Properties of Pyrococcus Furiosus Strain COM1 Enable Rapid Selection of Targeted Mutants.” Applied and Environmental Microbiology 78, no. 13 (2012): 4669–76. https://doi.org/10.1128/AEM.00936-12.

• Line 228: Was a transcription terminator added downstream of sso0890?

No. Please see above for the full response regarding transcriptional read-through and protein expression levels.

• Line 375: This is only true for one of the two plasmids. The expression is quite high on your pSF plasmid.

We agree that the original statement was too broad. We have rephrased the sentence to clarify that the response to arabinose induction is lower, rather than total expression levels.

Reviewer #2 (Significance (Required)):

S. acidocaldarius has previously been made accessible to genetic manipulation including in-frame markerless gene deletion and exogenous expression of proteins of interest from an expression vector, pSVA-AraFX, under the control of inducible promoters (arabinose, xylose, sucrose) that allow the timely expression of target proteins in the cell. Existing tools rely on uracil auxotrophy (i.e. the parental strain is deficient for uracil synthesis, and exogenous plasmid DNA carries the missing uracil synthesis gene, allowing selection of transformants). Here, the authors develop a tryptophan auxotrophy-based selection system in S. acidocaldarius by deleting the genes trpBA. They then modified the pSVA-AraFX plasmid by replacing the uracil synthesis genes pyrEF by the tryptophan synthesis genes trpBA, allowing double expression of proteins in S. acidocaldarius. The technique is used in the present work to show localization of S-layer proteins in dividing cells as a proof on concept. This novel selection method will likely be a useful new tool for archaeal cell biologists.

We thank the reviewer for their positive assessment and for recognizing the value of our tryptophan auxotrophy-based selection system.

---

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

The manuscript written by Foo and Baum describes the development of a tryptophan auxotrophy-based selection system for the archaeal model organism Sulfolobus acidocaldarius. The authors formulated a defined Brock-based dropout medium and demonstrated its use for tryptophan-based selection. They further combined this system with the established pyrEF marker to co-express two plasmid-borne constructs and used this approach to examine the localization of S-layer proteins in division-arrested cells.

The development of an additional selectable marker in S. acidocaldarius has great potential for sophisticated genetic analyses, including chromosomal marker exchange, simultaneous gene expression and complementation, and so on. I believe that this work is a valuable contribution to the Sulfolobus research community. Overall, the manuscript is clearly written, the experiments are generally well designed, and the results are clearly presented and discussed. I have several comments that I hope will help the authors strengthen the manuscript.

This is an accurate summary of our results.

Major concerns 1.The dual-plasmid system is one of the major advances claimed in this study. However, the two plasmids appear to share the same backbone and differ mainly in their selection markers. The compatibility and stability of the two plasmids within the same cells have not been adequately validated. The authors should evaluate the dual-transformation efficiency and plasmid retention over multiple generations under dual-selection conditions. Plasmid-specific analyses are also needed to confirm that both plasmids remain intact and to exclude potential recombination or rearrangement.

Thank you for the comment, this point was also raised by reviewers 1 and 2. We have now included new data in Fig. S4C to show the co-maintenance of both plasmids under selective and non-selective conditions. These experiments demonstrate that both plasmids can be maintained together under selection, while plasmid loss occurs progressively only when the corresponding selective pressure is relaxed. Please see our response to Reviewer 1 above for a more detailed description of these experiments.

2.I am not fully convinced that the current data support the authors' claim of stringent tryptophan-based selection. The spot assays do demonstrate that an established ΔtrpBA culture cannot grow on BDM without tryptophan. However, in Sulfolobus transformation, a spot assay is not equivalent to a transformation plating assay and does not directly demonstrate the performance of the selection marker during transformation. Although the authors present this approach as a further development of the S. acidocaldarius genetic system, they do not show representative transformation plates or report transformation efficiency, background colony formation, or false-positive frequency. These data are needed to establish the stringency and practical utility of the proposed selection system.

Thank you for raising this important point. We agree that the spot assays alone do not directly assess the performance of the trpBAD selection marker during transformation. We have therefore performed transformation plating assays and subsequently genotyped individual colonies to directly assess the stringency of tryptophan-based selection.

Specifically, we performed three independent transformations of and genotyped 15 colonies from each transformation. This was done for the case of single (trpBAD) and double (trpBAD and pyrEF) transformations, plated on BDM or BCS. These analyses allowed us to directly determine the frequency of genuine transformants among colonies recovered. We have now included the resulting false-positive frequencies in the revised manuscript (lines 234, 281 and 294). These results demonstrate that background colony formation under the selection conditions is low and provide direct evidence for the stringency and practical utility of the trpBAD selection system during transformation.

We have not presented CFU per µg DNA as a general transformation-efficiency metric. Although we recorded the number of colonies recovered following transformation, this value reflects not only DNA uptake but also recovery during the outgrowth period post electroporation and subsequent growth under selection. In addition, constructs containing different genes of interest can differ in plasmid size and in their effects on plasmid replication, copy number, gene expression, cellular fitness and recovery. Consequently, CFU per µg DNA would not provide a directly comparable measure of transformation efficiency across different constructs.

Instead, we have focused on the frequency of genuine transformants among colonies recovered under selection, determined by genotyping independent colonies. We believe this provides a more direct assessment of the parameter relevant to the reviewer’s concern, namely the stringency and specificity of the proposed tryptophan-based selection system.

Specific comments 1.The S-layer localization experiments provide a useful demonstration of the dual-selection system. However, the authors should clarify that SlaA and SlaB were examined separately in Vps4E209Q-arrested cells rather than simultaneously during unperturbed cytokinesis. Accordingly, terms such as "co-enrichment," "endogenous S-layer," and "spatial regulation" should be used with appropriate caution.

We have combed through the manuscript text and updated the terms accordingly to more accurately reflect the conditions and results presented in the paper.

2.The authors should provide additional information about key reagents, including the manufacturers and catalog numbers for casamino acids, tryptophan, Gelrite, and L-arabinose. This information is important for reproducing the defined and selective media, particularly because the composition of complex products such as casamino acids may vary among suppliers.

This information is now included in the Materials and Methods.

3.Plasmid sequences, annotated maps, primer sequences, and the complete BDM recipe should be deposited in a stable repository or provided as supplementary files. The statement that "all data are available in the manuscript" is not sufficient to ensure the reproducibility of a newly developed genetic system.

We have now included the annotated plasmid map and sequence of pSF251, and primer sequences used as supplementary files. The full BDM recipe can be found in the Materials and Methods, which we have now updated to include the full recipe for Brock media.

4.The sentence "The deletion of the arginine decarboxylase have been described" should be corrected to "Deletion of the arginine decarboxylase has been described."

We have edited this typo accordingly.

5.Figure S4C reports the percentages of HA-positive and His6-positive cells, but the gating strategy and negative controls used to establish the thresholds are not shown. Appropriate uninduced and single-expression controls should be included or described.

We appreciate the reviewer's request for clarity on the gating approach. Because the data are presented as a scatter plot, the boundary thresholds for HA-positive and His6-positive populations were established as a horizontal gate on the Y-axis, set directly above the wild-type parental control population. As noted earlier in the manuscript, the uninduced sample exhibits a degree of leaky/basal expression rather than a completely silent state. Because of this, the uninduced population displays a significant shift in fluorescence compared to the negative wild-type control. This is highly dependent on the protein of interest as can be clearly observed between the expression of the soluble SlaA-HA vs the membrane protein HA-SlaB (Fig. S4D).

As such, we chose to use the wild-type control to demonstrate the presence of the proteins of interest in this proof-of concept work. This Y-axis gate was positioned such that fewer than 5% of the negative wild-type control cells fall above the line. Because the fully induced populations exhibit an unambiguous upward shift in fluorescence intensity along the Y-axis, this clear boundary provides a highly reproducible separation between baseline cellular autofluorescence and protein overexpression.

We have added a statement to the Materials and Methods section to explicitly clarify this gating threshold rationale in light of the basal expression levels.

6.In line 227 and Figure 3A, why trpD was introduced into pSF251?

This point was raised by reviewer 2 as well, please see above for our full response. In short, RT-qPCR analysis (Fig. S3D) revealed that our ΔtrpBA deletion reduced downstream trpD expression. This was similar to what we found in the MW001 background strain where, pyrF expression was reduced following deletion of pyrE. In both cases, complementation was carried out with the corresponding Sa. solfataricus gene + the downstream gene (trpD or pyrF)

7.In line 268, I am not sure if "results not shown" should be allowed to use. The authors may need to rephrase these sentences or provide supporting data.

We have revised this section to remove the statement regarding reduced protein expression, which was not directly supported by data presented in the manuscript. In addition, we now provide direct evidence that the ΔtrpBA mutant can be efficiently selected in BCS as well (line 294).

Reviewer #3 (Significance (Required)):

Sulfolobus acidocaldarius is an emerging model archaeon for studying fundamental cellular processes. However, the limited availability of selectable markers restricts more sophisticated genetic analyses in this organism. The development of an additional selectable marker should facilitate chromosomal gene exchange and recombination, simultaneous gene expression and complementation, and experiments combining genetic perturbations with reporter constructs. This work therefore represents a valuable technical contribution to the Sulfolobus research community and may enable more advanced genetic and cell-biological studies in this important archaeal model.

We appreciate this supportive assessment of our work's significance.

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

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Referee #2

Evidence, reproducibility and clarity

In this manuscript, the authors develop a new selection method in the model thermoacidophilic archaeon S. acidocaldarius that allows the simultaneous expression of two proteins of interest. Namely, they expressed either the S-layer proteins SlaA or SlaB fused to an HA tag simultaneously with a dominant negative Vps4 protein point mutant tagged with a His6 tag that allows cell cycle arrest. Using this technique, they go on to show that S-layer proteins accumulate at division site in dividing cells. The paper is well written, the data well presented, and the novel selection method will likely be a useful new tool in this model species for archaeal cell biology. However, a few points should be addressed to further support some of the claims made, convince readers of the usefulness of the new strain, and increase the overall clarity of the manuscript.

Major points:

• Line 115: Was any RT-qPCR or transcriptomics done to confirm that the expression of the downstream genes in the operon remained the same?
• Line 227: Why express the trpBAD cassette if you only deleted trpBA? Does this mean you disrupted the expression of the downstream trpD gene (saci_1423) in the tryptophan biosynthesis operon?
• Line 227: Why did you choose to complement with the genes from Sa. solfataricus instead of using the native genes from S. acidocaldarius? Please clarify.
• Line 236: Why is the promoter so much leakier on pSF251-SlaA-HA vs. pSVAaraFX-SlaA-HA? pSF251 is a derivative of pSVAaraFX-HA so it seems strange that the promoter would behave so differently on the two plasmids. While the arabinose promoter is somewhat leaky, it should not be this leaky according to reference 22 and in comparison to the non-induced controls of pSVAaraFX-SlaA-HA. The high level of expression in the non-induced control suggests the slaA-HA gene is being constitutively expressed. This could potentially be driven by the promoter of trpBAD cassette you introduced if you did not add a transcription terminator downstream.
• Line 238: Why is the expression of SlaA-HA so much higher in BDM when using the pSF251-SlaA-HA plasmid vs. the pSVAara-Fx-SlaA-HA plasmid? It appears to express just as well as SlaA-HA did in BSN media when expressed on pSVAara-Fx-SlaA-HA. Do you think the promoter controlling the trpBAD casette is somehow driving stronger and more constitutive expression of genes downstream trpBAD?
• Line 243: The authors may want to re qualify this. While the system can support inducible protein expression, the existing plasmid seems to express genes constitutively even when they are placed under inducible promoters. While the expression does increase upon induction, it goes from "high" to "very high" rather than "low" to "high" which may not be readily useful in typical applications of inducible promoters.
• Line 275: Since both plasmids have the same replication strategy as well as possessing extended regions of homology, one could wonder whether there are any issues with plasmids undergoing recombination with one another? Or if there are any issues with inheritance of the plasmids? While we certainly see cells that are positive for both proteins being expressed (an HA tagged S-layer protein and a His6 tagged Vsp4 protein), what is the percentage of cells that are positive for both? And how stable is this?
• Line 379: Figure 3D actually shows the contrary (cells start to lose the pSF plasmid if grown in BSN). Please correct accordingly.
• Line 407: How does SlaB contribute to the recruitment or stabilization of SlaA if SlaA is also enriched in the portion of the extended division bridge that SlaB is absent from? Please discuss. -Figure 4: It is unclear what the sample size is for microscopy. If only N=10 cells were imaged in one single experiment for each strain, then this does not fit standard criteria for scientific reproducibility. Unless N=10 cells were imaged across multiple independent experiments (e.g. 3 or 4 cells in three independent experiments)? Either way, one would expect that more cells could be imaged and added to this analysis, especially given that the authors enriched for dividing cells in their assays. It is also important that cells be selected in a blinded fashion.
• Figure 4: "endogenous S-layer at the midzone": Here the authors image the localization of tagged, overexpressed copies of SlaA and SlaB, not endogenous proteins. Please correct.

Minor points:

• Line 145: While the cells clearly grow in the absence of added tryptophan, it appears that they have a more severe/noticeable growth defect when grown on solid vs. liquid media. Is there a reason why this might be so?
• Line 153: have been > has been
• Line 216: Would 5-FAA not be expected to just abiotically isomerize into the product of trpF under the acidic media conditions?
• Line 228: Was a transcription terminator added downstream of sso0890?
• Line 375: This is only true for one of the two plasmids. The expression is quite high on your pSF plasmid.

Significance

S. acidocaldarius has previously been made accessible to genetic manipulation including in-frame markerless gene deletion and exogenous expression of proteins of interest from an expression vector, pSVA-AraFX, under the control of inducible promoters (arabinose, xylose, sucrose) that allow the timely expression of target proteins in the cell. Existing tools rely on uracil auxotrophy (i.e. the parental strain is deficient for uracil synthesis, and exogenous plasmid DNA carries the missing uracil synthesis gene, allowing selection of transformants). Here, the authors develop a tryptophane auxotrophy-based selection system in S. acidocaldarius by deleting the genes trpBA. They then modified the pSVA-AraFX plasmid by replacing the uracil synthesis genes pyrEF by the tryptophan synthesis genes trpBA, allowing double expression of proteins in S. acidocaldarius. The technique is used in the present work to show localization of S-layer proteins in dividing cells as a proof on concept. This novel selection method will likely be a useful new tool for archaeal cell biologists.

Author response:

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

Note from the authors:

During review of the proofs and re-confirmation of all models and outcomes, we discovered that in the current version of the manuscript, the identity of the lagged time series in the exploratory cross-correlation analysis was misreported. In the cross-correlation plot (Fig. 4d), the posterior alpha time series was fixed and the frontal theta time series was lagged by the times indicated on the x-axis, not vice versa. The inset figures depicting the timeseries will be corrected accordingly in the Version of Record. The subsequent mediation model, in which we tested whether attention mediates the relationship between mnemonic prediction strength and cognitive control, was included as a follow-up to the previously reported cross-correlation outcomes and will therefore be removed. As noted in the Version of Record, the corrected interpretation of the temporal ordering is that in response to a strong mnemonic prediction error, increases in cognitive control precede increases in attention.

Public Reviews:

Reviewer #1 (Public review):

Summary:

This manuscript describes a multi-modal study of associative learning and memory in humans, that combines scalp EEG, pupillometry and behavioral analysis to explore the construct of mnemonic prediction errors (MPEs), in terms of their relationship to attention and cognitive control. Across two pooled studies, participants performed associative memory tasks in which they learned the relationship between a cue word (action verb) and subsequent picture (animate or inanimate) with a strong vs. weak (4 or 1 repetitions) encoding manipulation. At test, participants were encouraged to generate a prediction following the cue word to determine whether the subsequently presented picture was a match or mismatch.

The timecourse of pupillary responses during match decisions were decomposed using temporal principal components analysis, which identified 6 distinct and overlapping processes. Some of the components (PC3/PC4) exhibited sensitivity to both the strength and mismatch conditions, as well as behavior (both RT and accuracy) and retrieval success on the subsequent trial. Furthermore, relationships were also observed between pupillary responses (specifically for PC4) and both frontal theta and posterior alpha power measures obtained from scalp EEG in Experiment 2, as well as for frontal theta and subsequent learning from mismatch stimuli (assessed using subsequent memory findings from a surprise recognition test). The authors suggest the findings indicate that MPEs elicit changes in attention, arousal and cognitive control which impact subsequent learning.

Strengths:

This manuscript has many strengths, including a clever study design, thoughtful integration of multiple neurocognitive measures, and a set of rigorous and technically sophisticated analyses, which reveal a large set of relationships among the measures and behavior. The findings demonstrating brain/physiology-behavior relationships are particularly important, in that they point to potential functional consequences of MPEs.

Weaknesses:

The technical proficiency and complexity of the study and analysis also presents a clear limitation and challenge for interpretation. It is likely that readers, even those that are quite knowledgeable about the methods, constructs, and questions being addressed will often struggle (as this reviewer did) to keep the large set of findings in mind and gain understanding of how they all fit together.

Indeed, it seems like there many threads running together in the paper which make it challenging to find the through-line of the key findings. The authors do address some of the key questions motivating the paper in the Introduction, but the results are somewhat ambiguous with regard to the primary question of the study as to whether the detection of MPEs leads to interaction among cognitive control, attention, and arousal. To their credit, the authors tackle this question through both cross-correlation and formal mediation analyses, and summarize these in diagrammatic figures (Figure 3, Figure 6). Yet it is not resolved whether the results represent a clear answer pointing to independence, or rather a lack of statistical power, or ill-resolved formulation of the mediational relationship. In particular, the cross-correlation suggests that posterior alpha suppression in response to MPEs does precede frontal theta, yet this indirect relationship does not explain the variation in trial-by-trial RTs on mismatches. This suggests a potential model misspecification.

In addition to the primary interaction issue mentioned above (between cognitive control, attention & arousal), the Introduction lays out a number of claims:

(1) That pupil size will be more sensitive to strong than weak MPEs.

(2) That MPE-linked increases in attention (indexed with posterior alpha suppression) and arousal (indexed with pupil size) will be linked to learning.

(3) That MPE learning will vary as a function of prediction strength.

Given the focus on learning, it is somewhat surprising that learning is not included in the mediation models. As the authors indicate in the Discussion, the use of trial-by-trial RT variation to drive the mediation model might be problematic, given that the RTs are sensitive to a range of factors beyond mnemonic prediction strength and also are under competing pressures (longer for mismatches than matches, due to surprise-linked slowing, but also faster following stronger rather than weaker mnemonic predictions). Thus, an alternative possibility might be to use trial-by-trial recognition of mismatches as the outcome variable in mediation models rather than trial-by-trial RT as the independent variable.

A large component of the results (Sections 2 and 3) is devoted to analyses of cue-linked pupil and EEG processes that putatively reflect mnemonic predictions (i.e., occurring before picture probes are presented and match/mismatch detection, i.e., MPEs occur). Yet these Results and the subsequent pupillary PCA components (PC1 and PC5) that are elicited are not well-integrated with the primary themes of the paper or the causal hypotheses. One finding that does seem to figure prominently (in that it is mentioned in Abstract, Introduction & Discussion) relates to the amount of attention allocated to the mnemonic prediction generation. Yet this finding is not well emphasized in the Results themselves. Possibly it refers to the negative relationship between posterior alpha during memory retrieval and the magnitude of pupillary PC3 component, described in Section 3. But it was quite challenging to identify amongst the wealth of results described in this Section as well as the others. More generally, the large amount of findings described across all four lengthy Results sections makes it challenging for readers to discern what are the key ones that the authors would like to highlight.

It is recommended that the authors do another pass through the paper to better highlight the most critical findings that they want to emphasize or which are most interpretable from a mechanistic and causal flow perspective and then de-emphasize or move other findings to the Supplemental Materials. Although the authors are to be commended for such a rigorous and comprehensive set of analyses, there are so many of them and findings, that the key points get buried and the reader needs to struggle potentially unnecessarily to identify the key take-away points.

We thank Reviewer 1 for the helpful feedback on how the manuscript can be further strengthened. We recognize that the rich set of findings can overwhelm the reader, resulting in difficulty discerning the main take aways about the effects of mnemonic prediction errors. We particularly appreciate Reviewer 1’s encouragement to restructure the manuscript so as to focus on the findings reported in Sections 1 and 4 of the original revision; the current revision now focuses on these key observations.

As part of this restructuring, Reviewer 1 also proposed moving the content from Sections 2 and 3 of the original revision to the Supplement. We agree with the Reviewer that the questions addressed in these sections on retrieval-related processes are not the main focus of the paper, but that they are informative in their own right. To avoid their getting lost in the Supplement, we decided that these results would be better served in a separate manuscript and thus we have removed them entirely. 

We acknowledge in the revised manuscript that the mediation and cross-correlation analyses were exploratory and that these specific analyses may not be well powered in the current experiments. With respect to Reviewer 1’s concerns about the specification of the mediation models, we were motivated to test whether MPEs trigger an increase in cognitive control that in turn, triggers an increase in attention and/or arousal (Fig. 4a); as such, we designed the model to assess whether, on strong MPE trials, frontal theta mediates the relationship between prediction strength and attention/arousal. As noted in the manuscript and raised by Reviewer 1, mismatch RT here is an imperfect measure of trial-level prediction strength. Future experiments that selectively elicit strong MPEs and have a more controlled measure of trial-level prediction strength may be better equipped to address these questions about interactions between control, attention, and arousal. We agree with Reviewer 1 that models assessing subsequent memory as an outcome would be desirable. However, given that (a) we did not find strong evidence for interactions at the time of a strong MPE and (b) we only observed a relationship between frontal theta and subsequent memory (but not posterior alpha or pupil), subsequent memory mediation models do not appear to be well justified. Altogether, these findings illuminate open avenues for future research.

Reviewer #2 (Public Review):

Summary:

The authors studied cognitive control and attention in response to mnemonic prediction errors (MPEs): situations in which the external reality violates internal memory-based predictions. The behavioral task first established strong versus weak predictions, and then either confirmed or violated these predictions. The authors examined markers of cognitive control (frontal theta) and attention (posterior alpha suppression, pupil response) while strong and weak predictions were confirmed or violated. They found increased cognitive control (frontal theta) for strong MPEs, which correlated with subsequent memory. Markers of attention (alpha suppression, pupil response) also accompanied strong MPEs but did not correlate with subsequent memory.

Pupil response was investigated using an interesting approach that decomposes the response into different components, finding that different components respond earlier or later and show different correlations with MPEs and their strength. The authors also investigated how EEG, reaction time, and pupil responses correlated with one another, providing further insight into the mechanism underlying the response to MPEs. Together, the study points toward multiple control and attention mechanisms involved in MPE response and memory.

Strengths:

The study has a clear behavioral paradigm with multiple measures — behavioral, EEG, and pupillometry — that offer an investigation into different aspects of MPE response and memory.

The study is also very comprehensive in looking at multiple phases in processing MPEs: the prediction phase (prior to the violation), the response to MPEs, and subsequent memory of MPEs, all within one study. Specifically, the link between neural mechanisms and subsequent memory is a major advancement, as most prior studies did not include this component. Mechanisms underlying subsequent memory of MPEs are theoretically important, as a primary function of MPEs is to promote learning and memory. As the authors mention, the different neural and pupillary signals are not robustly correlated, suggesting multiple mechanisms underlying MPE detections, which is interesting, offers avenues for future research, and can facilitate a better theory of how MPEs are processed in the brain. Finally, the decomposition of pupil response into different components and their correlation with behavior (RT during match/MPE detection) is interesting.

Weaknesses:

The methods are rigorous, and the data support the claims. The weaknesses are minor and are offered here as avenues for future research.

(4) The relationships the authors find between brain measures and pupil components were largely not specific to mismatches/matches. Thus, the specificity of this relationship is untested.

(5) The results with subsequent memory are important and address a major gap in the field that largely did not relate neural effects of MPE to subsequent memory. However, one major limitation of the study is that the authors did not test memory for matches. I understand the logic of avoiding testing matches. Because matches were repeated more times in the study, it’s not a fair comparison and could change participants’ overall criterion for old/new decisions. Future research could address this, e.g., by testing weak matches or potentially using a between-subject design.

We appreciate Reviewer 2’s helpful feedback during the review process and encouraging comments on the strengths of the manuscript. We agree and note in the revision that it would be illuminating for future studies to contrast memory for events that violate and confirm mnemonic predictions.

Comments on revised version

The authors addressed all my concerns. I appreciate the authors’ thoughtful and detailed response.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

It was challenging to read the paper with key findings happening at the time of the MPE presented first, and then to go “backwards in time” to examine process that occurred at preceding time periods (i.e., prior to probe presentation), and then again forward in time to examine learning related processes.

(1) Restructuring the Results

In this regard two distinct recommendations are made:

- Move Sections 2 and 3 to Supplemental Materials, to maintain the focus on the key findings related to detection of MPEs and their effects on subsequent learning.

- An alternative structure would be to present the cue-locked findings first, which relate to mnemonic predictions, then to those that occur when those predictions get violated, and finally to the learning process that occur following MPEs and which can be detected with subsequent recognition tests.

We thank the Reviewer for this encouragement to restructure the manuscript. To address concerns regarding the density of the paper and the cohesiveness of the findings, we removed the content that was in Sections 2 and 3 of the original revision. We will publish those results in a separate paper with additional analyses to more directly address previously raised questions regarding the mechanisms indexed by frontal theta and posterior alpha at the time of retrieval.  

(2) Integration of the summary figures

At the minimum, a recommendation would be to better integrate Figure 6, and maybe various versions of Figure 3, earlier into the text, preferably even in the Introduction, and then repeatedly refer to them throughout the results. For example, in Figure 6, linking the leftmost panel of the figure to Sections 2 and 3 is critical, and the righthand panel to Sections 1 with the rightmost part related to learning explicitly linked to Section 4.

We moved the summary figure up to now be Figure 1; we reference this figure in the Introduction and throughout the manuscript; and we additionally make reference in the figure to the association between frontal theta and PC3 at the time of a strong MPE as well as the cross-correlation outcome. We hope these modifications further aid the reader in identifying the main findings of the manuscript.

(3) Specification of the mediation models

Additionally, for the mediation models it is quite unclear why mismatch RT is treated as the index of MPE magnitude, as this seems to be where the problem may lie in model fitting. Why not think of this as an outcome variable (since would seem to be a causal outcome of the underlying functional processes elicited by mismatch detection)?

We thank the reviewer for these thoughtful comments. Our goal in designing the mediation models in Fig. 4a-c was to test our hypothesis that strong MPEs trigger an increase in cognitive control that, in turn, triggers an increase in attention and/or arousal; thus, attention/arousal should be the outcome and cognitive control should be the mediator. Given that increases in attention and cognitive control were selectively observed for strong and not weak MPEs, the models were restricted to strong MPEs. We therefore needed a trial-level measure of MPE magnitude to determine whether stronger MPEs in the strong condition elicit greater attention/arousal by engaging more cognitive control. As such, we decided to use mismatch RT as a proxy measure of MPE magnitude; we acknowledge in the text that this measure is imperfect. While a model with mismatch RT as the outcome variable is possible, the relative timing of the attention/arousal effects (which largely occur following responses) would render interpretation to be more challenging. Had stronger evidence of indirect effects emerged in Figs. 4b-c, we could have conducted model comparison with RT as an outcome. We acknowledge in the text that these analyses were exploratory and characterization of potential indirect effects will require more data and a more precise measure of MPE magnitude.

Alternatively, examining trial-by-trial recognition memory of mismatches as the relevant outcome variable would also seem to capture the functional process of interest. In this regard, have the authors examined whether trial-by-trial RT on mismatches predicts subsequent recognition of these items? If this direct relationship holds, it could be a target for mediation analyses in itself.

We agree with the reviewer that in theory, a mediation model predicting subsequent memory would be a desirable test of an integrated model of the mechanisms underlying MPE-driven learning. However, the mediation analyses conducted to address the functional relationships at the time of a prediction error (Fig. 4) are not well-powered to begin with; this limitation is raised in the Results and the Discussion. A mediation model predicting subsequent memory would be similarly underpowered; given that there is not strong evidence for indirect effects at the time of a strong MPE, and that only frontal theta – and not posterior alpha nor pupil – predicts subsequent memory, we think that such a mediation model is not well justified to include. Such a model should be more directly tested by well-powered designs in future studies.

(4) Hippocampal theta in the Introduction

The Introduction discusses hippocampal theta as well as frontal theta yet also makes clear that the former is not really well-detected or analyzed using scalp EEG. Consequently, a recommendation would be to remove this paragraph from the Introduction, since it can be misleading and a “red herring” for the reader, and instead only bring up this point in the Discussion section, as a pointer to the need for future research using methods that may be more sensitive to hippocampal interactions with PFC regions.

We appreciate this point and moved discussion of the hippocampus from the Introduction to the Discussion.

I think this shows how easily stereotypes can influence the way people see themselves and others. By telling the children that one eye color was smarter and worked harder than the other, Elliott showed how people can be judged based on a physical characteristic instead of their actual abilities. I believe this is unfair because eye color has nothing to do with how intelligent or hardworking someone is. This also shows how quickly people may treat others differently when they believe one group is better than another. It reminds me that we should get to know people as individuals instead of making assumptions based on their appearance.

Author response:

[Editors’ note: An Expression of Concern has been published for this article. The authors’ responses submitted during revision have been appended for further context]

eLife Assessment

This study provides a useful inventory of genes that are up- or down-regulated during the early metamorphic development of male and female larvae and proposes that the microRNA cluster miR-277/34 is involved in the development of sexual differences during early metamorphosis of Drosophila melanogaster, although its precise role remains unclear. The strength of evidence, based on a combination of diverse methods including mRNA and small RNA sequencing, in silico analyses, in vitro assays, and loss-of-function experiments, is incomplete as it lacks a general model and an examination of the potential effects of the miR-277/34 mutations on phenotypes such as morphology or developmental time. This work will be of interest to developmental biologists interested in sexual dimorphism and in the interplay between hormones and microRNAs during development.

We thank the editor and reviewers for the positive and constructive comments and suggestions. Point-to-point responses are listed below.

Reviewer #1:

Summary:

In this paper, Li and colleagues have found mircoRNAs that affect levels of metamorphosis-regulating genes that can also affect levels of sesquiterpenoids (juvenile hormone and related compounds) and ecdysteriods, which regulate the timing and stages of insects, respectively. They first compared the transcriptomes of Drosophila at the third larval instar and at the white pre-pupa stage. They found thousands of differences in gene transcript levels between males and females, and between the two different stages. Among those genes that were differentially regulated they saw that genes involved in insect hormone biosynthesis were disproportionately represented. Many of the differentially regulated genes were involved in the insect hormone biosynthesis pathway and ascorbate and alderete metabolism. MicroRNAs were also differentially expressed during metamorphosis and were separately identified. The authors then considered genes and whether the differentially expressed microRNAs might regulate transcripts known to be involved in sesquiterpenoid production. In silico analysis of microRNAs predicted a list of 17 microRNAs that can regulate transcripts of sesquiterpenoid biosynthesis genes. The authors then used an in vitro luciferase assay to validate the binding and downregulation of 10 of the microRNAs to genes involved with sesquiterpenoid production in S2 cells.

Li and colleagues then focus on two genes they found were bound by microRNAs that have established roles in metamorphosis. The microRNAs miR-34 and miR-277 bind transcripts of two protein-coding genes that regulate metamorphosis Kr-h1, which encodes a transcription factor that is a JH-inducible transcription factor, and Allatostatin C Receptor 1, (AstC-R1), a G-protein coupled receptor that regulates the corpora allatum, the gland that produces sesquiterpenoids. Using a LAMP assay, one of the microRNAs, miR-277 was shown to bind to both AstC-R1 and Kr-h1 in in vivo whole-animal extracts. There is no mention of binding between either protein-coding transcript and the miR-34 microRNA. Temporal expression of all four transcripts shows that their abundance is anti-correlated; stages of high miR-34 or miR-277 expression correlate with low AstC-R1 or Kr-h1 expression. Homozygous deletions of both mircroRNAs result in 23% lethality, five days after adult eclosion. The authors also generated specific mutants in miR-34 or miR-277 and find differences in the expression of AstC-R1 and Kr-h1 and sex-specific differences in both sesquiterpenoids and ecdysteroids in the knock-out lines. If there were phenotypes associated with the specific knock-outs, those were not mentioned. Next, the authors examined the transcriptomes of the miR-3277 and miR-34 mutants and found several other GO-terms enriched among the differentially expressed genes. However, the sesquiterpenoid pathway and ascorbate and alderete metabolism are not listed.

Strengths:

This is an interesting manuscript that could make an important contribution to our understanding of the roles of micro RNAs at metamorphosis, and potentially of how sex-specific differences arise during metamorphosis. Strengths of the paper include the functional validation of microRNA binding, in vitro and in vivo-, as well as the characterization of sesquiterpenoid and ecdysteroid titers. The authors have also used CRISPR to generate specific knock-outs of miR-34 and miR-277. The transcriptomes will be a resource for future work to mine for differences in gene expression during metamorphosis.

Weaknesses:

(1) Spatial Expression of miR-34 and miR-277. If miR-34 and miR-277 regulate AstC-R1 and Kr-h1, then they must be expressed in the same cells. Although the authors show that the microRNAs do bind to the transcripts of AstC-R1 and Kr-h1 in S2 cells, and miR-277 binds AstC-R1 and Kr-h1 in vivo whole-animal homogenates, we do not know if the microRNAs are ever in the cells where AstC-R1 or Kr-h1 are expressed. AstC-R1 is only expressed in a few cells in the brain, so it is not at all certain that it is co-expressed with either microRNA. The creation of enhancer lines or in situ hybridization in Drosophila is straightforward and would sort this out.

We thank the reviewer for the positive and constructive comments. We agree with the reviewer, and have pointed out the limitation in the main text as follows:

Lines 307-309 - “Further exploration of the spatial expression between miR-277, miR-34, Kr-h1 and AstC could bring new insights to the regulatory effects they have during metamorphosis”.

(2) Phenotypes. Although a double deletion was used and specific knock-outs of both miR-34 and miR-277 were generated, the analysis of the mutants is very superficial. For the homozygous deletion of both microRNAs miR-34 and miR-277, only a decrease in survivorship was observed a full six days after adult eclosion - after the end of metamorphosis. No phenotype for either miR-34KO or miR-277-KO was given. The authors cite the work of others who have found specific phenotypes after manipulation of sesquiterpenoids or ecdysteroids, like Riddiford and Ashburner, but do not use any of these many studies to help them characterize the phenotype. If the loss of miR-34 and miR-277 affects so many pathways (including MAPK signaling, TGF-beta signaling, FoxO signaling, and Wnt signaling), as well as global titers of metamorphic hormones, then there shouldn't there be something different in the development to discuss?

We thank for reviewer for pointing out the phenotypes. We did not detect morphological or developmental abnormalities during larval-pupal transitions in the different knockout mutants, and have now included the previously established research on miR-34 in the main text, shown as follows:

Lines 305-307 - “MiR-34 has been documented to maintain the neural proteostasis while suppressing age-associated decline (Liu et al. 2012; Kennerdell, Liu and Bonini 2018; Srinivasan, Tran and Bonini 2022).”

(3) I think the reliance on GO term enrichment is getting in the way of biology. For instance, I would not describe Kr-h1 as a sesquiterpenoid biosynthesis pathway gene. Yet the authors say they were motivated to examine microRNA regulation of Kr-h1 because they saw differences in levels of the sesquiterpenoid biosynthesis pathway between WL3 and WPP, a period which also saw differences in expression of some microRNAs. I understand that Kr-h1 expression is regulated by JH, a sesquiterpenoid, but it is not directly involved with JH production, so relying on GO term enrichment has made the decision to focus on Kr-h1 feel arbitrary.

We have stated out the rationale and rephrased that Kr-h1 as sesquiterpenoid responsive gene in relevant sentences in the Results, shown as follows:

Lines 135-145 - “Utilising an established cell culture dual-luciferase reporter assay (Hui et al 2013); we have validated 7 microRNAs (miR-8, miR-277, miR-958, miR-1000, miR-1002, miR-2283, miR-2280) that can downregulate the expression of Drosophila genes involved in JH synthesis, responsive, or signalling genes to varying degrees, including allatostatin C (AstC), allatostatin C receptor 1 (AstC-R1), allatostatin C receptor 2 (AstC-R2), Krüppel homolog 1 (Kr-h1), Chd64, juvenile hormone binding protein (JHBP), juvenile hormone diol kinase (JHDK) and juvenile hormone esterase (JHE) (Figure 1C). Among these genes, Kr-h1 or Kruppel homolog 1, is a JH-dependent transcription factor (responsive gene), and have been found to be regulated by another microRNA in cockroaches (Lozano et al 2015); while AstC-R1 or allatostatin C receptor 1, is a G-protein coupled receptor for neuropeptide allatostatin C which regulates juvenile hormone synthesis (Stay and Tobe 2007).”

(4) The transcriptomes of miR-34 and miR-277 should have revealed genes encoding members of the sesquiterpenoid biosynthesis pathway as well as AstC-R1 and Kr-h1, but neither was mentioned. The functional tests of miR-34 and miR-277 were performed because they were shown to affect the levels of expression of genes in the sesquiterpenoid biosynthesis pathway. Figure 2 shows a significant decrease in AstC-R1 and Kr-h1 transcripts after the loss of miR-34 and miR-277. However, the results do not mention either (Lines 250-264). Instead, there is a list of 10 different GO terms (like arginine and proline metabolism or fatty acid degradation) that were enriched in miR-34 and miR-277 transcriptomes. If any of those ten types have any relationship to Kr-h1, AstC-R1, or metamorphosis, that has not been explained.

We have now explicitly stated that Kr-h1 is significantly downregulated in the miR-277-KO transcriptomes consistent with our qPCR validation, as well as the transcriptomic analyses were used to understand genome-wide changes, shown as follows:

Lines 211-217 - “Among these differentially regulated genes, Kr-h1 was significantly downregulated in the miR-277-KO mutants (Supplementary Table S2), consistent with our qPCR validations (Figure 2B). On the other hand, AstC-R1 was not classified as differentially regulated based on the in silico analyses threshold of the whole-body RNA-seq data, and whether this was due to its restricted expression in a small subset of brain neurons would require further experiments to differentiate between different scenarios.”

Lines 255-259 - “It implies that miR-277 could have conserved regulatory roles of sesquiterpenoid and related pathways, and also divergent roles between sexes during metamorphosis with signaling pathways associated with cell proliferation, wing development, nutritional support, and endocrine regulation (Pan et al 2018; Jiang and Edgar 2009; Gibbens et al 2011; Toyama et al 2014).”

(5) Not enough care was taken in describing the stages. The methods describe wandering larvae (WL3) and white pre-pupa (WPP) for the transcriptomes, but in the text, different terms are used, like "larva", "pupa" and "L3 larvae instars" "early pupae" "late L3". Also, it seems like the small RNA libraries for sequencing were taken from "L3 larvae", but the stage of the L3 larvae was not mentioned. Staging is important, especially during metamorphosis, since differences in expression are expected to exist between different stages of L3, between early vs late wandering, and between WPP and early pupal stages.

We thank the reviewer for highlighting the importance of staging clarity, and have now revised both the Results and Methods to ensure all stages are defined explicitly and used consistently throughout the manuscript. In our dataset, all references to “L3 larvae” or “larva” correspond specifically to wandering third-instar larvae (WL3) which that have exited the food, display 1/3 to 1/4 gut contents, and show protruding anterior spiracles. All references to “pupa”, “pre-pupa”, or “early pupae” refer to white prepupae (WPP), defined as immobile individuals with fully everted spiracles and no movement when gently probed.

Recommendations:

(1) Lines 171-173. The genotype of the deletion line is given, but what is the genotype of the flies that were used? Were the balancers and chromosomes with mutations included in the analysis? I cannot tell from the description.

The miR-277-34-KO line was used and significant decrease in survivorship was observed in double knockout line. The information is now included as follows:

Lines 158-164 - “In the homozygous loss of function of miR-277/34 cluster fly (w[*]; Df(3R)mir-277-34-KO, TI{w[+mW.hs]=TI}mir-277-34-KO/TM3, P{w[+mC]=GAL4-twi.G}2.3, P{UAS-2xEGFP}AH2.3, Sb[1] Ser[1]; Chen et al 2014), we found that the heterozygous knockout individuals displayed low to almost no lethality, while the survivorship for the double knockout flies fell significantly with 77% of the double knockout flies dying within five days after eclosion (Figure 2A).”

(2) The introduction and discussion are too broad. I would expect some information about what is happening to ecdysone and juvenile hormone titers during metamorphosis. Additional detail should be given to the regulation of the corpora allatum, since the Ast-C1 gene and sesquiterpenoid levels were a major part of the results. I had hoped the discussion would help to synthesize the details within the results, particularly the differences between sexes. Instead, the discussion is very general, citing other papers that are related, but without tying the results within those papers to specific results in this paper.

We thank the reviewer. The following information is now included in the main text:

Lines 47-53 - “Multiple ecdysone titre peaks were observed during Drosophila development with each pulse corresponds to a developmental transition (Kannangara et al., 2023; Scanlan et al., 2023). For instance, there are one small and another big one triggering wandering in larvae and pupariation, respectively. For sesquiterpenoid juvenile hormone, its titre in corpora allatum changes in different developmental stages (Zhang et al., 2022) and generally decreases closer to the end of larval stages for pupariation (Dubrovsky 2005).”

(3) I found the text to be unclear, and important details were missing. There are many different cases where titers or gene expression went up or down, in males or females, but it is difficult to understand if these were expected or not, or what to make of all the differences. I also do not have a clear idea of what the hypothesis is. I had thought that the microRNAs were promoting the degradation of AstC-R1 or Kr-h1, so their loss should result in higher levels of AstC-R1 or Kr-h1 transcripts. However, Figures 2B and C show that there are lower levels of AstC-R1 and Kr-h1 transcripts in the loss of either miR-34 or miR-277. How does this fit with what is known of the progression of metamorphosis? A model built from the results to this point could help to organize the text.

The following information is now included in the main text, shown as follows:

- Lines 172-177 - “We then compared the expression of Kr-h1 and AstC-R1 of miR-277-KO, miR-34-KO, and between KO mutants and wild type flies using quantitative real-time PCR. The expression level of Kr-h1 was found to be significantly downregulated in both sexes of WL3 and WPP miR-277-KO mutants, coherent to the RNA-seq results; whereas a reduction was only noted in the male WL3 for miR-34-KO mutants but not in RNA-seq (Figure 2B; Supplementary Table S2).”

- Lines 178-186 - “On the other hand, expression level of AstC-R1 determined by real-time PCR was found to be upregulated during metamorphosis in wild-type (w1118) flies, but not for either miR-277-KO or miR-34-KO mutants (Figure 2C; Supplementary Figure 6). This is in agreement with the transcriptomic analyses where AstC-R1 was only up-regulated during male and female metamorphosis in the wild-type fly (Supplementary Table S2). In addition, we also found that the expression level of AstC-R1 in WPP of both miR-277-KO and mir-34-KO flies were significantly different to that of the w1118 flies (Figure 2C). Together, these data demonstrated that Kr-h1 and AstC-R are stage-specifically regulated by miR-277/34 in vivo.”

Reviewer #2:

Summary:

This study proposes that the microRNA cluster miR-277/34 controls the generation of sexual dimorphism in Drosophila melanogaster during metamorphosis by acting on specific hormonal and developmental gene pathways.

Strengths:

Using a combination of mRNA and small RNA sequencing together with genome-wide in silico and in vitro analyses the authors identified a microRNA cluster that may be involved in metamorphosis and the generation of sexual dimorphism in Drosophila melanogaster.

Weaknesses:

Biological validation of the identified sexually dimorphic genes and a detailed understanding of how the microRNA cluster miR-277/34 might be involved in the regulation of sesquiterpenoids are needed.

Major suggestions:

(1) If AstC-R1 and Kr-h1 are targets of the miR-277/34 cluster and cause their downregulation, it is not clear why there would also be a decrease in the levels of these genes in the miR-277/34 mutants. This would suggest that the mechanism is not straightforward and that further epistatic experiments should be carried out in order to clarify this issue.

We thank the reviewer for the positive and constructive comments. We agree that targets participate in endocrine feedback loops is dynamic, which could be the case for Kr-h1 and AstC-R1 during the larvae-pupae transition as they are components of the sesquiterpenoid hormone regulatory network. Epistatic analyses would be useful for future work and seem to be beyond the current scope of this study. The following information is now included in the main text:

Lines 184-187 - “Together, these data demonstrated that Kr-h1 and AstC-R are stage-specifically regulated by miR-277/34 in vivo. Further epistatic experiments would be needed to understand the dynamics between and the hormone actions.”

(2) The changes in the expression levels of AstC-R1 in pupae of miR-277-KO and mir-34-KO flies must be accompanied by photos of the respective larvae and pupae, as well as an analysis of the larvae-pupa transition on the mutants by gender.

We thank the reviewer for this suggestion. We have now added reference images illustrating the WL3 and WPP stages for w1118 in the Appendix as suggested (Author response image 1). We have analysed the larvae-pupae transition in both sexes of miR-277-KO and miR-34-KO mutants, directly comparing them with stage-matched w1118 controls, and we did not observe any detectable differences in larval morphology, pupal morphology, anterior spiracle eversion, gut-purge status, or timing of pupariation between the mutants and controls.

Author response image 1.

(3) Biological validation of the identified sexually dimorphic genes in vivo will be necessary for the support of this work.

We have now included additional quantitative RT-PCR validation of key insect hormone pathway genes in male and female WL3 and WPP stages of wild-type, miR-277-KO, and miR-34-KO flies (Figure 5). These additional analyses confirm sex-specific expression differences in both wild-type and mutant backgrounds, supporting dimorphic endocrine regulation. The main text are also revised and shown as follows:

Lines 276-287 - “To understand how different hormones such as juvenile hormone (Belgacem and Martin, 2002) involved during metamorphosis in both sexes, we selected and tested a selection of candidates from both sesquiterpenoid and ecdysteroid hormone pathways, and found JHAMT, Spok, CG40486, and CG10962 showed differential expression during transition from WL3 to WPP in mutant and/or wild-type fly lines in the transcriptome analyses (Supplementary Figure 16). To further examine these RNA-seq patterns, we performed RT-PCR on nine candidate genes from WL3 to WPP in WT and mutant fly lines. In the larval-pupal transition comparison, CG40486 was consistent down-regulated in WT males and females in both RNA-seq and RT-qPCR datasets. In the mutant-vs-WT comparison, CG9360 showed concordant downregulation in miR-277-KO WPP females. Other tested genes showed more condition-specific patterns matching between the transcriptomic and RT-qPCR analyses. Further validation and mechanistic studies will be required to define how these hormone-pathway changes contribute to the larval–pupal transition.”

Reviewer #3 (Public Review):

Summary:

The authors show convincingly the complexity of gene up- and down-regulation at the outset of metamorphosis and identify substantial differences between the two sexes, even at this early time in development. The complexity of microRNA expression and the difference between the sexes are also nicely laid out. The functional significance of these differences, though, is harder to establish. The authors have focused on the roles of two families of developmental hormones, the ecdysteroids, and the juvenile hormones. The emergence of sex-specific differentiation of organs during metamorphosis is clearly downstream of the action of ecdysteroids and/or JH, but there is no evidence that the presence or lack of these hormones has any effect on the sexual identity of organ systems - i.e., that manipulations of JH or ecdysteroid result in either the masculinization or feminization of individuals or their organs. The precedence for the linkage of these hormones to sex determination is the 2002, Belgacem & Martin study, which describes the effects of JH on fly locomotion. These authors show that the number of stop/start bouts is sexually dimorphic, and removal of JH in males shifts their frequency into the female range while giving treated males exogenous JH moves it back. While this is referred to as a "feminization" of male behavior, this quantitative shift in frequency is not as compelling as would be a qualitative shift -- for example, the removal of JH causing males to show egg-laying behavior (a result that has never been seen). Also, these effects are in a fully mature system, rather than at the early metamorphic time examined in the present paper. In driving and coordination metamorphosis, JH and ecdysteroids are intimately involved in sexual differentiation, but I know of no compelling evidence that they play a role in sex determination.

We thank the reviewer for the positive and constructive comments. We agree that our findings advanced on the sexual differences in gene regulation during metamorphosis rather than establishing direct evidence of juvenile hormone (JH) or ecdysteroids in influencing insect sex determination. In addition to rephrasing at various parts of the main text (see below), we have also carried out additional experiments in obtaining and analysing transcriptomes of late larvae and early pupae of both sexes in the wild-type of another species (Drosophila virilis), which showed similar KEGG pathways enriched. The revised parts are shown as follows:

Lines 289-303 – Results section

“Metamorphosis between different sexes in D. melanogaster and D. virilis

In D. melanogaster, the transition from WL3 to WPP shows increased carbohydrate/energy metabolism and ER protein processing, with decreased lipid metabolism, detoxification (cytochrome P450), and redox/cofactor pathways (folate, glutathione, retinol); while PM-LM exhibits broader negative enrichment in translational and RNA-processing machinery (ribosome, spliceosome, proteasome, RNA degradation, ubiquitin-mediated proteolysis) and in signaling modules (mTOR, MAPK, FoxO, Hippo), whereas PF-LF shifts are smaller and less coordinated by GSEA (Supplementary Figure S15). On the other hand in D. virilis, core features match that of D. melanogaster from WL3 to WPP, carbohydrate/energy metabolism and ER protein processing increase, while lipid, detoxification, and redox/cofactor pathways decrease. The sex bias is inverted relative to D. melanogaster as PM-LM shows limited up-regulation, whereas PF-LF displays broader, coordinated repression involving amino-acid metabolism (glycine/serine/threonine; cysteine/methionine), lysosome, ABC transporters, and longevity-related signaling, yielding the largest DEG set in females (Supplementary Figure S15). These data strongly suggested the sexual differences in gene regulation during metamorphosis in insects is not species-specific.”

Lines 354-361 – Methods section

“D. melanogaster w1118 and D. virilis were reared at 25 C, 45-50% relative humidity and 14:10 hour light-dark cycle. Sexes of wandering L3 larvae instar (WL3) were differentiated under the light dissecting microscope by the presence (male) or absence (female) of gonads (Supplementary Figure 1). Collections were restricted to larvae wandering out of food and ready for pupariation. WPP were defined as immobile puparia with everted spiracles and a uniform white cuticle that were no longer moving even with external stimuli. A total of three biological replicates (Whole-body of 1 individual was served as per biological replicate) per stage and sex were obtained for D. melanogaster and D. virilis.”

While the summary of the effects or removal of specific microRNAs on the components of the biosynthetic pathway for the JHs and ecdysteroids (Figure 2E ,F) is quite compelling, I am concerned about the effects of the removal of mir-277 and mir-34 on the levels of both the JHs and 20E. My concern centers around the data from the control group (w[1118] animals in Figure 2D). These data are the first report of a marked sex difference in the titer of either JH or ecdysteroid at the start of metamorphosis in Drosophila. As expected, males show a 10-20 increase in levels of JH III, JHB3, and 20E between the L3 stage and the white puparium, but, surprisingly, the levels of these hormones in female L3 larvae are equal to or greater than that seen at pupariation! These data for females run counter to over 50 years of work on the effects of ecdysteroids in Drosophila!

We thank the reviewer and agree that the endocrine profiles of WL3 females require careful interpretation, given the late-L3 to WPP transition represents a highly dynamic window in which ecdysteroid and sesquiterpenoid titres can fluctuate over short developmental intervals. The revised text is shown as follows:

Lines 322-326 – “Given the WL3 to WPP transition represents a highly dynamic window in which ecdysteroid and sesquiterpenoid titres can fluctuate over short developmental intervals, future experiments on narrower early-/mid-/late-wandering timepoints will be required to understand the dynamics of the microRNAs and hormones.”

As far as I can gather from the paper, the L3 data were obtained using wandering larvae. This stage lasts for about 12 hours and ends with pupariation. Larvae from this period need to be used with caution for hormone studies. Levels of both JH and ecdysteroid are low as larvae leave the food but rapidly rise to their peak levels at the white puparium stage 12 hours later. To deal with the rapidly changing hormonal landscape through this period, the researchers have used physiological markers to track this progression. Initially, it was the sage of "puffing" of the giant salivary gland chromosomes, but, for bulk collection of staged larvae, larvae are fed on food containing a blue dye, and progression is tracked by the loss of blue coloring from the gut. I could not find if the authors had any criteria for selecting larvae during the wandering period. Male and female larvae grow to different sizes. Might this difference in growth be biased when larvae were selected during their wandering phase?

We thank the reviewer and agree that WL3 represents a hormonally dynamic 12-hour window. To minimise developmental heterogeneity, WL3 larvae were selected for larvae that had completely exited the food and climbing upwards of the fly vials. To ensure tight developmental synchrony, pupating individuals from the same batch were collected 4 hours later, allowing us to match WL3 and WPP animals from a single, developmentally coordinated cohort. This paired-batch collection tried to minimise variation arising from differences in timing of wandering onset. As for the differences between the body sizes of male and female larvae, we minimise size-dependent bias, hormone titres measurement were measured to ng hormone per gram of tissue in our study, which corrects for sex-specific differences in mass. The information is now included in the main text as follows:

Lines 276-287 – “To understand how different hormones such as juvenile hormone (Belgacem and Martin, 2002) involved during metamorphosis in both sexes, we selected and tested a selection of candidates from both sesquiterpenoid and ecdysteroid hormone pathways, and found JHAMT, Spok, CG40486, and CG10962 showed differential expression during transition from WL3 to WPP in mutant and/or wild-type fly lines in the transcriptome analyses (Supplementary Figure 16). To further examine these RNA-seq patterns, we performed RT-PCR on nine candidate genes from WL3 to WPP in WT and mutant fly lines. In the larval-pupal transition comparison, CG40486 was consistent down-regulated in WT males and females in both RNA-seq and RT-qPCR datasets. In the mutant-vs-WT comparison, CG9360 showed concordant downregulation in miR-277-KO WPP females. Other tested genes showed more condition-specific patterns matching between the transcriptomic and RT-qPCR analyses. Further validation and mechanistic studies will be required to define how these hormone-pathway changes contribute to the larval–pupal transition”.

The other hormone-related issue is the expression of Kr-h1 during larval stages and metamorphosis (Figure 1G). Kr-h1 is the main target of JH and Kr-h1 expression is often used as a proxy for the JH titer. The authors report that peak Kr-h1 expression occurs in the L3 (when the JH titer should be lowest!) and that it drops at wandering. This pattern is counter to that reported in the literature (e.g., FlyBase, ModEncode).

We have now revised the main text as follows:

Lines 204-207 – “It should be noticed that the analyses of this study was based on RNA taken from whole-body rather than individual tissue, and further experiments will be required to dissect the dynamics of Kr-h1 and different hormones both spatially and temporally.”

Besides dealing with the issues above, it would be useful in the background to establish the difference between "sex determination" and "sexual differentiation". I was surprised that the authors could deal with this subject without ever mentioning the sex determination pathway - e.g., double sex, transformer, etc.

In this study, one major focus was on the differences between sex during metamorphosis rather than the sex determination pathway. We have included the reviewer’s suggestion by adding the following information in the main text, shown as follows:

Lines 73-75 - “In insects, various genes related to sex determination or showing sexual dimorphic features have been revealed, including doublesex and transformer (Shukla and Nagaraju, 2010; Deng et al, 2025).”

Line 61: at the time that the authors are considering, -- the transition from larva to pupa - the main controller of ecdysone production in the prothoracicotropic hormone, not ecdysis triggering hormone.

Thanks for the reviewer’s suggestions. The main text is now written as follows:

Lines 44-47 - “In general, these three hormones work in a cooperative manner, where ecdysteroid 20-hydroxyecdysone controls the timing of ecdysis or molting, prothoracicotropic hormone and the insulin-like peptides act as regulators of ecdysteroid synthesis, and sesquiterpenoid hormones such as juvenile hormone (JH) regulates metamorphosis based on their titre levels.”

Line 71: it would be useful to name the main microRNAs that have been implicated in regulating insect metamorphosis.

The main text is now written as follows:

Lines 60-63 - “Previous studies have identified a number of microRNAs contributing to the regulation of insect metamorphosis such as let-7, miR-125, and miR-2 family (e.g. Caygill and Johnston 2008; Sokol et al 2008; Lozano et al 2015).”

For Figures 2E and F as well as 3C (and a number of supplementary figures), it would be useful to provide some quantitative representation of the level of activation or suppression (as done in Figure 3B) rather than just Red or Green

The trend of expression change of genes in selected pathways and detailed quantitative information can now be found in the supplementary file.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

The authors sought to determine how Rif1 contributes to DNA replication timing (RT), transcriptional regulation, and embryonic development using zebrafish. They generated a maternal-zygotic rif1 knockout line and examined developmental phenotypes, genome-wide replication timing profiles, RNA-seq, and nascent transcription (SLAM-seq) during early embryogenesis.

Their major findings in this manuscript are

(1) Rif1 is not essential for zebrafish viability, unlike its partially essential role in mice.

(2) Rif1 deficiency causes defects in female sex determination, delayed epiboly, and reduced primitive erythropoiesis.

(3) Genome-wide RT is altered by Rif1, but developmental stage has a much larger influence than Rif1 itself.

(4) Rif1 is required for the proper maturation ("sharpening") of the RT program during development rather than for specific developmental RT switches.

(5) Rif1 has a much stronger effect on transcription during zygotic genome activation (ZGA) than on replication timing at these early stages.

(6) Loss of Rif1 leads to increased expression of early zygotic genes, indicating that Rif1 normally suppresses widespread transcription during ZGA.

Overall, the work proposes that Rif1 independently regulates replication timing and transcription, with these two functions becoming most prominent at different developmental stages.

The major strengths of the manuscript are as follows.

(1) the study combines multiple genome-wide approaches including whole-genome RT profiling, RNA-seq, SLAM-seq in combination with gene KO and developmental analyses.

(2) One of the strongest points is that the authors conducted the analyses at multiple developmental stages rather than a single point.

(3) The most important conclusion is that the Rif1 regulates transcription during development in a manner largely independent of its RT function, which was further strengthened by the additional data provided in the revised manuscript.

On the other hand, the weakness of the manuscript includes the followings.

(1) Limited mechanistic insight. The questions such as where Rif1 binds on the chromatin (in relation to the transcriptional promoters/ enhancers and replication origins).

(2) Which functional domains of RIf1 are involved in regulation of transcription and replication (Is PP1 recruitment required for transcription regulation?) are not addressed.

(3) Since Rif1 is known to be involved in chromatin organization/ nuclear architecture regulation, the studies addressing this (Hi-C, compartment analyses, ATAC seq etc) would provide important mechanistic information.

(4) Female sex determination phenotype is intriguing, but it remains largely descriptive, and its mechanisms are elusive at the moment.

Overall, the results support the authors' conclusions and they have successfully provided answers to the authors' original questions on developmental roles of Rif1 in RT and transcription in vertebrate.

Comments on revised version:

The authors responded to my comments in a largely satisfactory manner. They have conducted additional analyses and concluded that Rif1 regulates transcription during ZGA largely independently of its classical RT function, which is an important finding.

Although authors did not examine origin firing and replication fork rate in rif1 KO cells, which I suggested in my original review, this can be saved for their future studies.

I think the revised manuscript has been improved and provides important basic information on the functions of the conserved Rif1 protein in RT and transcriptional regulation.

I have no further recommendation for additional experiments or data analyses.

We thank the reviewers for their public evaluations of the manuscript.

Reviewer #2 (Public review):

This study by Masser et al. analyzes global replication timing and gene expression in rif-1 null zebrafish. This work is an extension of their previous report of the normal replication timing pattern during wild-type zebrafish development. The major valuable finding here is that Rif1 is not essential for viability in zebrafish, and - counter to expectation from studies in cultured cells and other species - late replication does not strongly depend on Rif1. Instead, the data suggest that Rif1 subtly sharpens replication timing pattern during normal development rather than function generally to delay replication timing. In the absence of Rif1, the normal pattern establishment is somewhat delayed. The authors also document some changes in expression during development with more genes being repressed by Rif1 than activated at some early stages.

The study and analysis are generally rigorous, and the conclusions are supported by convincing data. Given the strong link between replication timing and cell type/development, studying timing in a whole developing organism is important. The experimental approach is technically challenging, particularly the bioinformatic analysis. The scientific advance here is largely confined to documenting the timing of Rif1-affected transcription, the unanticipated effect of the rif1 deletion on replication timing and on sex determination, though the latter is not explored. The difference in timing of the transcription phenotypes and replication phenotypes suggests they may be very distinct Rif1 roles. The overall study a useful set of findings and detailed data for future work.

Loss of Rif1 did not affect viability, but it did strongly influence sex determination, resulting in a lower population of females. This effect is the strongest organismal phenotype, but the study provides no mechanistic explanation for the loss of females from the data gathered here.

Comments on revised version:

We are generally satisfied with the revised version of this manuscript.

We thank the reviewers for their public evaluations of the manuscript.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

Characterization of a dissociable Mediator subunit implicated in cellular pathways, particularly lung alveolar function, and HIV latency is conceptually interesting.

Strengths:

The strengths of this study are:

(1) Demonstration of MED16 dissociation from the core Mediator complex and formation of a subcomplex containing MED16, upstream-binding protein 1 (UBP1), and transcription factor cellular promoter 2 (TFCP2) by elegant biochemical fractionation and immunoblotting analysis.

(2) Defining nine N-terminal WD-40 repeats (WDRs) of MED16 as a Mediator-incorporating module and the C-terminal ⍺β-domain (157 amino acids) important for interaction with the UBP1-TFCP2 heterodimeric complex.

(3) Illustration of a weak hydrophobic interaction between MED16 and the Mediator core that could be disrupted by 1,6-hexanediol, but not by its 2,5-hexanediol isomer nor by high salt (500 mM NaCl) disruption.

(4) Classification of UBP1-upregulated cellular genes typically containing binding sites flanking the transcription start site (TSS) in contrast to UBP1-downregulated genes often containing a TSS-overlapping UBP1-binding site

(5) Presenting evidence for Mediator complex-dissociated free MED16-repressed HIV promoter activity through functional association with UBP1 and showing bromodomain-containing protein 4 (BRD4) inhibitor JQ1 that potentially disrupts BRD4-inhibited HIV-1 transcription elongation could lead to reversal of HIV-1 latency.

Weaknesses:

Nevertheless, foreseeable weaknesses include:

(1) No clear demonstration of MED16-UBP1-TFCP2 indeed forming a trimeric core subcomplex in regulating cellular gene transcription and HIV-1 promoter inhibition

We appreciate this insightful comment from the reviewer. The physical interaction between MED16 and the UBP1–TFCP2 heterodimer was uncovered serendipitously via biochemical fractionation. Specifically, UBP1 and TFCP2 were identified in gel-filtration fractions containing free MED16 that eluted separately from the intact core Mediator complex (Figures 1D–1F). This biochemical observation suggested to us a potential functional linkage between MED16 and these two transcription factors. Subsequently, our functional assays further clarified this regulatory relationship: UBP1 and TFCP2 do interact with MED16 that is required to be fully assembled into Mediator complexes to exert transcriptional control. Truncation of MED16’s N-terminal WD40-repeat (WDR) domain (MED16ΔWDR) eliminates MED16 integration into the Mediator complex. Notably, this MED16ΔWDR mutant still retains an intact C-terminal αβ-domain capable of binding UBP1 yet completely loses the capacity to support UBP1-dependent transcription. Collectively, these data demonstrate that UBP1–TFCP2 engage MED16 as a component of the complete Mediator complex to govern target gene expression in cells.

We have updated the abstract and full manuscript to present this model more clearly and coherently throughout the text.

(2) No validation of transcriptomic datasets and pathways identified.

We thank the reviewer for this comment. Since our RNA-seq analysis identified SFTP family genes (SFTPA1, SFTPA2, SFTPB, SFTPD) as UBP1-MED16 co-regulated targets, and these are lung-specific surfactant protein genes, we have now performed qRT-PCR validation in the A549 human lung adenocarcinoma cell line. The results confirm that knockdown of MED16 largely attenuates the expression of these SFTP genes (see Author response image 1) and other UBP1 target genes identified in our RNA-seq dataset.

Author response image 1.

qRT-PCR validation of SFTP gene family expression (SFTPA1/A2/B/D) in A549 cells

(3) Use of mostly artificial reporter gene constructs and non-HIV host cells (e.g., human 293T embryonic kidney cells, human HeLa cervical cancer cells, and mouse HT pancreatic cancer cells) for examining MED16/UBP1-regulated HIV transcription.

To overcome the limitations of artificial reporter systems, we have managed to utilize multiple complementary approaches beyond reporter assays, including: (i) RNA-seq analysis of endogenous gene regulation, (ii) biochemical co-IP and gel filtration experiments, (iii) immobilized template transcription assays that directly measure PIC assembly and nascent RNA production, and (iv) validation in the J-Lat 10.6 CD4+ T cell line harboring an integrated latent HIV-1 provirus, where MED16 overexpression suppresses HIV-1 reactivation.

Unfortunately, the direct infection experiments with replication-competent HIV-1 were not feasible as our institution does not have the biosafety level 3 (BSL-3) containment facilities.

(4) Inconsistent use of 293T and HeLa cells in the characterization of dissociated MED16 interaction with UBP1 and TFCP2.

For biochemical characterization in this study, HEK293T cells were primarily utilized for overexpression-based co-immunoprecipitation (Co-IP) and domain-mapping assays owing to their superior transfection efficiency. In contrast, HeLa cells were employed for gel-filtration chromatography and endogenous Co-IP, as fractionation of HeLa nuclear extracts represents a well-established workflow for purifying native protein complexes. Critically, the physical interaction between MED16 and the UBP1–TFCP2 heterodimer was consistently detected in both HEK293T whole-cell lysates and HeLa nuclear extracts across all assays.

(5) In vitro transcription using immobilized DNA templates was not performed to a high standard, thus failing to convincingly show MED16/UBP1-inhibited HIV-1 transcription preinitiation complex formation.

We appreciate the reviewer’s careful assessment of the immobilized template assay. While we recognize the technical challenges inherent in this approach, we want to emphasize that the proposed model—that MED16-UBP1 inhibits HIV-1 transcription at the level of PIC assembly—does not rest solely on this single experiment.

Multiple independent lines of evidence converge on this model:

(1) The MED16-UBP1 inhibition depends on the UBP1 binding site overlapping the TSS: a chimeric reporter with the UBP1 binding site placed at the TSS is inhibited by MED16, whereas placing it upstream does not show inhibition, demonstrating the UBP1 binding site-specific repression (Fig 6A-C).

(2) MED16 overexpression inhibits HIV-1 reporter activity in a manner depending on interaction with UBP1. Deletion of the MED16 αβ-domain (MED16Δαβ), which abolishes MED16-UBP1 interaction, completely abrogates the inhibitory effect (Fig 5E-G).

(3) The MED16-UBP1 inhibition of HIV is independent of TAR-mediated elongation (Fig S2B-C) and HDAC-mediated deacetylation (Fig S2A), consistent with an inhibition mechanism operating at the initiation stage rather than at the post-initiation steps.

(4) Upon MED16 overexpression, the immobilized template assay shows reduced CDK8 binding and Pol II pSer5 signals, along with TFIIB retention, providing mechanistic evidence that is consistent with the aforementioned functional observations.

Thus, the model is supported by convergent evidence from reporter assays, domain-mapping experiments, pharmacological inhibition, and in vitro biochemical reconstitution. In the revised manuscript, we have further clarified how these complementary approaches collectively support the PIC inhibition model.

Reviewer #2 (Public review):

Summary:

The article from Zheng et al. proposes an interesting hypothesis that the Med16 subunit of Mediator detaches from the complex, associates with transcription factor UBP1, and this complex activates or represses specific sets of genes in human cells. Despite my excitement upon reading the abstract, I was concerned by the lack of rigor in the experimental design. The only statement in the abstract that has some experimental support is the finding that Med16 dissociates from the Mediator and forms a subcomplex, but the data shown remain incomplete.

We would like to first address a core conceptual point that we believe underpins several of the reviewer’s concerns.

We respectfully disagreed that the reviewer summarized our proposed model as a pathway where “Med16 detaches from the complex, associates with transcription factor UBP1, and this complex activates or represses specific sets of genes.” We acknowledge that phrasing in our original manuscript may have created this misleading interpretation, yet this is not the mechanistic model we intend to convey. We identified the MED16–UBP1–TFCP2 interaction serendipitously during biochemical fractionation: UBP1 and TFCP2 co-eluted with free MED16 in gel-filtration fractions that were fully separated from the intact core Mediator complex. While this biochemical result guided our subsequent functional investigation into MED16–UBP1–TFCP2 crosstalk, we never intend to propose that a standalone MED16–UBP1–TFCP2 subcomplex can drive transcriptional activation or repression independently of the intact Mediator complex.

Most importantly, our functional experiments demonstrate that UBP1 and TFCP2 require MED16 as an integral part of the Mediator complex to regulate transcription as shown by domain mapping experiments. Specifically, MED16 uses its N-terminal WDR domain to integrate into the Mediator and its C-terminal αβ-domain to bind UBP1/TFCP2. Deletion of either WDR or αβ-domain is functionally inert in both cellular and HIV-1 reporter assays. Thus, the MED16-UBP1 interaction is functionally relevant because it links these transcription factors to the Mediator complex, not because it forms an autonomous regulatory complex. In another word, UBP1–TFCP2 target MED16 to recruit the whole Mediator complex for governing gene expression in cells.

We have comprehensively revised the full manuscript to sharply distinguish our initial biochemical observation from the validated functional model. As all experimental approaches carry inherent limitations, we tried our best to validate every major conclusion using multiple orthogonal assays and to draw mechanistic interpretations when results from distinct experimental systems do converge. Our detailed replies to each specific concern from the reviewer are provided below.

Strengths:

The authors have preliminary evidence that a stable Med16 complex may exist and that it may regulate specific sets of genes.

Weaknesses:

The experiments are poorly designed and can only infer possible roles for Med16 or UBP1 at this point. Furthermore, the data are often of poor quality and lack replication and quantitation. In other cases, key data such as MS results aren't even shown. Instead, we are given a curated list of only about 6 proteins (Figure S1), a subset of which the authors chose to pursue with follow-up experiments. This is not the expected level of scientific process.

As clarified in our Summary Response above, we thought this reviewer may have misinterpreted our data and model. Overall, our work demonstrates that MED16 acts as a molecular bridge, linking UBP1/TFCP2 to the Mediator complex, not that three proteins form a free-standing subcomplex, and we have extensively revised the manuscript to clarify this.

Here we also want to address the specific concerns about data completeness and rigor. The full mass spectrometry datasets were not clearly presented in the original submission. We have now reanalyzed the IP-MS data using a more precise quantification approach. Rather than scoring proteins by simple presence or absence, we calculated a bait-preferential score for each protein by comparing its normalized abundance in the MED16 IP to that in the other three Mediator bait IPs (MED1, MED12, CDK8). This score reflects the degree to which a protein is preferentially enriched by MED16 relative to other Mediator subunits. The bait-specific candidates identified by this analysis are presented in Fig S1B, and the complete list of MED16-specific candidates is now included. In addition, the raw abundance values and peptide counts for all identified proteins have been compiled and uploaded as supplementary tables. A detailed description of the normalization and scoring procedure is provided in the Methods section

Furthermore, we have added quantification analysis for key Western blot results throughout the revised figures.

(1) The data supporting the Med16 dissociation and co-association with UBP1 are incomplete and not convincing at this stage. According to the Methods and text, the gel filtration column was run with "un-dialyzed HeLa cell nuclear extract" and eluted in 300mM KCl buffer. The extracts were generated with the Dignam/Roeder method according to the text. Undialyzed, that means the extract would be between 0.4 - 0.5M NaCl. Under these high salt conditions (not physiological), it's possible and even plausible that Mediator subunits could separate over time. This caveat is not mentioned or controlled for by the authors. Because a putative Med16 subcomplex is a foundational point of the article, this is concerning.

The data are incomplete because a potential Med16 complex is not defined biochemically. The current state suggests a smaller Med16-containing complex that may also contain UBP1 and other factors, but its composition is not determined. This is important because if you're going to conclude a new and biologically relevant Med16 complex, which is a point of the article, then readers will expect you to do that.

We appreciate the reviewer’s thorough feedback and address the two core concerns separately below.

(1) Undialyzed nuclear extracts & high-salt conditions

Published work confirms Mediator undergoes massive precipitation (~70% loss) upon dialysis to low-salt 100 mM KCl buffer (1), justifying our use of undialyzed HeLa nuclear extracts for biochemical assays. Prior study also demonstrated intact Mediator remains stable in up to 1 M KCl (1). Therefore, MED16 dissociation seen at 300 mM KCl arises from its unique biochemical property, rather than non-specific high-salt damage.

(2) Biochemical interpretation of MED16-containing fractions

We have revised ambiguous original wording to clarify our model: we do not intend to propose an autonomous MED16–UBP1–TFCP2 subcomplex functions independently in cells. Gel filtration only captures a biochemical state where MED16 co-elutes with UBP1/TFCP2 separate from core Mediator, which merely inspired our functional follow-up. Three lines of evidence prove UBP1/TFCP2 require fully assembled Mediator to function:

(i) MED16’s N-terminal WDR domain mediates Mediator integration, while its C-terminal αβ-domain binds UBP1; both interactions can occur simultaneously (Fig 2B).

(ii) MED16Δαβ incorporates into Mediator but loses UBP1 binding, showing no activity in UBP1-driven and HIV-1 reporter assays (Fig 3G, 5G).

(iii) MED16ΔWDR retains UBP1 binding yet cannot assemble into Mediator, thus fails to repress HIV-1 transcription (Fig 5F).

In vitro MED16 separation only reflects its extractable biochemical behavior, not a functional standalone complex. Collectively, our data establish UBP1/TFCP2 recruit the entire Mediator complex via MED16. All relevant manuscript sections have been rewritten to distinguish this preliminary biochemical observation from our validated functional model.

Equally concerning are the IP-western results shown in Figure 1. In my opinion, these experiments do nothing to support the claims of the authors. The authors use hexanediols at 5% or 10% in an effort to disrupt the Mediator complex. Assuming this was weight/volume, that means ~400 to 800mM hexanediol solution, which is fairly high and can be expected to disrupt protein complexes, but the effects haven't been carefully assessed as far as I'm aware. The 2,5 HD (Figure 1B) experiments appear to simply contain greater protein loading, and this may contribute to the apparent differential results. In fact, in looking at the data, it seems that all MED subunits probed show the same trend as Med16. They are all reduced in the 1,6HD experiment relative to the 2,5 HD experiment. But it's hard to know, because replicates weren't completed and quantitation was not done. There aren't even loading controls. Other concerns about the IP-Western experiments are outlined in point 2.

Treatment with 10% (w/v) 1,6-hexanediol (1,6-HD) is a well-established method to selectively disrupt weak hydrophobic interactions while maintaining stable protein assemblies. A comparable strategy was recently applied to dissect NEAT1-dependent paraspeckle formation driven by liquid–liquid phase separation (2). Notably, we included 2,5-hexanediol (2,5-HD) as a critical specificity control: as a structural isomer with distinct hydroxyl group positioning, 2,5-HD cannot efficiently disrupt weak hydrophobic contacts and failed to trigger MED16 dissociation (Figure 1B). The divergent outcomes observed side-by-side with equal sample input therefore serve as an internal control, validating that MED16 dissociation is a specific consequence of 1,6-HD treatment.

We acknowledge mild signal reductions for several other Mediator subunits following 1,6-HD exposure under certain immunoprecipitation (IP) conditions (Figures 1A, 1B). Nevertheless, MED16 exhibits a uniquely pronounced dissociation by 1,6-HD that is consistent across three independent IPs using anti-CDK8, anti-MED1, and anti-MED12 antibodies, in both HEK293T whole-cell lysates and HeLa nuclear extracts. By contrast, the mild depletion of other Mediator subunits varies substantially depending on the antibody and cell extract used, whereas robust MED16 loss is universally observed in all experimental setups we tested.

(2) At no point do the authors apply rigorous methods to test their hypothesis. Instead, methods are applied that have been largely discredited over time and can only serve as preliminary data for pilot studies, and cannot be used to draw definitive conclusions about protein function.

We greatly appreciate the reviewer’s emphasis on methodological rigor. We fully concur that individual techniques including protein fractionation, IP-WB, transient transfection, shRNA knockdown, immobilized template and luciferase reporter assays each carry intrinsic limitations when deployed alone. To address this, we employed a panel of orthogonal experimental strategies throughout our work and only draw conclusions supported by convergent results across distinct assays. Our core mechanistic conclusion—that MED16 acts as a molecular bridge linking the UBP1–TFCP2 heterodimer to the intact Mediator complex to control transcription—is validated by multiple independent lines of evidence, rather than resting on a single experimental approach, as elaborated in detail below.

(a) IP-westerns are fraught with caveats, especially the way they were performed here, in which the beads were washed at relatively low salt and then eluted by boiling the beads in loading buffer. This will "elute" bound proteins, but also proteins that non-specifically interact with or precipitate on the beads. And because Westerns are so sensitive, it is easy to generate positive results. It's just not a rigorous experiment.

We acknowledge that IP-Western has inherent limitations regarding specificity. To minimize non-specific signals, we included IgG controls in our CDK8 IP experiments (available in raw data) and the boiling elution method has been extensively validated in our hands. More importantly, the interaction between MED16 and UBP1/TFCP2 is not solely supported by IP-Western.

This interaction was initially observed through co-elution of MED16 with UBP1 and TFCP2 in gel filtration fractions (Fig 1D), confirmed by reciprocal co-IP with anti-MED16 and anti-TFCP2 antibodies in both HeLa NE and the resolved fractions (Fig 1E-F), and further corroborated by in vitro GST pull-down assays showing direct binding between MED16 αβ-domain and recombinant UBP1 (Fig 2C). IP-MS analysis with three biological replicates independently identified UBP1 and TFCP2 as MED16-associated proteins. Each of these methods has different sources of potential artifacts, yet they all converge on the same conclusion.

(b) Many conclusions relied on transient transfection experiments, which are problematic because they require long timeframes, during which secondary/indirect effects from expression/overexpression will result. This is especially true if the proteins being artificially expressed/overexpressed are major transcription regulators, which is the case here. It is simply impossible to separate direct from indirect effects with these types of experiments. Another concern is that there was no effort to assess whether the induced protein levels were near physiological levels. Protein overexpression, especially if the protein is a known regulator of pol2 transcription (e.g., UBP1 or Med16), will create many unintended consequences.

The reviewer raises a valid concern about indirect effects from overexpression. To address this, our key conclusions were validated by multiple loss-of-function approaches that do not rely on overexpression alone. Specifically, the conclusion that MED16 is required for UBP1 transcriptional activity is supported by:

(i) shRNA-mediated MED16 knockdown (Fig 3C);

(ii) CRISPR-mediated MED16 knockout in five independent frameshift clones with consistent phenotypes (Fig 3E-F);

(iii) Using a domain-disruption approach, we demonstrated that a UBP1-binding-deficient MED16 mutant (Δαβ) fails to exert the dominant-negative effect on UBP1 activity, as seen with wild-type MED16 (Fig 3G and 6A). All these different methods point to the same conclusion. This makes it unlikely that the effects we see are simply artifacts of overexpression or indirect consequences.

(c) Many conclusions were made based upon shRNA knockdown experiments, which are problematic because they require long timeframes (see above point), which makes it nearly impossible to identify effects that are direct vs. indirect/secondary/tertiary effects. Also, shRNA experiments will have off-target effects, which have been widely reported for well over a decade. An advantage of shRNA knockdowns is that they prevent genetic adaptation (a caveat with KO cell lines). A minimal test would be to show phenotypic rescue of the knockdown by expressing a knockdown-resistant Med16 (for example), but these types of experiments were not done.

We agree that shRNA has potential off-target effects, and that is why we did not rely on shRNA as our sole loss-of-function approach. We have generated five independent CRISPR MED16 knockout clones, each with a distinct frameshift mutation, and all five clones showed consistent reduction in UBP1 reporter activity (Fig 3E-F). Furthermore, we performed RNA-seq on MED16 knockout cells in which wild-type MED16 was re-introduced. As presented in Author response image 2, re-expressing MED16 in KO cells can largely restore the expression of UBP1 target genes. These rescue data provide strong evidence that the transcriptional defects are specifically attributable to MED16 loss rather than off-target effects or clonal adaptation.

Author response image 2.

Gene profiling of MED16 KO and rescue effect

(d) Many experiments used reporter assays, which involved artificial, non-native promoters. Reporters are good for pilot studies, but they aren't a rigorous test of direct regulatory roles for Med16 or other proteins. Reporters don't even measure transcription directly. In fact, no experiment in this study directly measures transcription. An RNA-seq experiment was done with overexpressed or Med16 knockdown cells, but these required long timeframes and RNA-seq measures steady-state mRNA, which doesn't test the potential direct effects of these proteins on nascent transcription.

The two principal reporters used in this study are both based on native promoters. The UBP1 reporter is derived from the mouse α-globin gene promoter, a well-established natural target of UBP1/TFCP2 that contains two endogenous UBP1 binding sites. To enhance sensitivity, we expanded these to six copies, as the α-globin promoter has low basal activity in most cell lines. Critically, this expansion preserved the original promoter architecture, including the CCAAT box, TATA box, and TSS. The HIV-1 reporter is driven by the HIV-1 core promoter (-78 to +60), which contains all elements required for basal transcription and Tat-mediated activation. Thus, both reporters retain the native sequence context of the regulatory elements under study.

These reporter assays served as initial screening and hypothesis-testing tools. The key functional insights from reporters were then validated in more physiological contexts:

(i) The position-dependent effect of UBP1 binding (activation when upstream of TSS, repression when overlapping TSS) observed in chimeric reporters (Fig 6A-C) was independently confirmed by motif enrichment analysis of endogenous genes from RNA-seq data (Fig 6D-E).

(ii) Our immobilized template transcription assays directly measure nascent RNA production from the HIV-1 promoter, showing that MED16 overexpression reduces transcriptional output (Fig 7C). Thus, while reporter assays alone would be insufficient, our conclusion on UBP1-MED16 function are further corroborated by both global genomic analysis and direct in vitro transcription measurements.

(e) The MS experiments show promise, but the data were not shown, so it's hard to judge. The reader cannot compare/contrast the experiments, and we have no indication of the statistical confidence of the proteins identified. How many biological replicate MS experiments were performed?

The IP-MS experiments were performed with three biological replicates for each of the four antibodies against MED1, MED12, CDK8, and MED16 respectively. The complete datasets are now provided in the revised manuscript (Supplementary Table 1).

In addition, we have reanalyzed the data using a more quantitative approach. In the original submission, we classified proteins by a binary cutoff—detected or not detected in MED16 relative to other baits. In the revised analysis, we calculated a bait-preferential score for each protein by comparing its normalized abundance in the MED16 IP to its mean abundance across the other three Mediator baits. This score reflects how strongly a protein is enriched by MED16, rather than simply whether it meets an arbitrary detection threshold. A detailed description of this method is provided in the revised Methods section.

Notably, using this quantitative method, UBP1 and TFCP2 can also be detected at lower levels in some replicates of the other Mediator baits. This is consistent with our functional model: UBP1 and TFCP2 associate with the whole Mediator complex through MED16. The MED16-biased enrichment pattern, now supported by the bait-preferential score, reinforces the conclusion that MED16 serves as the primary anchor for UBP1/TFCP2 to associate with the Mediator complex.

(3) The data are over-interpreted, and alternative (and more plausible) hypotheses are ignored. Many examples of this, some of which are alluded to in the points above. For example, Med16 loss or overexpression will cause compensatory responses in cells. An expected result is that Mediator composition will be disrupted, since Med16 directly interacts with several other subunits. Also in yeast, the Robert, Gross, and Morse labs showed that loss of Med16/Sin4 causes loss of other tail module subunits, and this would be expected to cause major changes in the transcriptome. The authors also mention that yeast Med16/Sin4 "alters chromatin accessibility globally" and this would be expected to cause major changes in the transcriptome, leading to unintended consequences that will make data analysis and identification of direct Med16 effects impossible. The unintended consequences will be magnified with prolonged disruption of MED16 levels in cells (e.g., longer than 4h). These unintended consequences are hard to predict or define, and are likely to be widespread given the pivotal role of Mediator in gene expression. One unintended consequence appears to be loss of pol2 upon Med16 over-expression, as suggested by the western blot in Figure 8B. I point this out as just one example of the caveats/pitfalls associated with long-term knockdowns or over-expression.

We thank the reviewer for raising this important point. Indeed, our new Co-IP and IP-MS data confirm that MED16 knockout leads to partial dissociation of MED23, MED24, and MED25 from the Mediator complex. We agree that this structural perturbation must be carefully considered when interpreting phenotypes from MED16 depletion experiments, and we acknowledge that long-term knockdown or knockout approaches are inherently susceptible to secondary effects and cellular adaptation.

Author response image 3.

MED16 knockout impacts on the Mediator complex

However, our key conclusions are not based solely on long-term depletion experiments. Several lines of evidence, including experiments performed on short timescales without prolonged MED16 loss, converge on the same conclusion:

First, the MED16 mutant lacking its C-terminal αβ-domain cleanly separates the two functions. This mutant retains the intact N-terminal WDR domain of MED16 and can integrate into the Mediator complex, preserving its structural role and preventing tail module dissociation. Yet it completely fails to exert the competitive inhibition (squelching) effect on the UBP1 reporter that is observed with wild-type MED16 overexpression (Fig 3G), and similarly fails to inhibit HIV-1 reporter activity (Fig 5G). The sole molecular defect of this mutant is its inability to bind UBP1 (Fig 2B). Critically, this overexpression experiment is performed in a wild-type background where the endogenous Mediator complex remains structurally intact. The only variable is whether the overexpressed MED16 can interact with UBP1. This provides strong evidence that the transcriptional effects are mediated specifically through the MED16-UBP1 interaction interface, independent of MED16's structural role in maintaining Mediator integrity.

Second, the transcriptional changes we observe are not random but show specific functional coherence. If the transcriptomic changes in MED16 knockdown cells were merely secondary consequences of Mediator tail module disruption, we would expect broad, non-specific dysregulation. Instead, the UBP1-MED16 co-regulated genes are enriched for specific biological processes—angiogenesis—which largely align with the known biological functions of UBP1 (Fig 4D-E). This functional specificity is difficult to reconcile with the global, non-specific transcriptional disruption that would be expected from the total Mediator dysfunction.

Finally, we wish to address the reviewer's observation regarding Pol II levels in Figure 8B. In preparing the revised manuscript, we carefully re-examined our original Western blot data and found that the reduction of Pol II upon MED16 overexpression was not consistently reproducible across independent experiments. We have therefore replaced new Pol II blot in Figure 8B. We note that this revision does not affect any of the conclusions drawn from Figure 8, which focus on the inhibitory effect of MED16 overexpression on HIV-1 latency reversal in J-Lat cells.

We are grateful for the reviewer’s careful assessment, which encouraged us to refine our data presentation and enhance experimental rigor. The manuscript has been significantly improved as a result.

Reviewer #3 (Public review):

Weaknesses:

(1) The decrease in 1,6-hexanediol-treated cells of MED16 is modest, variable, not quantified, and internally inconsistent. For example, in Figure 1A, 1,6-hexanediol treatment should not have an impact on the level of the protein being directly IP. For MED12 (and CDK8 and MED1 to a lesser extent), 1,6-hexanediol treatment alters the level of the target protein in the IP. Along these lines, Figure 1A shows a no 1,6H-D dependent decrease in MED1 or MED12 levels in the CDK8 IP, whereas Figure 1B does show a decrease. Figure 1A shows no 1,6H-D dependent decrease in CDK8 levels in the MED1 IP, whereas Figure 1B shows a dramatic decrease. MED24 levels in the MED12 IP increase upon 1,6H-D in Figure 1A, but decrease in Figure 1B. Internal inconsistencies of this nature persist in the other Figures.

We thank the reviewer for this careful observation, and we here clarify the rationale behind our experimental design to resolve the apparent discrepancies between Figures 1A and 1B.

We first performed co-immunoprecipitation (co-IP) assays using HEK293T whole-cell lysates with three distinct antibodies targeting CDK8, MED1, and MED12, respectively, to pull down intact Mediator complexes. This setup was designed to assess whether 1,6-hexanediol (1,6-HD) impairs Mediator complex integrity and, if so, whether this perturbation affects individual subunits unequally. Across all three independent IP replicates, we observed a uniform trend: most Mediator subunits displayed only mild signal attenuation, whereas MED16 exhibited a striking, dose-dependent reduction upon escalating 1,6-HD concentrations (Fig 1A). Quantitative densitometry of these immunoblot signals has now been incorporated into the revised Figures 1A and 1B to better visualize this difference. Thus, this initial result in Fig 1A indicated that MED16’s interaction with the core Mediator complex is uniquely vulnerable to 1,6-HD disruption, irrespective of which Mediator subunit was used for immunoprecipitation.

To validate the reproducibility of this phenotype, we replicated the assay in an alternative biochemical system using HeLa nuclear extracts (NEs) (Fig 1B), with 2,5-hexanediol (2,5-HD) included as a critical negative control—this structural isomer cannot disrupt weak hydrophobic protein-protein contacts. Notably, the HeLa NE experiments in Fig 1B were carried out under elevated salt conditions (~300 mM NaCl), in contrast to the 150 mM NaCl buffer used for the HEK293T lysate assays in Figure 1A.

We want to emphasize that despite these substantial technical disparities between the two experimental setups, both datasets converge on the identical core conclusion: MED16’s association with the core Mediator complex is selectively disrupted by 1,6-HD. This consistent trend is further strengthened by quantitative analysis of immunoblot band intensities from biological replicates, which we have added to the revised figures.

Minor variability observed for other Mediator subunits between Fig 1A and 1B arises from intrinsic differences in cell type, extraction protocols, and buffer salt concentrations. For this reason, we did not draw mechanistic interpretations regarding the variable signal changes of other subunits across distinct experimental conditions; instead, our analysis focused on the robust, consistent loss of MED16 following 1,6-HD exposure.

(2) Undermining the value of Figure 1E/F, UBP1 and TFCP2 may also associate with the small amount of MED16 in the 2MDa fractions. This is not tested, and therefore, the conclusion that they just associate with the dissociable form of MED16 is not supported.

We thank the reviewer for this insightful observation. Indeed, UBP1 and TFCP2 can associate with MED16 in the context of the intact Mediator complex. Figure 1B directly supports this: under 2,5-HD conditions, where MED16 remains integrated into the Mediator, both UBP1 and TFCP2 are co-immunoprecipitated with the Mediator complex (via anti-MED1). This association is lost under 1,6-hexanediol conditions, where MED16 dissociates—suggesting that UBP1 and TFCP2 are tethered to the Mediator through MED16.

The gel filtration experiment (Fig 1D) further reveals that a portion of MED16 resolves away from the core Mediator complex under these in vitro conditions, and Figure 1E-F shows that UBP1 and TFCP2 co-immunoprecipitated with MED16 in these lower molecular weight fractions. Taken together, these data indicate that UBP1 and TFCP2 can be found in association with MED16 in two biochemically distinguishable states: one integrated into the Mediator complex, and another that has dissociated from it under our experimental conditions. We did not state that UBP1 and TFCP2 associate exclusively with the dissociated form; rather, the dissociated fraction is where we initially identified this interaction, which then led us to investigate its functional significance. The whole manuscript has been extensively rewritten now, and hopefully the confusion has been clarified.

Our functional data further demonstrate that the transcriptional activities of UBP1 and TFCP2 require the intact Mediator complex. MED16 bridges this interaction through its C-terminal αβ-domain, which binds UBP1/TFCP2, and its N-terminal WDR domain, which anchors MED16 into the Mediator. We have revised the manuscript to clearly distinguish the biochemical observation from the functional model, and we now explicitly state that UBP1 and TFCP2 associate with the Mediator complex through MED16.

(3) Domain mapping studies in Figure 2 are overinterpreted. Since the interactions could be indirect, it is not accurate to conclude "Therefore, the N-terminal WDR domain of MED16 is crucial for its integration into the Mediator complex, while the C-terminal αβ-domain is essential for interacting with UBP1-TFCP2."

We fully acknowledge that co-immunoprecipitation (co-IP) assays alone cannot discriminate direct physical binding from indirect protein associations mediated by intermediate partners. Nevertheless, our conclusion that MED16 directly interacts with UBP1 is supported by two orthogonal, independent experimental datasets.

First, GST pull-down assays using purified recombinant proteins expressed in E. coli confirm direct binding (Figure 2C). This cell-free biochemical system removes all potential cellular bridging factors, unambiguously demonstrating a physical contact between the C-terminal αβ-domain of MED16 and UBP1.

Second, our mutational functional analyses further rule out an indirect interaction model. Deletion of the unique 36-residue USP peptide in UBP1 completely abrogates MED16 binding (Figure 2F, comparison between ΔSAM and DBD truncations). Reciprocally, MED16 mutants lacking the C-terminal αβ-domain lose all capacity to associate with UBP1. Importantly, both truncation mutations yield identical functional defects in UBP1-driven and HIV-1 luciferase reporter assays (Figures 3G and 5G). If this complex assembly relied on an uncharacterized bridging protein, it would be statistically improbable for two distinct, structurally unrelated deletions (USP removal on the UBP1 side and αβ-domain truncation on the MED16 side) to independently disrupt the same indirect linkage and generate identical loss-of-function phenotypes.

Collectively, the congruent results from cell-free in vitro biochemistry and targeted mutational functional assays provide robust evidence for a direct, specific physical interaction between MED16 and UBP1.

(4) A close examination of Figure 2C undermines confidence in the association studies. The bait protein in lanes 5-8 should be equal. Also, there is significant binding of GST to UBP1 and TFCP2, in roughly the same patterns as they bind to GST-MED16 αβ. The absence of input samples makes the results even more difficult to interpret.

We acknowledge the technical limitations the reviewer pointed out. Regarding the concern about unequal protein loading across lanes 5-8, we note that lanes 7 and 8 in fact contain more GST-M16αβ bait protein than lanes 5 and 6, yet TFCP2L1 and YY1 still show no appreciable binding above the GST-alone background. This loading asymmetry therefore strengthens the conclusion that these proteins do not directly interact with MED16. For UBP1 and TFCP2, we have now provided quantification of the Western blot signals, which confirms a clear difference in binding to GST-M16αβ versus GST alone. Furthermore, these GST pull-down experiments were performed under stringent conditions—300 mM NaCl and 0.5% Tween-20 in the wash buffer—and the UBP1 and TFCP2 interactions with GST-M16αβ persisted under these conditions (lane 5-8), whereas binding to GST alone was minimal (lane 1-4). These technical details support the specificity of the observed interactions.

(5) The domain deletion mutants are utilized throughout the manuscript as evidence of the importance of the UBP1-MED16 interaction. However, in Figure 2F lanes 7 and 8, the delta-S mutant binds MED16 as well as full-length UBP1. This undermines much of the subsequent data and conclusions about specificity.

We believe the reviewer may have a misunderstanding about the experimental design. The delta-S (ΔSAM) mutant deletes the SAM motif, which is required for UBP1-TFCP2 heterodimerization, but retains the UBP1-specific sequence (USP) that mediates MED16 binding. The observation that ΔSAM still binds MED16 at levels comparable to full-length UBP1 is therefore not a discrepancy—it is the expected result and confirms that USP is the region responsible for MED16 interaction. The DBD mutant, which further removes USP, completely loses MED16 binding. Together, these deletion constructs delineate two separable interaction surfaces on UBP1: USP for MED16 binding and the SAM motif for TFCP2 heterodimerization (see Figure 2 G). The functional analysis of these domains is reflected in Figure 3B: ΔSAM, which retains MED16 binding but loses TFCP2 dimerization, shows approximately half the transcriptional activity of full-length UBP1, suggesting that both interactions contribute to full UBP1 function. To avoid similar confusion, we have renamed ΔS to ΔSAM，UBP1-SP to USP in the revised manuscript.

(6) Even if the delta-S mutant were defective for MED16 binding, the result in Figure 3B does not "confirm that MED16 is required for the transcriptional activity of UBP1,". Removal of that domain may have other effects.

We wish to first clarify a factual point: the delta-S mutant (ΔSAM) is not defective for MED16 binding. ΔSAM deletes the SAM motif that is required for UBP1-TFCP2 heterodimerization, but retains the UBP1-specific sequence (USP) that mediates MED16 binding. As shown in Figure 2F, ΔSAM binds MED16 at levels comparable to full-length UBP1. The mutant that loses MED16 binding is DBD, which further deletes USP.

The functional result in Figure 3B is therefore consistent with this biochemical mapping: ΔSAM retains MED16 binding but loses TFCP2 dimerization, and accordingly shows approximately half the transcriptional activity of full-length UBP1. This suggests that both the MED16 interaction (via USP) and the TFCP2 interaction (via the SAM motif) contribute to full UBP1 function.

More importantly, the conclusion that MED16 is required for UBP1 transcriptional activity does not rest on domain mutant analysis alone. It is supported by independent loss-of-function approaches: shRNA-mediated MED16 knockdown (Fig 3C) and CRISPR-mediated MED16 knockout across five independent frameshift clones (Fig 3E-F), both of which consistently reduce UBP1 reporter activity. The domain deletion mutants complement these approaches by mapping the specific interaction interfaces.

(7) As Mediator is critical for the activation of many genes, it is not accurate to assume that the impact of its deletion in Figure 3E/F demonstrates a direct requirement in UBP1-driven transcription. This could easily be an indirect effect.

MED16 knockout data must be interpreted cautiously due to potential Mediator destabilization artifacts. However, our conclusion does not rely solely on loss-of-function data; transient competitive overexpression and domain-mapping assays bypass chronic MED16 depletion entirely. The MED16Δαβ mutant retains full Mediator integration but loses UBP1 binding. Unlike wild-type MED16, this mutant fails to change UBP1 or HIV-1 reporter activity in 36–48 h transient assays performed in wild-type cells with intact endogenous Mediator. Dose titration further confirms that only UBP1-interacting MED16 competes for UBP1 binding to repress target promoters (Fig 3G). Since these experiments involve no permanent MED16 ablation, the observed transcriptional effects cannot be attributed to indirect global Mediator dysfunction, verifying specific MED16–UBP1 regulation.

(8) Without documenting the relative protein expression levels in Figure 3G/H, conclusions cannot be drawn about the titration experiments, nor the co-expression experiments. These findings are likely the result of squelching or some form of competition that is not directly related to the UBP1-mediated transcription. A great deal of validation would be required in order to support the model that these effects are a result of MED16 overexpression sequestering UBP1 away from holo-Mediator.

We thank the reviewer for this insightful comment. In fact, the squelching interpretation that the reviewer proposes is fully consistent with our functional model and helps reinforce a key conclusion of our study.

The reviewer correctly points out that overexpressed MED16 may compete with the endogenous Mediator complex for UBP1 binding, sequestering UBP1 away from the holo-Mediator and thereby inhibiting UBP1-driven transcription. This interpretation directly implies that UBP1 requires association with the intact Mediator complex—not merely free MED16—to activate transcription. This is precisely the model we advocate, and the squelching phenomenon observed in Figure 3G thus provides independent functional evidence for it.

The specificity of this effect is confirmed by the MED16 Δαβ mutant: the Δαβ mutant integrates into the Mediator complex normally but cannot bind UBP1, and consequently fails to exert any competitive inhibition on the UBP1 reporter (Fig 3G). This demonstrates that the squelching effect is specifically dependent on the MED16-UBP1 interaction interface. We have now documented the relative protein expression levels for these experiments in the revised manuscript.

(9) The lack of any documentation of expression levels for the various ectopic proteins in the majority of Figures, renders mechanistic claims meaningless (Figures 3, 4, 5, 6, 7, S2, S3). This is particularly relevant since the model presented for many of the results invokes concentration-dependent competition.

In the revised manuscript, we have now included Western blot data documenting the expression levels of ectopic proteins for the key experiments. The expression level data confirm that the proteins were expressed at the expected levels across the different conditions.

Recommendations for the authors:

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Reviewer #1 (Recommendations for the authors):

(1) The writing and presentation are generally good, except that some typos and mistakes in conceptual statements (e.g., lines 407-408 "WDR-deleted MED16, which cannot interact with UBP1") often confuse the readers.

We thank the reviewer for the careful reading. We have tried out best to correct the typos and misstatements, including the error in line 407-408 where "WDR-deleted MED16, which cannot interact with UBP1" should refer to the αβ-domain deletion rather than the WDR deletion. The whole manuscript has been extensively rewritten for better clarity and preciseness.

(2) Inconsistency in the citation format between numbering and author names should be avoided.

The citation format has now been unified throughout the manuscript.

(3) Two important scientific concepts based on the published literature should be mentioned:

(a) "The position-dependent function of transcription factors (TFs) relative to the TSS" (lines 427-428) is a well-known fact in the transcription field that partly explains gene activation versus gene repression; and

(b) the statement "JQ1 that is known to reverse HIV-1 latency by antagonizing BRD4's suppression of the Tat-P-TEFb/SEC (Super Elongation Complex) interaction" (lines 384-386) is only partially correct and is a property unique to the BRD4 long (BRD4-L) isoform.

We thank the reviewer for this suggestion. We have now cited the relevant literature on the position-dependent function of transcription factors relative to the TSS, including the recent study by Duttke et al. (3), which systematically demonstrated that the effect of TF binding on transcription initiation is highly position-dependent. Our findings provide a clear example that UBP1 activates transcription when its binding motif is located upstream of the TSS but represses when the motif overlaps the TSS, which exemplifying this concept.

We have corrected the statement to specify that JQ1 antagonizes the BRD4 long isoform (BRD4-L)-mediated suppression of Tat-P-TEFb/SEC, and have noted that the BRD4 short isoform (BRD4-S) may also contribute to HIV-1 promoter repression and JQ1-mediated latency reversal.

(4) Another relevant concept is that BRD4 short (BRD4-S) isoform-inhibited HIV-1 promoter activity could be potentially alleviated by JQ1, leading to latency reversal. Besides the aforementioned points and those comments already provided in the Public Review, the involvement of TFCP2 and YY1 in MED16-UBP1 function has not been clearly established and will require more careful and detailed investigation.

We thank the reviewer for these suggestions. Regarding BRD4-S, we have added a discussion of the BRD4 short isoform's role in HIV-1 promoter regulation and its potential contribution to JQ1-mediated latency reversal.

Regarding the involvement of TFCP2 and YY1, we agree that their precise roles within the MED16-UBP1 regulatory axis have not been fully dissected in the current study. Our data indicate that TFCP2 can dimerize with UBP1 to enhance transcriptional activation (Fig 3H), and YY1 is present in the MED16-containing fractions (Fig 1E), consistent with its previously reported role in HIV-1 silencing. However, the molecular details of how TFCP2 and YY1 contribute to MED16-UBP1 function—and whether they act in the same or parallel pathways—remain to be determined. We have acknowledged this as a limitation and a direction for future investigation in the revised Discussion.

Reviewer #2 (Recommendations for the authors):

(1) The data from Figure 1F are hard to interpret, the blot quality is poor for Med23, 16

We acknowledge that the blot quality for MED23 and MED16 in Figure 1F was suboptimal in the original submission. We have now provided better Western blot, which confirms the specific co-immunoprecipitation of MED16 and MED23 with TFCP2 in both HeLa nuclear extract and the gel filtration fractions. Importantly, the reciprocal co-IP (anti-MED16 IP blotted for TFCP2 and UBP1, Fig 1E) independently validates this interaction.

(2) Figure 2: No MW markers on gels. Also, these types of experiments are ok for pilot studies, but they aren't rigorous. Only a few proteins were tested, and it's easy to get false positives with how the experiments were completed. Finally, the Mediator proteins were tested as single isolated proteins rather than in their native context. As isolated proteins, they likely have large exposed hydrophobic patches (normally bound to other subunits), and this can generate non-specific "sticky" interactions that can lead to false positive results.

We have now included MW markers on the gel images in the revised Figure 2.

The reviewer raises a valid general concern about domain mapping experiments. However, we wish to emphasize that the readout in Figure 2B and 2F is the binding of exogenously expressed truncated proteins to their endogenous interaction partners—MED1, TFCP2, MED16, and MED23—which are natively folded and assembled in their physiological environment. This is not a situation where two isolated proteins are mixed in a test tube. Furthermore, the deletion series themselves contain important internal controls against non-specific "stickiness": In Figure 2B, progressive deletion of the WDR domains leads to a gradual reduction in MED1 binding, consistent with the predicted structural role of the β-propeller (WDR domain). The truncation at the αβ-domain specifically abolishes TFCP2 binding but does not affect its association with Mediator complex as indicated by MED1. If the truncated proteins were non-specifically sticky due to exposed hydrophobic patches, one would expect uniform binding across all truncations or random binding patterns, which is not observed. And in Figure 2F, deletion of the 36-amino-acid USP abolishes its MED16 binding, while deletion of the SAM motif does not. This sequence-specific differential effect is inconsistent with non-specific hydrophobic interactions.

The domain mapping experiments in Figure 2 were not designed as an unbiased screen but as hypothesis-driven tests guided by the IP-MS results identifying UBP1/TFCP2 as MED16 interactors, sequence and structural analysis predicting the roles of the WDR and αβ-domains. The conclusions from these experiments are corroborated by subsequent functional assays: the USP-deleted mutant and the MED16 Δαβ mutant show corresponding functional defects in both UBP1 reporter and HIV-1 reporter assays (Fig 3G, Fig 5G), providing strong support that the mapped interaction interfaces are functionally relevant.

(3) Figure 3: UBP1 reporter is artificial, 6X UBP1 sites upstream of a TATA box.

We appreciate this comment and wish to clarify a misunderstanding. The UBP1 reporter used in Figure 3 is not an artificial construct assembled from random elements. Its backbone is derived from the mouse α-globin gene promoter, a well-established natural target of UBP1/TFCP2, which contains two endogenous UBP1/TFCP2 binding sites. In order to increase the reporter's sensitivity to UBP1/TFCP2, we expanded the original two sites to six. Critically, this expansion did not alter the native architecture of the promoter—the relative positions of the transcription factor binding sites, the CCAAT box, the TATA box, and the TSS remain unchanged from the original α-globin promoter. This reporter therefore retains the physiological spacing and topological organization of a genuine UBP1 target promoter, and its low basal activity and high inducibility by UBP1 make it a well-suited tool for modeling UBP1 transcriptional activity. We have further clarified this description in the revised manuscript.

(4) Figure 3D: Med16 KD not compelling, perhaps 50% knockdown? Hard to tell because no replicates and no quantitation.

We acknowledge that the shRNA-mediated MED16 knockdown in Figure 3D was partial and that the original presentation lacked replicate quantification. We initially tested three independent shRNAs targeting MED16, of which only one achieved appreciable knockdown. Recognizing this limitation, we turned to a more definitive loss-of-function approach: CRISPR-Cas9-mediated MED16 knockout. Five independent frameshift KO clones were generated in mouse HT cells, each verified by sequencing and Western blotting (Fig 3F), and all five clones consistently showed reduced UBP1 reporter activity compared with wild-type cells (Fig 3E). The consistency between the shRNA knockdown and CRISPR KO reinforce the conclusion that MED16 is required for UBP1 transcriptional activity.

(5) Figure 3E: Med16 KO will be a different cell line because of genetic adaptation. That is, an RNA-seq experiment is expected to result in many gene expression changes compared to the parental line. This could contribute to differences, or differences could result from altered Mediator composition to compensate for Med16 loss, but this wasn't addressed by the authors. A rapid degron method would be much more rigorous.

We thank the reviewer for raising this important concern. We agree that prolonged MED16 loss can elicit cellular adaptation and compensatory changes in Mediator composition, as our own new data on tail module dissociation confirm. This makes it challenging to disentangle direct and indirect effects using constitutive KO models alone.

However, two independent lines of evidence support a direct role for MED16 in UBP1-mediated transcription that cannot be explained by adaptive responses:

First, acute shRNA-mediated knockdown produces the same phenotypic trend. shRNA operates on a shorter timescale (days) without prolonged selection for compensatory mutations, yet it also reduces UBP1 reporter activity (Fig 3C). The convergence of acute and chronic loss-of-function approaches suggests the phenotype is driven by MED16 loss itself rather than by the secondary adaptations that accumulate over time in KO cells.

Second, and most critically, the MED16Δαβ mutant experiment completely bypasses the issues of genetic adaptation and Mediator structural disruption (Fig 3G). This experiment is performed in wild-type cells with an intact endogenous Mediator complex, without any MED16 depletion and without any long-term selection. The MED16Δαβ mutant retains full ability to integrate into the Mediator complex (its WDR domain is intact) but cannot bind UBP1. Overexpression of wild-type MED16 competitively inhibits the UBP1 reporter due to the squelching effect, whereas overexpression of MED16Δαβ at comparable levels does not (Fig 3G). The sole molecular difference is that MED16Δαβ doesn`t contain the UBP1-binding interface. Because this experiment involves no MED16 loss and no adaptive period, the result directly demonstrates that MED16-UBP1 interaction is required for UBP1 transcriptional activity, entirely independent of concerns about clonal adaptation.

We appreciate the reviewer's suggestion of a rapid auxin-inducible degron approach. While acute depletion strategies offer clear advantages in minimizing cellular adaptation, they are not without limitations. First, degron-based depletion rarely achieves 100% elimination of the target protein, and residual protein may confound interpretation. Second, and particularly relevant to our system, degron-mediated degradation may preferentially target free, unassembled subunits while sparing proteins already stably integrated into large macromolecular complexes such as the Mediator—potentially creating a lag or even complete resistance to degradation for the pool of MED16 that is assembled into the complex. Given these considerations, we believe our convergent strategy—combining shRNA knockdown, CRISPR-mediated knockout in multiple independent clones, and the Δαβ mutant that bypasses structural perturbation—provides a robust and complementary set of evidence that does not rely on any single depletion method.

(6) The title for Figure 3 is "Med16 is required for UBP1 activation of gene transcription", but that's not conclusively shown by these experiments.

We agree that the original title of Figure 3 may overstate. We have revised the title to " MED16 acts through the Mediator complex to support UBP1-mediated transcriptional activation ", which may better reflect the data. As discussed in our responses above, this conclusion is supported by converging evidence from shRNA knockdown (Fig 3C), CRISPR-mediated KO across multiple clones (Fig 3E-F), and the specific loss of function observed with the MED16Δαβ mutant (Fig 3G).

(7) Figure 5: Med16 protein levels were never measured, nor were other transfected proteins. Reporter assay data are correlative only; no evidence for direct effects, and only 2 other MED subunits are probed. Again, this is a starting point, but nothing to use for concrete conclusions about Med16.

We have now provided Western blot data documenting MED16 and other transfected protein levels for the experiments in Figure 5, confirming that the proteins were expressed at the expected levels. We agree that plasmid-based reporter assays alone cannot establish direct transcriptional mechanisms. The HIV-1 reporter experiments in Figure 5 serve as an initial functional readout, and their conclusions are corroborated by more direct approaches: (i) the position-dependent specificity demonstrated by chimeric reporter assays (Fig 6A-C); (ii) the independence of the effect from TAR-mediated elongation and HDAC activity (Fig S2), ruling out alternative mechanisms; and (iii) the immobilized template transcription assays, which directly measure nascent RNA production and PIC assembly on the HIV-1 promoter (Fig 7). The reporter data should be viewed as one component of a larger body of convergent evidence rather than as standalone proof.

MED23 and MED24 were chosen as the most relevant controls because they, along with MED16, form the core of the tail module submodule that creates the transcription factor interaction platform. They are structurally adjacent to MED16 within the same submodule. The fact that neither MED23 nor MED24 overexpression affects HIV-1 reporter activity (Fig 5C), whereas MED16 overexpression does so in a UBP1-binding-dependent manner (Fig 5C, 5E), demonstrates that the inhibitory effect is specific to MED16 and not a generic consequence of overexpressing a Mediator tail subunit.

(8) Figure 6: similar concerns to Figure 5. The promoters are artificial, derived from a chicken beta-actin promoter with artificially inserted UBP1 binding sequences.

We acknowledge that the chimeric promoters in Figure 6 are indeed deliberately designed. To address this specific question: Does the binding position of the UBP1 relative to the TSS dictate whether UBP1-MED16 activates or represses transcription?

To isolate position as the sole variable, we needed a backbone promoter that (i) is stably and robustly active in the cell lines used, (ii) does not itself contain endogenous UBP1 binding sites that would confound the interpretation, and (iii) allows precise placement of the UBP1 binding motif either upstream of or overlapping the TSS. The chicken β-actin promoter meets all three criteria and is a widely used tool in molecular biology for such controlled promoter engineering experiments. Notably, its high GC content around the promoter region is also a feature shared with the HIV-1 core promoter, making it a particularly relevant backbone for the HIV-1 TSS chimeric constructs.

The key controls for this experiment are internal: in the same backbone, placing the UBP1 binding site at the TSS results in MED16-UBP1-dependent repression, whereas placing it upstream does not (Fig 6A vs 6B). Furthermore, this position-dependent effect requires the MED16-UBP1 interaction interface, as the MED16 Δαβ mutant and the UBP1 DBD mutant both fail to produce the inhibitory effect (Fig 6A). The differential outcome between the two constructs—which differ only in the placement of the UBP1 binding site—cannot be attributed to the artificial nature of the backbone, because the backbone is identical in both cases.

(9) Figure 6D: Not rigorous, no statistical analysis, cannot determine whether the modest changes are biologically relevant/meaningful. Also, data were obtained through indirect measurements and long timeframes, so any direct effects from possible UBP1 binding are probably lost.

The differentially expressed genes in Figure 6D were selected using DESeq2 with a significance threshold of p < 0.05. The top 50 upregulated and top 50 downregulated transcripts were then used for UBP1 motif enrichment analysis around their promoters. We have clarified these selection criteria in the revised figure legend.

Regarding the concern that indirect measurements over long timeframes, we now have additional evidence that UBP1 binding effects are preserved in our RNA-seq data. Motif analysis of UBP1-upregulated genes using HOMER identified the CP2 family binding motif (CNRG-N6-CNRG) as the most significantly enriched motif. This indicates that UBP1-binding-dependent transcriptional effects are not lost in our dataset.

Author response image 4.

Motif enrichment result of the UBP1 up-regulated genes

Furthermore, when these UBP1-upregulated and UBP1-downregulated genes are analyzed separately for motif position relative to the TSS, a clear pattern emerges: UBP1-upregulated genes show motif enrichment flanking the TSS, whereas UBP1-downregulated genes show enrichment overlapping the TSS (Fig 6D). If the transcriptional changes were non-specific secondary consequences of prolonged UBP1 overexpression, one would not expect this position-specific distribution. Finally, this positional specificity is corroborated by the chimeric reporter experiments (Fig 6A-C), where moving the UBP1 binding site across the TSS in an otherwise identical promoter directly switches the regulatory outcome. The concordance among the de novo motif discovery, the genome-wide positional analysis, and the functional reporter assays supports the biological relevance of the motif enrichment pattern.

(10) The title for Figure 6 is "UBP1 binding site determines the UBP1-Med16 inhibition in HIV-1 transcription" but the data do not convincingly show this.

We appreciate this suggestion. We have revised the title to "The position of the UBP1 binding site relative to the TSS dictates whether MED16-UBP1 activates or represses transcription.". For clarification, Figure 6 not only demonstrates that the UBP1 binding position dictates MED16-UBP1-mediated inhibition in the HIV-1 context, but also revealed that this positional effect could be generalized to endogenous genes: UBP1 motifs flanking the TSS are associated with activation, while motifs overlapping with the TSS are associated with repression.

(11) Figure 7: The data and the experiment do not support the claim in the title that "MED16-UBP1 complex prohibited PIC formation of HIV-1 transcription". I cannot convince myself that there are meaningful differences between the results shown in 7B, but it's hard to judge because there are no replicates and no quantitation.

We have revised the title from "MED16-UBP1 complex prohibited PIC formation of HIV-1 transcription" to "MED16 interferes with HIV-1 PIC assembly at the TSS via its interaction with UBP1." We have also provided quantification of the Western blot signals from replicate experiments in Figure 7B, which confirms statistically significant differences in CDK8 binding, Pol II pSer5 signals, and TFIIB retention between conditions. We note that the key observations in Figure 7B were consistently observed across multiple pilot experiments prior to the final dataset presented in the manuscript. Thus, the reported differences are reproducible and not based on a single experiment.

(12) The immobilized template experiments had only -78 upstream and +60 downstream of the TSS. By my understanding, much more upstream DNA is needed to allow a PIC to assemble, because the 5'-end bead attachment will block. I think this was outlined in an article by the Carey lab, but I'm not sure. A point here is that it would be reassuring for the authors to show that PIC assembly was occurring and that transcription was responsive to a transcription factor, similar to what the Carey lab has done with immobilized templates. See, for example, Figure 1 in Lin & Carey Curr Protocol Mol Biol 2012 Ch12 unit 12.14.

We thank the reviewer for raising this technical consideration. We respectfully offer a different perspective based on current structural data on the human PIC.

A recent cryo-EM study of the human Mediator-bound preinitiation complex (4) demonstrated that the PIC spans approximately 50 bp upstream and downstream of the TSS. The DNA templates used for structural determination in that study were generally within 105 bp upstream and 63 bp downstream of the TSS. Our HIV-1 template (-78 to +60, i.e., 78 bp upstream and 60 bp downstream of the TSS) falls within this well-characterized range and provides sufficient space for PIC assembly.

Regarding the choice of the -78 boundary: the HIV-1 core promoter is defined as -78 to +60, and the region from -78 to -105 encompasses the HIV-1 enhancer, which contains additional regulatory elements including NF-κB and NFAT binding sites. We deliberately excluded these enhancer elements to avoid confounding regulatory inputs and to focus specifically on the UBP1 binding site at the TSS, which is the central focus of our model. The robust luciferase mRNA production observed in wild-type nuclear extract (Fig 7C) provides direct functional evidence that PIC assembly and transcription initiation proceed efficiently on this template under our conditions.

Author response image 5.

Promoter templates used for human PIC assembly (Chen et al., Science 372, eaba8490, 2021): templates within −105 to +65 bp of the TSS support PIC formation

(13) Related to the above concern, the qPCR analysis from the extract experiments may be misleading because of contaminating nucleic acids in the extract. More control experiments are needed, such as no NTP controls.

We thought this concern has been addressed by our experimental design.

First, the PIC step in our experimental design (Fig 7B, "PIC") is the no-NTP control: nuclear extract is incubated with the immobilized template without NTPs. After washing, the proteins bound at this step are analyzed by Western blot, and importantly, there is no transcription occurred at this step. Transcription is then initiated by adding NTPs (Fig 7B, "Trx."), and the supernatant from this step is collected for qPCR analysis of transcription.

Second, it is unlikely that the contaminating nucleic acids from the nuclear extract could confound our qPCR results, because the qPCR analysis specifically detects Luciferase mRNA transcribed from the immobilized HIV-1-Luciferase template, which is absent from eukaryotic genomes; and the endogenous genomic DNA or RNA cannot generate a false-positive signal.

Lastly, after transcription, the immobilized templates are retained on the streptavidin beads and removed, while only the supernatant containing newly synthesized RNA is collected for qPCR. Any residual template DNA or extract-derived nucleic acids bound to the beads are therefore excluded from the qPCR sample.

(14) Some references are made with the format of (author name, year), but others use numbers.

The citation format has been unified throughout the manuscript.

(15) On line 111-115, it is stated that 2,5 HD somehow "does not interfere with weak hydrophobic interaction due to different positions of hydroxyls" with no reference. Both 1,6 HD and 2,5 HD are hydrophobic molecules, and they will disrupt protein structure. The authors make a point about the differential results with 1,6 HD vs. 2,5 HD, but it's not compelling and not justified.

We have now provided the reference to support this statement. The specificity of the 1,6-HD effect is further clarified as follows.

1,6-HD and 2,5-HD are structural isomers sharing the same chemical formula and molecular weight. The key difference lies in the positions of their hydroxyl groups (See Author response image 6). The position of the two hydroxyl groups changes both the molecule’s shape and how it interacts with water and hydrophobic surfaces.

In 1,6-HD, the two -OH groups sit at the ends of the chain, giving a more symmetric, flexible molecule, while in 2,5-hexanediol the -OH groups are closer to the middle, which changes polarity distribution and local geometry (5, 6). The distinctive structures matter because hydroxyl groups strongly hydrogen-bond with water. When they are terminal and well separated in 1,6-HD, the molecule can present a more balanced hydrophilic “cap” at both ends while keeping a relatively long hydrophobic center, which helps 1,6-HD partition into and disturb weakly interacting hydrophobic regions in condensates or hydrophobic interfaces (Author response image 6). By contrast, moving the hydroxyls inward in 2,5-HD does not help with disrupting the hydrophobic interfaces (Author response image 6). That is why 2,5-HD is often used as a comparison compound: it has the similar chemical formula, but the different hydroxyl pattern usually makes it a weaker or at least differently acting perturbant.

Author response image 6.

Differential disruption of hydrophobic interfaces by 1,6-HD vs 2,5-HD

(16) On lines 117-120, the authors claim that Med16 is "integrated into the Mediator complex through weak hydrophobic interaction but not ionic interaction" based upon a few IP results. They then state (lines 130-131) that "the interaction between Mediator and Med16 is an unstable hydrophobic interaction." These statements make no sense based on any data shown, and they ignore the fact that Med16 purifies with Mediator from many different purification protocols. It's safe to say that its interaction with Mediator results from strong, extensive hydrophobic interfaces, which is further supported by actual structural data. The authors should check their reasoning here because they are over-interpreting their results, and this will be misleading to readers.

We thank the reviewer for this important suggestion. The reviewer is right that our original phrasing—particularly "unstable hydrophobic interaction"—was imprecise and inconsistent with the established structural data. As the reviewer notes, MED16 co-purifies with the Mediator complex through multiple purification protocols, and recent cryo-EM structures (4) reveal that MED16 engages in extensive hydrophobic interfaces with neighboring tail module subunits, particularly MED24 and MED25. We fully agree that this is a strong, hydrophobic interaction in the physiological context.

Our 1,6-hexanediol experiments demonstrated that the MED16-Mediator interface does have a hydrophobic character, which renders the sensitivity to 1,6-HD disruption. This does not mean the interaction is weak. We have now carefully described the relevant statements in the revised manuscript.

Reviewer #3 (Recommendations for the authors):

(1) It is not accurate to claim that "198 (genes) were repressed by shMED16 knockdown (Fig 4B and 4C)". These genes were simply not activated by UBP1 in the knockdown cells.

We thank the reviewer for this careful distinction. We have revised the text to state that the UBP1-activated genes were “profoundly downregulated upon MED16 depletion” rather than “repressed by shMED16 knockdown”. The biological point remains unchanged: MED16 is required for UBP1 to activate this set of target genes.

(2) Like the majority of experiments presented, the RNA-seq presented in Figure 4 may reflect indirect effects of MED16 loss. As such, the results do not support the claim that "This result demonstrated that UBP1 and MED16 collaborate to regulate transcription".

We acknowledge that RNA-seq data from MED16 knockdown cells alone cannot distinguish direct from indirect effects. However, we did not rely on the RNA-seq data alone to support a collaborative role for UBP1 and MED16.

The key evidence comes from experiments comparing wild-type MED16 with the MED16Δαβ mutant. MED16Δαβ integrates into the Mediator complex normally but cannot bind UBP1 (Fig 2B). When overexpressed in wild-type cells, wild-type MED16 inhibits the UBP1-driven reporter activity through a squelching effect. In contrast, MED16Δαβ has no effect on the UBP1 reporter assay (Fig 3G), and the same is true for the HIV-1 reporter assays (Fig 5G). Thus, MED16 must both integrate into the Mediator complex and directly bind UBP1 to support UBP1-mediated transcription.

In addition, the genes identified as UBP1-MED16 co-regulated by RNA-seq are enriched for specific biological processes—angiogenesis (Fig 4D-E)—that align with the known physiological functions of UBP1. Such functional coherence would be unexpected if the transcriptional changes were merely non-specific secondary consequences of Mediator disruption.

Thus, while we agree that RNA-seq alone has limitations, the convergent evidence from the MED16Δαβ mutant and the functional specificity of the co-regulated gene set supports a collaborative role for UBP1 and MED16 in transcriptional regulation.

(3) The data in Figure 4 are not presented with controls documenting the relative expression levels of MED16 and UBP1. For example, it would be important to understand the level of UBP1 overexpression achieved, relative to endogenous UBP1 levels in HeLa cells.

We agree with the reviewer that documenting expression levels is important. Author response image 7 are the CPM values for UBP1 from our RNA-seq data, confirming robust overexpression in the UBP1-overexpression condition compared with the control. The MED16 protein levels in the knockdown cells can be found in Fig 3D, as the same MED16-knockdown HeLa cell line was used for the RNA-seq experiment.

Author response image 7.

UBP1 expression level derived from RNA-seq

Regarding the physiological relevance of UBP1 overexpression, several observations support that the transcriptional effects we observe are specific rather than artifacts of overexpression: (i) the UBP1-activated genes are enriched for pathways known to be regulated by UBP1—angiogenesis (Fig 4D-E)—rather than showing random, non-specific activation; (ii) the activation of these genes is attenuated upon MED16 knockdown, demonstrating dependence on the MED16-UBP1 interaction; and (iii) in reporter assays, the MED16 mutant lacking its C-terminal αβ-domain fails to competitively inhibit UBP1 driven reporter transcription even when UBP1 is similarly overexpressed (Fig 3G), indicating that the competitive inhibition of the UBP1 reporter depends specifically on the MED16-UBP1 interaction interface, rather than on the amount of UBP1 protein overexpressed.

(4) The enhancer-promoter architecture of the luciferase construct used in Figure 3 is not sufficiently described. Are the elements far enough apart that Mediator-dependent looping is required for transcription, for example?

We appreciate the reviewer's question. The UBP1 reporter construct used in Figure 3 is derived from the mouse α-globin gene promoter, a well-established natural target of UBP1/TFCP2(7, 8). The native α-globin promoter contains two endogenous UBP1/TFCP2 binding sites; to increase the reporter's sensitivity to UBP1, we expanded these to six tandem copies. Critically, this expansion preserved the native architecture of the promoter—the relative positions of the UBP1 binding sites, the CCAAT box, the TATA box, and the TSS were not altered. The entire reporter construct spans only 198 bp in total length. At this scale, all regulatory elements reside within a compact proximal promoter region, with no element separated by a distance that would require DNA looping for functional communication. The reporter therefore measures UBP1-dependent transcriptional activation from the proximal promoter, consistent with the canonical role of Mediator in facilitating PIC assembly rather than mediating long-range enhancer-promoter interactions. We have added a detailed description of the construct architecture to the Methods section.

(5) The identification of matches to the UBP1 consensus sequence in a promoter does not prove that this is how UBP1 overexpression is impacting their transcription. "highly matched UBP1 motifs were identified in their promoters (Fig. 4F), leading to their activation when UBP1 was overexpressed."

We agree with the reviewer that the presence of a UBP1 consensus motif in a promoter does not by itself prove direct regulation. We have revised the original statement: the activation of these genes by UBP1 overexpression is now described as "associated with" the presence of UBP1 motifs in their promoters.

We acknowledge that the ideal experiment to demonstrate direct UBP1 occupancy would be ChIP-seq. However, ChIP-grade antibodies against UBP1 are not commercially available, and no UBP1 ChIP-seq datasets exist in public databases. We attempted to carry out the ChIP-seq ourselves but were unable to obtain sufficiently good-quality data.

In the absence of ChIP data, three lines of evidence indicate that the identified UBP1 motifs are functionally relevant. First, motif analysis of UBP1-upregulated genes using HOMER identified the CP2 family binding motif (CNRG-N6-CNRG) as the most significantly enriched motif. This demonstrates that UBP1-binding-dependent transcriptional could be preserved in our RNA-seq data. Second, when we examine the positional distribution of these motifs, a clear pattern emerges: UBP1 motifs flank the TSS in activated genes, but overlap the TSS in repressed genes (Fig 6D). Indirect effects would not produce this position-specific pattern. Third, our chimeric reporter experiments (Fig 6A-C) directly test this position effect: moving the UBP1 binding site upstream of the TSS leads to activation, while moving it to overlap the TSS leads to repression. Together, these three independent approaches support the conclusion that UBP1 regulates these genes through the motifs we identified. See Author response image 4.

(6) Lines 266 and 277 are redundant.

We have carefully reviewed lines 266 and 277. Line 266 is the topic sentence (caption) of the section ("MED16 collaborates with UBP1 to inhibit HIV-1 transcription"), which introduces the overall conclusion, while line 277 describes the specific experimental result ("MED16 inhibited HIV-luciferase activity in a dose-dependent manner"). These serve distinct rhetorical functions. We have ensured that no other redundant phrasing exists elsewhere in the section.

(7) The mere correlation of binding site position with activation status does not prove "that UBP1 may act as either a transcriptional activator or repressor, depending on distance of its binding site to TSS."

We appreciate the reviewer's concern regarding the distinction between correlation and causation. The genome-wide analysis (Fig 6D) reveals an association between UBP1 motif position and transcriptional outcome, which prompts us to postulate that the UBP1 binding position could dictate the transcriptional activity level. The causal evidence comes from the chimeric reporter experiments (Fig 6A-C), in which we directly manipulated the position of the UBP1 binding site relative to the TSS in an otherwise identical promoter background. Placing the UBP1 binding site at the TSS resulted in MED16-UBP1-dependent repression, whereas placing it upstream of the TSS did not. This controlled experiment demonstrates that changing only the position of the UBP1 binding site is sufficient to switch the regulatory outcome, thereby establishing a causal relationship between binding site position and transcriptional effect. We have revised the text to clearly distinguish the correlational genome-wide analysis from the causal reporter experiments.

(8) In Figure 7, MED16 overexpression results in less CDK8 binding. This undermines the claim that MED16 overexpression lowers transcription by binding to UBP1, and suggests an indirect effect.

We appreciate the reviewer's careful observation. The reduction in CDK8 binding upon MED16 overexpression is consistent with our model: MED16, through UBP1 occupying the TSS, interferes with PIC assembly, of which CDK8 is a component. Importantly, the input levels of CDK8 and other Mediator subunits remained unchanged across the three conditions (Fig 7B), indicating that the reduced CDK8 signal in the PIC is not due to altered protein expression.

In support of the specificity of the transcriptional effect, MED16Δαβ—which integrates into the Mediator complex but cannot bind UBP1 (Fig 2B)—fails to competitively inhibit either the UBP1 reporter (Fig 3G) or the HIV-1 reporter (Fig 5G), confirming that the transcriptional outcome depends on the MED16-UBP1 interaction.

(9) Figure 8F is not referenced in the text or legend.

Figure 8F has now been referenced in the Results and Discussion section.

Reference:

(1) Wang G, Cantin GT, Stevens JL, Berk AJ. Characterization of mediator complexes from HeLa cell nuclear extract. Mol Cell Biol. 2001;21(14):4604-13.

(2) Yamazaki T, Souquere S, Chujo T, Kobelke S, Chong YS, Fox AH, et al. Functional Domains of NEAT1 Architectural lncRNA Induce Paraspeckle Assembly through Phase Separation. Molecular Cell. 2018;70(6):1038-+.

(3) Duttke SH, Guzman C, Chang M, Delos Santos NP, McDonald BR, Xie J, et al. Position-dependent function of human sequence-specific transcription factors. Nature. 2024;631(8022):891-8.

(4) Chen X, Yin X, Li J, Wu Z, Qi Y, Wang X, et al. Structures of the human Mediator and Mediator-bound preinitiation complex. Science. 2021;372(6546).

(5) Zheng T, Wake N, Weng SL, Perdikari TM, Murthy AC, Mittal J, et al. Molecular insights into the effect of 1,6-hexanediol on FUS phase separation. EMBO J. 2025;44(10):2725-40.

(6) Romero CM, Páez MS, Miranda JA, Hernández DJ, Oviedo LE. Effect of temperature on the surface tension of diluted aqueous solutions of 1,2-hexanediol, 1,5-hexanediol, 1,6-hexanediol and 2,5-hexanediol. Fluid Phase Equilibr. 2007;258(1):67-72.

(7) Lim LC, Swendeman SL, Sheffery M. Molecular cloning of the alpha-globin transcription factor CP2. Mol Cell Biol. 1992;12(2):828-35.

(8) Chae JH, Kim CG. CP2 binding to the promoter is essential for the enhanced transcription of globin genes in erythroid cells. Mol Cells. 2003;15(1):40-7.

Author response:

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

Our revision includes:

(1) The generated data from long-read whole-genome sequencing of 1000 Genomes Project samples, including FASTQ files, SV calls, and the imputation panel, are now openly available via ENA and OpnMe. The imputed structural variant data have been submitted to UK Biobank for release through the UK Biobank Research Analysis Platform, subject to UK Biobank release procedures. SV-WAS summary statistics have been made available via OpnMe.

(2) Clarification of analyses and methods, addition of two new Supplementary Figures, and correction of minor issues throughout the manuscript.

(3) A significantly expanded Discussion to address the reviewers’ comments and better contextualise our methods and results.

eLife Assessment

This fundamental work significantly enhances our understanding of how structural variants influence human phenotypes. The conclusion is convincingly supported by rigorous analyses of long-read sequencing data. If the raw data are made publicly available, these high-quality datasets and findings will further advance our knowledge of genetic variation in the human population.

We thank the editors for this positive assessment of our work. The raw long-read sequencing data (FASTQ files) can now be accessed through the European Nucleotide Archive (ENA) under accession number PRJEB89727, as part of a larger collection of 1019 sequenced probands from the 1000 Genomes Project (https://www.ebi.ac.uk/ena/browser/view/PRJEB89727). The generated imputation panel and the structural variant calls, based on the 888 probands used in the present manuscript, remain freely available for download at https://opnme.com/genomiclens. We have now added the summary statistics of 32 SV-wide association studies to the same resource. In addition, we have submitted the imputed SV genotypes for UK Biobank participants to the UK Biobank; once processed by UK Biobank, these genotypes will be released via the UK Biobank Research Analysis Platform (RAP).

Public Reviews:

Reviewer #1 (Public review):

Summary:

The authors sequenced 888 individuals from the 1000 Genomes Project using the Oxford Nanopore long-read sequencing method to achieve highly sensitive, genome-wide detection of structural variants (SVs) at the population level. They conducted solid benchmarking of SV calling and systematically characterized the identified SVs. While short-read sequencing methods, including those used in the 1000 Genomes Project, have been widely applied, they exhibit high accuracy in detecting single nucleotide variants (SNVs) and small insertions and deletions but have limited sensitivity for SV detection. This study significantly enhances SV detection capabilities, establishing it as a valuable resource for human genetic research. Furthermore, the authors constructed an SV imputation panel using the generated data and imputed SVs in 488,130 individuals from the UK Biobank. They then conducted a proof-of-principle genome-wide association study (GWAS) analysis based on the imputed SVs and selected traits within the UK Biobank. Their findings demonstrate that incorporating SV-GWAS analysis provides additional insights beyond conventional GWAS frameworks focusing on SNVs, particularly in improving fine mapping.

The authors constructed a high-sensitivity reference panel of genome-wide SVs at the population level, addressing a critical gap in the field of human genetics. This resource is expected to significantly advance research in human genetics. They demonstrated the imputation of SVs in individuals from the UK Biobank using this panel and conducted a proof-of-concept SV-based GWAS. Their findings highlight a novel and effective strategy for integrating SVs into GWAS, which will facilitate the analysis of human genetic data from the UK Biobank and other datasets. Their conclusions are supported by comprehensive analyses.

We thank the reviewer for highlighting the value of our SV imputation reference panel.

Weaknesses:

(1) Although the authors employ state-of-the-art analytical approaches for the identification of SVs, the overall accuracy remains suboptimal, as indicated by an F1 score of 74.0%, particularly in tandem repeat regions. To enhance accuracy, it would be beneficial to explore alternative SV detection methods or develop novel approaches. Given the value of the reference panel and the fact that improved SV accuracy would lead to more precise SV imputation and GWAS results, investing effort in methodological refinement is highly encouraged.

Accurate SV calling remains an active area of research and is beyond the scope of the present study. Tandem repeat regions are particularly challenging for standardised SV detection. We believe that achieving a benchmark for NA12878 of F1 = 74% on a genome-wide level and, notably, F1 = 91% when excluding longer tandem repeats, represents strong performance. This result is especially convincing when considering that our benchmarking compared the SV calls to data generated using a different sequencing technology and processed using different bioinformatics pipelines.

(2) From the Methods section, it appears that the authors employed Beagle for both imputation and the UK Biobank imputation.

(a) It would be better to explicitly clarify this in the Results section and provide a detailed description of the corresponding procedures and parameters in the Methods section for both analyses, as this represents a key aspect of the study.

We thank the reviewer for these suggestions. Accordingly, we added the clarification to the Methods section that the leave-one-out imputation used exactly the same pipeline and settings as the UK Biobank imputation (page 14, section “Leave-one-out imputation performance”):

“We excluded one individual from the panel and imputed SVs for this individual using the panel of the remaining 887 samples, applying exactly the same pipeline and settings as those later used for SV imputation into UK Biobank (see below).”

(b) Additionally, Beagle is not specifically designed for SV imputation, the imputation quality of SVs is generally lower than that of SNVs. Exploring strategies to improve SV imputation, such as developing a novel method with reference panel data, may enhance performance.

As stated in our manuscript (page 4), we believe that, in our study, the imputation quality of SVs is lower than of that of SNVs primarily because of a) the greater difficulty of SV calling compared to SNV genotype calling and b) the heterogeneity in SV representation across samples. Once SVs are encoded as bi-allelic markers in the reference panel, they can be imputed using the same LD/haplotype-based framework as any other variants. Accordingly, improving SV imputation is likely to benefit most from more accurate upstream SV calling and genotyping (e.g., through more robust multi-sample calling and harmonised variant representations) and not so much from improved or SV-specific imputation methods. While improved imputation is an important research direction, it is beyond the scope of the present manuscript.

(c) It is also important to assess how this reduced imputation quality may influence GWAS results. For instance, it would be useful to examine whether associated SVs exhibit higher imputation quality and whether SVs with lower quality are less likely to achieve significant association signals. In addition, the lower imputation quality observed for INV, DUP, and BND variants (Figure 3) may be due to their greater lengths (Figure 2). It is better to investigate the relationship between SV length and imputation quality.

We agree that imputation quality can influence GWAS results. For example, for the FEV1/FVC phenotype, SVs with INFO > 0.9 are almost twice as likely to reach genome-wide significance (p < 5e-8) compared with SVs with 0.7 < INFO < 0.9 (odds ratio 1.95; Fisher’s exact test p-value 2.5e-5). This is consistent with the intuitive notion (applicable to any variants, not only to SVs) that greater uncertainty in the imputed genotypes dilutes association signals and therefore reduces power. For a detailed discussion of the relationship between allele frequency, imputation accuracy, and GWAS association results, see Zhang et al., Human Molecular Genetics 31(1):146–155 (2022), https://doi.org/10.1093/hmg/ddab203

We have now investigated the relationship between SV length and imputation quality (the new Supplementary Figure 6). The results suggest that the observed association between imputation quality and SV size is primarily driven by the SV-size–dependent minor allele frequency in the imputation panel.

(3) All examples presented in the manuscript focus on SVs that overlap with genes. It may also be valuable to investigate SVs that do not overlap with genes but intersect with enhancer regions. SVs can contribute to disease by altering regulatory elements, such as enhancers, which play a crucial role in gene expression. Including such analyses would further demonstrate the utility of SV-GWAS and provide deeper insights into the functional impact of SVs.

We agree with the reviewer that examining SVs intersecting with enhancer regions could be an interesting direction for future studies, as it would provide additional insights into regulatory mechanisms and disease associations. However, in the present proof-of-principle study, we prefer focusing on SVs overlapping with genes and have now highlighted this in additional detail in the revised manuscript (Discussion, page 7):

“In the present proof-of-principle study, we focused on SVs overlapping with the coding sequence of genes. In future applications of our SV imputation panel, more refined gene mapping approaches could be employed, e.g., including SVs overlapping enhancer regions or epigenetic marks. Such an enhanced mapping would increase the number of identified associated genes and thus provide additional insights into regulatory mechanisms and disease biology.”

(4) The data availability link currently provides only a VCF file ("sniffles2_joint_sv_calls.vcf.gz") containing the identified SVs.

(a) It would be beneficial for the authors to make all raw sequencing data (FASTQ files) and key processed datasets (such as alignment results and merged SV and SNV files) available. Providing these resources would enable other researchers to develop improved SV detection and imputation methods or conduct further genetic analyses.

Thank you for emphasising the importance of data sharing, which we agree with.

The Data Availability section of the manuscript already includes a link to https://opnme.com/genomiclens, where we made both the SV calls and the full and reduced SV imputation panel files freely available. We have now added SV summary statistics from 32 SVwide association studies to the same resource. Based on the reviewer’s request, we now also reference the ENA repository project PRJEB89727 (https://www.ebi.ac.uk/ena/browser/view/PRJEB89727), where the raw FASTQ files are available for download, in the manuscript.

We have appended the Data Availability statement on page 22 of the revised manuscript as follows:

“Raw SV calls, the long-read sequencing-based SV imputation panel, and the SV summary statistics from 32 SV-wide association studies are available through the OpnMe initiative of Boehringer Ingelheim GmbH (https://opnme.com/genomiclens). The raw long-read sequencing data (FASTQ files) for the 1000 Genomes Project samples included in this study are accessible via the European Nucleotide Archive under accession number PRJEB89727 (https://www.ebi.ac.uk/ena/browser/view/PRJEB89727). The dataset analysed here constitutes a subset of this broader collection.”

(b) Furthermore, establishing a dedicated website for data access, along with a genome browser for SV visualization, could significantly enhance the impact and accessibility of the study. Additionally, all code, particularly the SV imputation pipeline accompanied by a detailed tutorial, should be deposited in a public repository such as GitHub. This would support researchers in imputing SVs and conducting SV-GWAS on their own datasets.

The Methods section provides a full and detailed description of the imputation pipeline and parameters in the section “Preprocessing and imputation of SVs into UK Biobank” on page 14 of the revised manuscript. Our data processing simply consisted of running standard bioinformatics tools with the parameters exactly as described in the manuscript.

Reviewer #1 (Recommendations for the authors):

(1) In the Results section, Figure 3b is mentioned before 3a, and it is better to switch them in the Figure.

Thank you for highlighting this fact. We acknowledge that typically the sequence of sections matches exactly between text and figures. However, in this specific case, we would prefer to deviate from the norm: In our opinion, Figure 3 is easier to interpret in its current sequence. At the same time, the text flows more logically in its current sequence, describing 3b before 3a. We would therefore prefer to stick to the current order, even if it means that Fig. 3b is described before 3a in the text.

(2) Page 10, "Figure 1e" -> "Figure 2e".

Thank you, we corrected this issue.

(3) Page 14, "Leave-one out" -> "Leave-one-out".

Thank you, we corrected this mistake.

(4) It is better not to use abbreviations in the subheadings, especially "UKB" (page 3).

Thank you, we changed the acronym ‘UKB’ to ‘UK Biobank’ in all subheadings.

Reviewer #2 (Public review):

Summary:

The authors aimed to develop a novel and efficient method for SV detection, utilizing data from the 1000 Genomes Project (1KGP) for modeling and calibration. This method was subsequently validated using UK population data and applied to identify structural variants associated with specific disease phenotypes.

Strengths:

Third-generation single-molecule sequencing data offers several advantages over traditional high-throughput sequencing methods, particularly due to its long-read lengths, which provide valuable insights into significant forms of genomic variation. The authors have developed an efficient method for detecting structural variations and optimizing the utilization of genomic data. We hope that this method will continue to be refined, enabling researchers to more effectively leverage long-read data, high-throughput data, or even a synergistic combination of both.

Weaknesses:

Although this research contributes to our ability to more effectively utilize long-length and high-throughput data, there are some key issues that need to be addressed in terms of analyzing the specific results as well as writing the article.

Reviewer #2 (Recommendations for the authors):

(1) How to discuss the lower detection rate of structural variations (SVs) in East Asian populations, it is worth considering whether the authors' training dataset, which may have been based on raw data with insufficient representation of East Asian individuals, could have introduced a bias favoring other populations. This potential bias might arise from the relatively limited data available for Asian ancestry. Alternatively, the observed differences could also be influenced by the role of natural selection, which may have shaped the genomic landscape of East Asian populations in distinct ways. Further investigation is needed to clarify these possibilities.

Thank you for raising this important point. Although an interesting research direction, a detailed investigation of the factors affecting SV detection rates is beyond the scope of the present study. However, we do not think that the lower detection rate in East Asians is due to an underrepresentation of Asian ancestry in our dataset. To explain this to all readers, we have added the following explanation to page 7 of the Discussion:

“In this context, we observed that the number of SVs detected per individual differed between superpopulations. We identified the highest average number of SVs in individuals of African descent and a slightly lower average in East Asians, compared to the other superpopulations. While we included a higher number of African ancestry individuals, the number of East Asian individuals included in our reference panel was comparable to the number of individuals from other, non-African ancestries. In fact, it was even larger than the number of European ancestry individuals (AFR n=241, SAS n=171; EAS n=168; EUR n=164; AMR n=144). Therefore, we do not expect a major bias from underrepresentation of any superpopulation in the training dataset. It is well established that African ancestry is more diverse than is the case for other superpopulations [32, 33] and previous studies indicate that East Asian populations tend to exhibit slightly lower genetic diversity compared to European populations [34], which is consistent with the lower observed SV counts per genome.”

(2) The authors did not present the results of the detection of CNV.

Copy number variations (CNVs) are considered a subclass of structural variants. In our analysis, we detected deletions and duplications, which represent the most common forms of CNVs. However, we did not specifically investigate high copy-number SVs, as these are often larger than what can be reliably detected using long-read sequencing. Large-scale CNVs are typically identified in biobank studies through analysis of intensity data from genotyping microarrays using tools like PennCNV, and there is extensive literature supporting the use of this microarray approach in UK Biobank and other genotyped cohorts, see for example Aguirre et al.: Phenomewide Burden of Copy-Number Variation in the UK Biobank. Am J Hum Genet. 2019, Aug 1;105(2):373-383. doi:10.1016/j.ajhg.2019.07.001.

(3) Multiple testing correction is essential for ensuring the validity of large-scale structural variation (SV) association analyses. It is strongly recommended that the statistical methods and correction strategies employed, such as Bonferroni correction or false discovery rate (FDR) control, be explicitly detailed to enhance the transparency and reliability of the findings.

For genome-wide SV association analyses, we applied the commonly used genome-wide significance threshold of 5e-8, which is standard in genome-wide studies. Given that these were exploratory proof-of-principle analyses illustrating use cases for SV analyses, we decided not to correct on top of that for multiple testing for the number of traits (32) tested. For the pQTL analyses, we further adjusted this threshold using a Bonferroni-type correction based on the number of proteins tested (1,463), to account for the increased number of multiple comparisons.

We have now added a more detailed description of this multiple testing procedure to the Methods subsection “SV-wide association studies in UK Biobank” on page 16 of the revised manuscript:

“In the exploratory SV-WAS, we used the standard threshold for genome-wide significance of p < 5×10^-8. For the pQTL analyses, we applied Bonferroni correction for multiple testing on top of that genome-wide threshold, correcting for the number of tested protein levels (n=1463): p < 5×10^-8/ 1463 = 3.4×10^-11.”

(4) The study primarily relied on data from the 1000 Genomes Project (1KGP) and the UK Biobank; however, the UK Biobank cohort is predominantly composed of individuals of European ancestry, which may restrict the generalizability of the research findings to other populations.

Our reference panel was constructed to cover multiple ancestries, enabling imputation for diverse populations. Thus, our imputation panel can be applied to biobanks around the world and is freely available for this purpose. As a proof of principle, we have demonstrated the feasibility and performance of SV imputation in UK Biobank as an example of a broadly accessible cohort. We are looking forward to biobanks from diverse ancestries downloading our imputation panel and applying it to their populations.

(5) Although the study employed long-read sequencing technology, the validation of structural variation (SV) detection accuracy predominantly relied on internal data, such as 'leave-one-out' validation. To further strengthen the reliability of the SV detection methods, it is recommended to incorporate additional external independent datasets for validation.

The leave-one-out procedure in our study was used to validate the imputation performance, not the accuracy of SV detection. To assess SV calling accuracy, we performed extensive benchmarking against external SV call datasets derived from PacBio long-read sequencing and Illumina short-read sequencing. These details are provided under the subheading ‘Structural variant calling and benchmarking’ in the Results section on page 2 of the manuscript.

(6) Some of the SVs mentioned in the study overlap with disease association loci in the GWAS Catalog, but functional annotation and exploration of the biological mechanisms of these SVs are more limited. It is suggested that LD can be added to analyse whether there are SNP that are highly linked to them to further explore their functions.

We thank the reviewer for this suggestion. We have actually conducted an analysis addressing exactly this question: We performed conditional association analyses of the SV signals with nearby short variants (SNPs and InDels) at the SV locus. Such a conditional analysis addresses whether the observed SV association is influenced by LD-correlated SNPs or not. The results of this analysis are reported in Supplementary Tables 16 and 17. These tables include both the conditional analysis results and the LD between each SV and the variant at the locus with the second-highest evidence for an association.

Researchers interested in exploring the biological significance of the SV-WAS results in more detail can now download the full SV-WAS summary statistics from https://opnme.com/genomiclens.

(7) The discussion section could be further expanded to explore the role of SV in complex diseases and its potential application in precision medicine. For example, it could discuss how SV information can be integrated into existing GWAS frameworks to enhance the accuracy of disease risk prediction.

Thank you for the suggestion, we have now added the following sentences to the discussion (page 7/8):

“Structural variants can influence complex disease biology through either the disruption of coding sequence or an altered regulation of gene expression. Such effects may not be well captured by short variants alone. Incorporating SVs into GWAS and follow-up analyses would thus provide more accurate disease risk prediction, uncover underlying pathomechanisms by highlighting actionable pathways and targets, and support precision medicine by providing biomarkers for patient stratification.”

(8) The geographic labeling of certain samples in Figure 2 appears to contain inaccuracies. For instance, the CDX sample, which represents the Dai population from Xishuangbanna in China's Yunnan Province, is currently mislabeled as originating from China's Inner Mongolia. This discrepancy should be corrected to ensure the accuracy of the data representation.

We apologise for the misunderstanding. The geographic map in Figure 2a serves as an illustrative mapping of the samples to countries. It is intended to provide readers with an overview of population coverage, rather than to indicate the precise geographic origins of individual populations. The populations CDX, CHB, and CHS are displayed within the outline of China in alphabetical order, without any intention to indicate their exact geographic origin. We changed the respective figure caption to make this clear (page 19 of the revised manuscript):

“Map of the 888 samples from the 1000 Genomes project, mapping the samples to countries and not indicating detailed geographical origins of populations.”

Reviewer #3 (Public review):

This study successfully identified genetic loci associated with various traits by generating large-scale long-read sequencing data from a diverse set of samples. This study is significant because it not only produces large-scale long-read genome sequencing data but also demonstrates its application in actual genetics research. Given its potential utility in various fields, this study is expected to make a valuable contribution to the academic community and to this journal. However, there are several critical aspects that could be improved. Below are specific comments for consideration.

Strengths:

Producing high-quality, large-scale variant datasets and imputation datasets

Weaknesses:

(1) Data availability

Currently, it appears that only the Genomic Lens SV Panel is available on the webpage described in the Data Availability section. It is unclear whether the authors intend to release the raw sequencing data. Since the study utilized samples from the 1000 Genomes Project, there should be no restriction on making the data publicly accessible. Given this, would the authors consider making the raw sequencing reads publicly available? If so, NCBI SRA or EBI ENA would be the most appropriate repositories for data deposition. I strongly encourage the authors to consider public data release. Additionally, accessing the Genomic Lens SV Panel data does not seem straightforward. The manuscript should provide a more detailed description of how researchers can access and utilize these data. In my opinion, the best approach would be to upload the variant data (VCF files) to a public database such as the European Variation Archive (EVA) hosted by EBI.

I strongly request that the authors publicly deposit the variant data. At a minimum:

(a) The joint genotype data for all 888 samples from the 1000 Genomes Project must be publicly available.

Thank you for emphasising the importance of data sharing, which we agree with.

The Data Availability section of the manuscript already includes a link to https://opnme.com/genomiclens, where we make both the SV calls and the full and reduced SV imputation panels (provided as multi-sample VCF files) freely available. Based on the reviewer’s request, we now also reference the ENA repository project PRJEB89727 (https://www.ebi.ac.uk/ena/browser/view/PRJEB89727), where the raw FASTQ files are available for download.

We have appended the Data Availability statement on page 22 of the revised manuscript as follows:

“Raw SV calls, the long-read sequencing-based SV imputation panel, and the SV summary statistics from 32 SV-wide association studies are available through the OpnMe initiative of Boehringer Ingelheim GmbH (https://opnme.com/genomiclens). The raw long-read sequencing data (FASTQ files) for the 1000 Genomes Project samples included in this study are accessible via the European Nucleotide Archive under accession number PRJEB89727 (https://www.ebi.ac.uk/ena/browser/view/PRJEB89727). The dataset analysed here constitutes a subset of this broader collection.”

(b) For the UK Biobank samples, at least allele frequency data should be disclosed.

Supplementary Table 5 includes the allele frequencies of the SVs imputed into UK Biobank.

(c) Since eLife has a well-established data-sharing policy, compliance with these guidelines is essential for publication in this journal.

By sharing the FASTQ files, the SV calls, the SV imputation panels, the SV summary statistics, and (once processed by UK Biobank) the genotypes of SVs imputed into UK Biobank, we are providing all SV data generated in our study.

(2) Long-read sequencing data quality

While the manuscript presents N50 read length and mean or median read base quality for each sample in a table, it would be highly beneficial to visualize these data in figures as well. A violin plot or similar visualization summarizing these distributions would significantly improve data presentation.

Notably, the base quality of ONT long-read sequencing data appears lower than expected. This may be attributed to the use of pore version 9.4.1, but the unexpectedly low base quality still warrants attention. It would be helpful to include a small figure within Figure 2 to illustrate this point. A visual representation of read length distribution and base quality distribution would strengthen the manuscript.

We thank the reviewer for this suggestion. We have now included two violin plots (the new Supplementary Figure 1) to the revised manuscript, summarising a) the N50 read length per sequencing run and b) the median read quality per sequencing run. These plots provide a clearer visualisation of the underlying distributions. We do not consider the ONT base quality to be low. Importantly, structural variant detection is generally robust to modest variations of per-base quality. Therefore, we do not expect the observed base quality levels to significantly affect SV calling in this study.

(3) Variant detection precision, recall, and F1 score

This study focuses on insertions and deletions (indels) {greater than or equal to}50 bp, but it remains unclear how well variants <50 bp are detected. I am particularly interested in the precision, recall, and F1 score for variants between 5-49 bp.

While ONT base quality is relatively low, single-base variants are challenging to analyze, but variants {greater than or equal to}5 bp should still be detectable as their read accuracy is still approximately 90%, making analysis feasible. Given that Sniffles supports the detection of variants as small as 1 bp, I strongly encourage the authors to conduct an additional analysis.

A simple two-category classification (e.g., 5-49 bp and {greater than or equal to}50 bp) should suffice. Additionally, a comparative analysis with HiFi and short-read sequencing data would be highly valuable. If possible, I strongly recommend that all detected variants {greater than or equal to}5 bp be made publicly available as VCF files.

Because short InDels are available from high-coverage Illumina sequencing data generated for the same individuals (i.e., the data referred to as the NYGC dataset in our manuscript), we decided against calling such short variants from our lower coverage Oxford Nanopore data and thus concentrated our efforts on reliably calling longer variants covering at least 50 bp, consistent with the conventional definition of structural variants.

(4) Assembly-based methods

Given the low read accuracy and low sequencing depth in this dataset, it is understandable that genome assembly is challenging. However, the latest high-quality human genome datasets-such as those produced by the Human Pangenome Reference Consortium (HPRC)demonstrate that assembly-based approaches provide significant advantages, particularly for resolving complex and long structural variants.

Since HPRC data also utilize 1000 Genomes Project samples, it would be highly informative to compare the accuracy of ONT sequencing in this study with HPRC's assembly-based genome data. The recent publication on 47 HPRC samples provides a valuable reference for such a comparison. Given its relevance, the authors should consider providing a comparative analysis with HPRC data.

The aim of the present study was to generate an SV reference panel that enables SV imputation for large biobanks. Detailed assessments of ONT sequencing quality in general and comparisons to other sequencing efforts and technologies are out of scope for the present manuscript. We invite the scientific community to use the FASTQ files provided at ENA for conducting such detailed assessments in follow-up studies.

I found it interesting that economic mobility can vary so dramatically from one neighborhood to another within the same city. We often talk about inequality as if it is primarily an individual or family issue, but this whole article goes to show that inequality can also be geographic. As we've been reading all week, where someone lives determines what resources and opportunities are available to them. This makes me continue to think about how policies focused only on helping individuals aren't enough. If the underlying conditions of a community remain unchanged, people may continue to face the same barriers even when they receive individual assistance.

Author response:

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

eLife Assessment:

This study provides important findings on the expression of glutamate receptor (GluR) subunits across developmental stages and muscle types in Drosophila. It shows that adult muscle differs in GluR composition from larval body wall muscles, which have been the focus of most past studies. The study, while convincing, could be strengthened by acknowledging that it relies on heterogeneous methods and the absence of positive signals to infer receptor loss, which limits confidence in some of its claims. The findings illuminate how Drosophila excites muscles in diverse tissue types at different life stages, and are of interest to researchers across neuroscience.

A note on the eLife assessment

We are grateful for the assessment and for the reviewers' engagement. The assessment notes that the study "could be strengthened by acknowledging that it relies on heterogeneous methods and the absence of positive signals to infer receptor loss." We have taken this seriously and have addressed it in three ways in the revised manuscript:

(i) We have replaced claims of absence with "not detected" throughout;

(ii) We have added a paragraph describing the discrepancies between methods and the specific false-negative risks of each; and

(ii) We have made explicit the internal positive controls that constrain our negative results, including the reciprocal GluRIIB/GluRIIC labeling within a single femur and the detection of Brp, Neto-β, and GluClα in the same flight muscle preparations in which GluRII subunits were not detected.

Public Reviews:

Reviewer #1 (Public review):

Summary:

The manuscript by Sustar et al. takes a methodical approach to document the types of glutamate receptor subunits that reside in Drosophila muscles, examining developmental stages spanning from larvae to adults. Prior work thoroughly documented the subunits operating in Drosophila larval body wall muscles. Most subsequent research focused on the glutamate receptor heterotetramers found in the body wall, composed of GluRIIA/C/D/E or GluRIIB/C/D/E subunits, along with auxiliary subunits like isoforms of Neto.

For the current work, the authors report that the larval muscle glutamate receptor composition is not universal for all Drosophila muscles. They examine the following muscle systems: larval body wall, adult abdomen, adult leg coxa, and adult indirect flight. They also briefly examine adult muscle structures associated with the proboscis, neck, and haltere. The authors find that the receptor subunits in the adult abdomen (mostly) match those in the larval body wall. This makes sense given that the adult abdominal muscles are derived from the larval body wall. Yet not much else matches the larval body wall. For example, all (or most) of the GluRII-type subunits are missing from the adult indirect flight muscles. Leg muscles have GluRII-type subunits, but they do not have all of them expressed prominently, and they are missing GluRIIB. Additionally, leg muscles express a glutamate-gated chloride channel, which could be a source of inhibitory glutamatergic transmission. Interestingly, when it comes to non-abdominal adult muscles, one general theme seems to be an active promoter (GAL4 driver) for the kainate-type glutamate receptor called Clumsy. The authors propose that Clumsy could be key to understanding how functional GluR complexes are assembled in adult insects.

Strengths:

(1) Documenting the types of glutamate receptors that operate in diverse insect muscle systems is important because it uncovers fundamental information.

(2) Much of the prior research focus has been on how the body wall muscle tetramers assemble and operate. It is a strength to demonstrate the other receptor solutions used by adult NMJs.

(3) The work uses GAL4 drivers and immunohistochemistry (when possible) in combination to draw conclusions.

(4) The muscle anatomical analyses are of high quality. This allows the research group to reach refined conclusions.

(5) The confocal-level images of synaptic active zones and their apposed glutamate receptor clusters are of high quality.

Weaknesses:

(1) There is a strawman argument that is used repeatedly to highlight the significance of the work. The argument implies that the field broadly assumes (or “tacitly” assumes) that the larval body wall glutamate receptor composition extrapolates to all muscles of the fly, including the adult. This reviewer cannot find evidence that this assumption or argument has been explicitly promulgated by others. More likely, others have not examined these muscles directly, and thus, they have not speculated one way or the other.

The reviewer is correct that we could not find a paper stating explicitly that "the adult NMJ is molecularly identical to the larval NMJ," and we have revised the text to avoid implying that such an explicit claim exists. However, we do argue that larval body-wall findings are routinely presented as properties of "the Drosophila NMJ," "the fly NMJ," or "Drosophila muscle". That unqualified generalization is what has led readers (ourselves included) to extrapolate the canonical larval architecture to the adult.

Many concrete examples can be found in the literature. He and Dickman (2025, Curr Opin Neurobiol) state that "two subtypes of ionotropic glutamate receptors (GluRs) mediate postsynaptic currents in Drosophila muscle, GluRIIA- and GluRIIB-containing," and describe their regulation by Neto as a general feature of "the fly NMJ". The word "adult" does not appear in the review. Chou et al. (2020, Neural Development) similarly assert that "at the Drosophila NMJ, iGluRs are heterometric tetramers composed of three invariant subunits, GluRIII/GluRIIC, GluRIID, and GluRIIE, as well as one of either GluRIIA or GluRIIB". A highly cited review of these receptors is titled "Glutamate receptors at the Drosophila neuromuscular junction" (DiAntonio, 2006) yet describes only the larval body-wall system, and Harris and Littleton (2015, Genetics) introduce the larval NMJ as "a well-established model glutamatergic synapse" before discussing "the fly NMJ" throughout. Notably, we could not find a review paper about Drosophila neuromuscular control that discussed differences in receptor composition between larval and adult muscles.

This assumption is related to the genesis of this project, which came about due to the failure of pharmacological tools used in the larva (e.g., philanthotoxin) to block synaptic transmission at adult fly muscles. We (the Tuthill Lab) contacted several principal investigators studying adult fly motor control and within the larval NMJ field (including now co-author Dion Dickman) and asked for advice about why these drugs were not effective in paralyzing leg muscles. Nobody suggested that this could be because adult muscles use different glutamate receptors than the larvae. Indeed, it was only years later when we noticed a high level of GluCl expression in the FlyCellAtlas data that we realized it could be due to differences in receptor expression.

We agree with the reviewer that adult muscle has rarely been examined directly (Rivlin et al., 2004 being the principal exception, which we cite and now discuss at greater length). Our argument is that this gap has been filled by an untested extrapolation from larvae rather than by data. Of the ~50 papers citing Rivlin et al. (2004), we could not find any that compare glutamate‑receptor subunit expression between larval and adult muscle. Follow‑up work pursued NMJ morphology, remodeling, adhesion molecules, and transporters, leaving the receptor question open.

Overall, we respectfully disagree with the reviewer that this argument is a strawman, because it reflects our lived experiences as active investigators of adult and larval fly motor control. However, we take the reviewer’s point. We have removed language implying that an explicit model was being overturned, and we now frame the assumption as implicit and not universally held. We note only that the assumption was operative in practice: this project began when pharmacological tools that reliably block transmission at the larval NMJ (e.g., philanthotoxin) failed to paralyze adult leg muscles, and when we consulted colleagues who work on the larval NMJ and adult fly motor control, differences in receptor composition were not among the explanations offered. We recognize this is an anecdote rather than evidence, and we have kept it out of the manuscript.

(2) Related - to the extent that there has been any tacit assumption about GluRIIC/D/E-anchored receptors being ubiquitous among adult muscles, tacit doubt was raised by Rivilin et al., 2004 (cited by the authors but not as a source of doubt) and by RNAseq datasets like FlyAtlas from 2022 (replicated in Figures s11 and s12). To be clear, the current analysis is better than a bulk transcript analysis from adult tissues. But rather than “overturning” a field or being paradigm-shifting, the current data seem confirmatory of FlyAtlas - and confirmatory of Rivlin et al., 2004, which explicitly concluded that larval and adult NMJs were different

Rivlin et al. did not examine GluRIIC, D and E, or most of the other glutamate receptor subunits. Nevertheless, we revised the beginning of our Discussion (pg 8) to position our work in the context of their important findings:

In 2004, Rivlin and colleagues conducted a careful survey of NMJs in seven muscles in the adult Drosophila thorax. They established that adult NMJs are morphologically distinct from larval NMJs, and that GluRIIA and GluRIIB are expressed in muscle-specific subsets, with some muscles mysteriously lacking both. Importantly, they speculated that some adult muscles must be using different glutamate receptor subunits (which were unknown at the time) to build synapses. This problem has remained unexplored for the last two decades.

As the reviewer requested, we have removed "overturning"/"paradigm-shifting" language throughout. But we respectfully disagree that our analysis is “confirmatory” of the Fly Cell Atlas. The Fly Cell Atlas (Li et al., 2022) does not mention glutamate receptors, or the NMJ, anywhere in its analysis. It is a general single-nucleus transcriptomic resource whose adult-muscle glutamate-receptor content was never extracted, curated, or interpreted. Extracting meaning from the dataset required posing the question, curating the relevant cells and genes, and analyzing them, which is itself a meaningful scientific contribution.

(3) One can draw expression-level conclusions from these data. But genetic tests (e.g., would clumsy losses of function impair leg muscles?) could help the authors and the field draw stronger conclusions about the roles of some of these glutamate receptor gene products. The current dataset falls short of definitively establishing the function of alternate glutamate receptor modules.

We intend to perform functional and behavioral experiments with clumsy loss-of-function flies. However, this work will require creation of new genetic reagents and behavioral experiments that make it beyond the scope of this manuscript. We intend to address this important topic in a future paper.

(4) The confocal synaptic images are of high quality. They are good enough that one could analyze how well Brp directly apposes a specific glutamate receptor subunit for all the associated imaging data underlying Figures S1-S8. No such analysis is done, but understanding what components seem to directly oppose the site of release could lead to better conclusions.

In all tissues where IIA-E are expressed at the NMJ, the protein localization is directly adjacent to Brp (see representative images in Figure 2B and s5-8). This localization is often clear in single z-slices. We attempted to perform more detailed analyses, like measure the distance between Brp and GluR puncta, but found it very challenging due to the 3D orientation of the NMJ structure. We added a sentence to page 4 of the manuscript describing what we see and the overall similarity of IIA-E localization.

Overall Assessment and Discussion:

The data in this study are of high quality, and the results support the main conclusion: adult muscle glutamate receptor clusters do not recapitulate the “canonical” larval body wall clusters. This is important, and the data stand on their own. That is the most important part. This reviewer does have suggestions on how to put the current work in proper context; the current draft appears to overstate the novelty of the findings. Additionally, some sentences need editing for accuracy. None of those concerns impeach the excellent foundational data.

Reviewer #2 (Public review):

Summary:

This manuscript presents a broad survey of glutamate receptor composition at the neuromuscular junction in Drosophila across developmental stages and muscle types. The topic is clearly important, and the central observation-that adult muscles differ substantially from the canonical larval NMJ-is interesting and potentially impactful. The dataset is extensive and will likely be of value to the community. However, in my view, there are significant limitations in how the data are generated and interpreted, which at present reduce the strength of the conclusions.

Strengths:

The study addresses a relevant and timely question and provides a large and systematic dataset. The finding that adult muscles diverge from larval NMJ organization is compelling and challenges a widely held assumption in the field. The breadth of approaches, including genetic reporters, immunohistochemistry, endogenous tagging, and transcriptomic data, is, in principle, a strong aspect of the work and allows for a broad overview of receptor expression across tissues and developmental stages. Even in its current form, the manuscript provides useful descriptive information that will be of interest to the community.

Weaknesses:

A major concern is the reliance on a heterogeneous combination of detection methods (GAL4 reporters, antibody staining, endogenous tagging, and RNA), which are treated largely as equivalent lines of evidence. These approaches differ substantially in what they measure and in their sensitivity and specificity. While convergence across methods can in principle be convincing, here this convergence is often inferred from the shared absence of signal. This is problematic because all methods used are susceptible to false negatives for different reasons. As a result, the repeated conclusion that specific GluR subunits are “absent” from adult muscles, including those previously considered essential, is not fully justified by the data presented.

This issue is not only theoretical. The manuscript itself seemingly contains examples where methods disagree, demonstrating that detection is incomplete and method-dependent. These discrepancies could be better integrated into the interpretation. Instead, negative results across methods are often taken as strong evidence for absence, which overstates the certainty of the findings.

In addition, antibody validation appears to rely largely on prior work in larval tissue. Given the structural and biochemical differences in adult muscles, it is not clear that staining performance is equivalent, particularly in cases where the signal is weak or undetected. This further complicates the interpretation of negative results.

More generally, the manuscript moves in several places from descriptive observations to functional or mechanistic implications that are not directly supported. The suggestion that adult muscles operate with fundamentally different receptor assemblies is intriguing, but remains speculative without functional validation. At a minimum, the distinction between observation and interpretation should be made more explicit.

I thus think that the current conclusions need to be more carefully constrained. Ideally, the study would be strengthened by at least one functional experiment, such as electrophysiological recordings from adult NMJs or perturbation of candidate receptors like GluClα or Clumsy. This would help to anchor the expression data in synaptic function.

We thank the reviewer for a careful and constructive critique. We agree that inference from the absence of signal requires caution, and we have revised both the wording and the framing of the manuscript substantially in response. We would also like to draw attention to a feature of our dataset that we did not previously make explicit, and which we believe speaks directly to the core concern: a number of our negative results are internally controlled by positive signal from the same reagent, in the same tissue, in the same preparation.

(i) In the adult femur, anti-GluRIIB labels NMJs on tibia extensor fibers but not on accessory tibia flexor fibers within the same bisected femur, processed, stained, and imaged together (Figure 3C-D).

(ii) Anti-GluRIIC shows the reciprocal pattern in the same preparations (Figure 3E-F). The failure to detect GluRIIC in the tibia extensor therefore cannot be attributed to a general failure of that antibody in adult tissue, to fixation, or to reagent penetration, because the same antibody labels NMJs tens of microns away in the same section.

(iii) In indirect flight muscle, where we detected none of the five GluRII subunits, we reliably detected Brp, Neto-β::sfGFP, and GluClα:V5 at and around NMJs in the same preparations (Figures 2B, 2D, 4C). Reagent access, epitope preservation, and NMJ identification are therefore all demonstrated in the same tissue where our negative results are strongest.

These controls do not exclude the possibility that receptors are present below our detection threshold, and we have accordingly replaced "absent" with "not detected" throughout the manuscript. They do, however, argue that the muscle-specific differences we report reflect genuine biological variation rather than method failure. We have added a paragraph to the Discussion making this argument explicitly, alongside a new paragraph describing the discrepancies between methods, and we have added a description of antibody validation to the Methods.

In summary, this is an interesting and potentially important study, but the current manuscript somewhat overinterprets heterogeneous and partly indirect evidence. It will already be useful in its present form, but could be more convincing if the authors more rigorously account for methodological limitations and moderate their claims accordingly.

Reviewer #3 (Public review):

The Sustar et al. manuscript catalogs glutamate receptor composition across distinct Drosophila NMJs: larval and adult abdominal NMJs, as well as NMJs on adult leg and flight muscles. This work is important and probably overdue. The larval NMJ is the exemplar NMJ in this system, and the identity of “essential” and “alternative” subunits at this stage is assumed by many to hold across developmental stages and NMJ types. Here, the authors show that there is surprising diversification among NMJ types and that the notion of essential/alternative subunits only holds true at larval NMJs.

The study will generate interest in the Clumsy GluR subunit, which has not been well-characterized at all, but is widely expressed at adult NMJs. They also find striking extrasynaptic expression of glutamate-gated chloride channel GluRClalpha in adult leg and flight muscles, raising questions about its role. The study is interesting, logical, and well-written. The figures are clear, and the discussion was particularly thoughtful. I have a couple of comments that the authors could consider.

(1) They cite Rivlin et al., (2004) in the Introduction as the sole previous study to investigate the molecular composition of adult NMJs, but do not mention this work again. In the Discussion, it would be helpful to compare/contrast their finding with those of the earlier work.

Thank you for the suggestion. We have revised the beginning of our Discussion (pg. 8) to position our work in the context of Rivlin et al.’s important findings.

(2) Were these analyses done in adults of consistent ages? It seems possible that the GluR subunit composition could be different in very young adults or in aged flies. The age of the animals should be mentioned in the Methods.

Thank you for noticing this gap. We added age of flies to the Methods section, including the important detail that in cases where we failed to detect any GAL4 signal (e.g., GluRIID-GAL4), we additionally imaged very young and very old flies (0-2 hours old and 20-day-old). It did not change the results.

(3) The broad expression of GluCl:V5 in adult leg and flight muscles is surprisingly robust and appears to light up the edges of all muscle fibers. Would the authors comment on the controls that were done to ensure that this staining is real and specific to animals carrying that V5 endogenous tag?

We added a sentence to the results section (pg 8) to highlight the V5 negative staining controls that are shown in Figure s15.

(4) The snRNAseq data in Figure S12 differ a bit from the IHC/GAL4 data summarized in the table in Figure 2. In particular, the data suggests that Ukar and Grik are widely expressed in adult muscles. Is there a reason not to include an “snRNA seq” column in Figure 2 alongside the data from GAL4 lines and IHC? To my mind, it is about as reliable as GAL4 lines that often capture only a subset of the full expression pattern. In this case, the snRNAseq data suggest that Ukar/Grik are likely at adult flight muscle NMJs, which might be important since NMJ was negative for everything except Neto-beta by IHC.

We liked your suggestion to put these data together in one figure, and we tried to incorporate this during our revisions. However, because of the difficulty of combining multiple types of data into one table, we ultimately decided to keep them separate to avoid any confusion. The GAL4 analysis is qualitative (no expression, weak expression, strong expression) in percent of muscles. The RNA-seq data is quantitative and measured in fraction of muscle cells. Figure s13 now shows RNA-seq results in a table format that is parallel to the table with GAL4 results in Figure 2.

We also added a paragraph to the end of the discussion to mull several discrepancies in results (e.g. Grik and Ukar) when using different methods.

We did observe some discrepancies across the different experimental approaches. For GAL4 reporter lines, we used T2A gene trap lines where possible (for 15 of the 16 GluR genes) to determine receptor expression. However, some of these reporters were extremely weak and may have resulted in false negatives. For example, we did not detect Grik-GAL4 or Ukar-GAL4 expression in any tissue (Figure 2C), despite RNA-seq evidence that these are expressed robustly in adult muscles (Figures s11, s12). We do not have antibodies or protein reporters for these genes to help resolve this. Another discrepancy was with GluRIIE. In this case, antibody staining and RNA-seq did not detect GluRIIE in flight muscles (Figures s8, s11), while the GAL4>GFP reporter showed extremely faint signal in the flight muscles. Because of the marginal signal and the discrepancy with the other methods, we believe this could likely be a false positive. The table in Figure 2 does not effectively capture the nuance of this otherwise confusing result. Overall, however, we found that results from different approaches generally agreed and revealed intriguing differences between different muscle types.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Most of these recommendations are for text edits. Where experiments are noted (#8 and #9 below), they could be helpful, but they are not essential because the study has value as is.

(1) It would be appropriate to scrub the entire manuscript of statements that say that the work is overturning an incorrect model about larval GluRII receptor tetramers working the same way in adult muscles. First, it is not necessary. But more importantly, by this reviewer’s reading, there is not an explicit model promoted by others that the larval body wall findings extrapolate to other muscles. The better way to frame the work is to state that it clearly shows the field has a lot of work to do to properly characterize glutamate receptor composition and function in Drosophila adults. Places in the text that the authors should edit include:

- “...challenging assumptions about the uniformity of neuromuscular function” (Abstract)

We deleted this clause.

- “...it is often tacitly assumed...This extrapolation overlooks...during metamorphosis.” (Introduction)

New wording: … “…it has commonly been assumed…” (Abstract) and “…we and others assumed…” (Intro)

- “(With one notable exception, Rivlin et al., 2004)” (Introduction). This reference deserves more than an obscure parenthetical because it explicitly concluded that larval and adult NMJs differ.

As described above, we revised the beginning of our Discussion (pg 8) to position our work in the context of Rivlin et al.’s important findings.

In 2004, Rivlin and colleagues conducted a careful survey of NMJs in seven muscles in the adult Drosophila thorax. They established that adult NMJs are morphologically distinct from larval NMJs, and that GluRIIA and GluRIIB are expressed in muscle-specific subsets, with some muscles mysteriously lacking both. Importantly, they speculated that some adult muscles must be using different glutamate receptor subunits (which were unknown at the time) to build synapses. This problem has remained unexplored for the last two decades.

- “Collectively, these results overturn the assumption of NMJ uniformity...” (Introduction)

New wording: Collectively, these results reveal a diversity in NMJ composition”

- “Our findings challenge the assumption...” (Conclusions)

We deleted this clause.

(2) (Related) The authors quibble in a couple of places that the GluRIIC/D/E subunits have been “previously considered essential for viability and NMJ function.” This reviewer’s understanding of those subunits has always been that they are essential for life, and indeed, they are essential because null mutants arrest as embryos. The places where the text seems to combine viability and NMJ function (including the Abstract) as incorrectly assigned roles for these subunits, should be more carefully edited. This reviewer agrees with the “NMJ function” conclusion since the authors are considering so many NMJs. Viability still holds.

We agree with the reviewer, and we thank them for catching an imprecision that recurred throughout the manuscript. GluRIIC, GluRIID, and GluRIIE are essential for viability, and nothing in our data contradicts that conclusion.

We think the point we were trying to make is narrower and sharper when stated precisely. Null mutants for these subunits arrest as embryos — that is, they die before the adult leg and flight muscles are formed. Those experiments therefore established a requirement for viability and for larval NMJ function, but they could not, in principle, have tested whether the same subunits are required at NMJs that arise only during pupal development. Our data do not revise the viability conclusion. They show that the subunit requirement established at the larval body-wall NMJ does not generalize to every NMJ in the animal.

We have decoupled "viability" from "NMJ function" throughout the manuscript (Abstract, Introduction, Discussion) and have added a sentence to the Discussion making the developmental logic explicit:

Importantly, because these mutants die before metamorphosis, these experiments established a requirement for viability and for larval NMJ function, but could not test whether the same subunits are required at adult NMJs, which are formed during pupal development.

(3) “...the physiology and molecular architecture of adult fly NMJs remain largely unexplored...” The authors cite the Rivilin paper that examined the prothorax. But physiology has certainly been examined at DLMs as well as proboscis NMJs.

As the manuscript says on page 2, the topic is largely unexplored compared to the larva. The Rivlin paper is an excellent contribution but was conducted over 20 years ago with more limited genetic reagents. There were also no follow-up studies. In the same amount of time, over 1000 papers have been published regarding the Drosophila larval NMJ.

The reviewer is correct that physiology has been performed in adult DLMs and proboscis muscles. These studies, however, have focused on other biological questions and did not investigate the makeup of the NMJ or manipulate glutamate receptors with pharmacology or genetic tools. Our study reveals the need for such experiments.

(4) “Surprisingly, we found that none of the primary GluRII subunits was strongly expressed in adult indirect flight muscles...” This sentence was difficult to parse when simultaneously examining the large dot for GluRIIE-Gal4 in the IFMs (Figure 2C), until the realization that the blank IHC result was driving the conclusion (no expression). The authors may want to delineate Gal4 vs. IHC for each dataset to avoid confusion for readers.

We agree with the reviewer that this result is confusing. GluRIIE-GAL4 expression was a case in which a dot in the table didn’t capture the subtlety of the result. The GluRIIE-GAL4 was expressed very faintly in the IFM, to a degree that we almost called it negative.

We added a paragraph to the Discussion in which we reflect on some data discrepancies:

We did observe some discrepancies across the different experimental approaches. For GAL4 reporter lines, we used T2A gene trap lines where possible (for 15 of the 16 GluR genes) to determine receptor expression. However, some of these reporters were extremely weak and may have resulted in false negatives. For example, we did not detect Grik-GAL4 or Ukar-GAL4 expression in any tissue (Figure 2C), despite RNA-seq evidence that these are expressed robustly in adult muscles (Figures s11, s12). We do not have antibodies or protein reporters for these genes to help resolve this. Another discrepancy was with GluRIIE. In this case, antibody staining and RNA-seq did not detect GluRIIE in flight muscles (Figures s8, s11), while the GAL4>GFP reporter showed extremely faint signal in the flight muscles. Because of the marginal signal and the discrepancy with the other methods, we believe this could likely be a false positive. The table in Figure 2 does not effectively capture the nuance of this otherwise confusing result. Overall, however, we found that results from different approaches generally agreed and revealed intriguing differences between different muscle types.

(5) “GluClalpha in adult muscles establishes the molecular identity of inhibitory glutamate responses described decades ago in other insects...” This reviewer really likes this idea. But the current data fall far short of the conclusion in this sentence.

You are correct. We tempered this statement to “The identification of extrasynaptic GluClα in adult muscles establishes a possible mechanism for inhibitory glutamate responses described decades ago […]”

(6) “One past study (Han et al., 2015) explored many combinations....” Nothing in this sentence is untrue. This reviewer just wanted to point out that one interesting observation from the Han paper was that an A/E combination alone yielded significant function in the heterologous system. To the extent that A and B have been described as competitive for the same C/D/E core, it is not a stretch to imagine that a B/E combination would have significant function, just like A/E. Or B/D/E as well.

We thank the reviewer for this observation, which we think materially strengthens the plausibility of our interpretation, and we have incorporated it into the Discussion. Han et al. (2015) found that GluRIIA and GluRIIE together were sufficient to reconstitute functional receptors in a heterologous system, without GluRIIC or GluRIID. Because GluRIIA and GluRIIB are thought to compete for the same position within the tetramer, there is no obvious reason a GluRIIB/IIE or GluRIIB/IID/IIE complex should not also be functional. This provides a concrete precedent for exactly the kind of non-canonical combinations our expression data imply — for example, GluRIIB in the absence of detectable GluRIIC in tibia extensor fibers. We have added the following to the Discussion (p. 9):

Notably, Han et al. (2015) found that GluRIIA and GluRIIE alone were sufficient to reconstitute functional receptors, without GluRIIC or GluRIID. Because GluRIIA and GluRIIB are thought to occupy the same position within the tetramer, this raises the possibility that GluRIIB-containing complexes lacking GluRIIC — such as the GluRIIB/IID/IIE combination implied by our data in the tibia extensor — could likewise be functional. Neto-β, which is required for receptor gating and synaptic clustering (Han et al., 2024; Kim et al., 2012), is expressed at all adult NMJs we examined (Figures 2D, 3B), so the auxiliary subunit requirement for such complexes would be satisfied. Direct tests of these subunit combinations by heterologous reconstitution are an important next step.

(7) GluClalpha roles: The idea of a negative feedback controller is a good one. An alternative idea can be gleaned from the NMJ anatomy of circuits like the Mauthner Cell Escape Circuit in zebrafish. In that circuit, the fish have excitatory connections on some muscles and simultaneous control of inhibitory connections wired for other muscles to enable fast changes of direction.

We thank the reviewer for this interesting comparison. We think the Mauthner arrangement is unlikely to apply here, for two reasons. First, GluClα appears to be expressed broadly across the leg and flight muscles we examined, rather than in a subset complementary to the excitatory receptors. Second, and more importantly, GluClα is extrasynaptic: it is distributed along the periphery of the muscle fiber and is not apposed to Brp-positive active zones (Figure 4C-D). Target-specific inhibitory transmission of the kind used in the Mauthner circuit requires inhibitory receptors positioned at synapses, whereas the localization we observe is better suited to tonic or slowly varying modulation of muscle excitability. We have added a sentence to the Discussion making this distinction, since the reviewer's question is one that readers will also have. And add to the manuscript, at the end of the GluClα hypothesis paragraph in the Discussion:

We note that this arrangement differs from circuits in which excitatory and inhibitory transmission are targeted to different muscles to produce rapid directional control, as in the Mauthner cell escape circuit of larval zebrafish. While most arthropods possess GABAergic motor neurons that directly inhibit leg muscles, holometabolous insects such as Drosophila do not (Witten and Truman, 1998). And because GluClα is extrasynaptic rather than apposed to active zones, it is unlikely to support fast, target-specific inhibitory transmission.

Two optional experimental suggestions:

(8) The authors’ findings with Clumsy expression along with Clumsy message expression in the FlyAtlas RNAseq datasets - and finally, the unpublished work on Clumsy - all collectively suggest that it is a great target for adult knockdown. It is not required, but the authors’ conclusions would be bolstered if they were to test RNAi against Clumsy in chosen adult NMJs and check behavior (e.g., walking?) for defects.

We intend to perform functional and behavioral experiments with clumsy loss-of-function flies. However, this work will require creation of new genetic reagents and behavioral experiments that make it beyond the scope of this manuscript. We intend to address this in a future paper.

(9) The confocal synaptic images are of high quality. They are good enough that one could analyze how well Brp directly apposes a specific glutamate receptor subunit for all the associated imaging data underlying Figures S1-S8. No such analysis is done, but understanding what components seem to directly oppose the site of release could lead to better conclusions.

In all tissues where IIA-E are expressed at the NMJ, the protein localization is directly adjacent to Brp (see representative images in Figure 2B and s5-8). This localization is often clear in single z-slices. We attempted to perform more detailed analyses, like measure the distance between Brp and GluR puncta, but found it very challenging due to the 3D orientation of the NMJ structure. We added a sentence to page 4 of the manuscript describing what we see and the overall similarity of IIA-E localization.

Reviewer #2 (Recommendations for the authors):

The authors should revise the wording throughout to more clearly distinguish between “absence” and “not detected,” in particular for statements regarding GluRII subunits in adult muscles. In the current form, some claims appear stronger than supported by the methods.

Thank you for this important suggestion. We replaced “absence” with “not detected” throughout the manuscript. We also note this distinction explicitly in the Discussion.

It would also improve clarity if the different experimental approaches (GAL4, antibody staining, tagging, RNA-seq) were presented more explicitly separated, rather than combined into a single readout. This would allow a better assessment of the evidence.

We have kept the Results organized by finding rather than by technique, because the majority of our results were concordant across approaches and a technique-by-technique presentation would fragment each biological conclusion across four sections. However, we agree that the evidence should be separable by the reader, and it now is: Figure 2C reports GAL4 and IHC in separate columns, Figure s13 presents the RNA-seq results in a parallel table format, and the new Discussion paragraph identifies each case in which the methods disagreed and states which result we consider likely to be a false positive or false negative. Where a single method underlies a conclusion, we now say so in the text.

The discrepancies between methods (e.g., RNA-seq vs GAL4 expression) should be discussed more directly, and the possibility of false negatives, especially for antibody staining in adult tissue, should be acknowledged more clearly.

Thank you. Other reviewers also noticed this weakness of our manuscript, and as noted above, we added a paragraph in the discussion to highlight several important discrepancies in methods and possibilities of false positives.

A functional experiment is not strictly required, but would clearly strengthen the manuscript. For example, electrophysiology at adult NMJs or perturbation of candidate receptors (e.g., GluClα or Clumsy) would help to link expression to function.

We intend to perform functional and behavioral experiments with clumsy loss-of-function flies. However, this work will require creation of new genetic reagents and behavioral experiments that make it beyond the scope of this manuscript. These experiments and the accompanying behavioral analysis will form a separate study, which will be the foundation of a future paper.

Author response:

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

eLife Assessment

This fundamental study is part of an impressive, large-scale effort to assess the reproducibility of published findings in the field of Drosophila immunity. In a companion article, the authors analyze 400 papers published between 1959 and 2011, and assess how many of the claims in these papers have been tested in subsequent publications. In this article, the authors report the results of validation experiments to assess a subset of the claims that, according to the literature, have not been corroborated. While the evidence reported for some of these validation studies is convincing, it remains incomplete for others.

We thank the reviewers for their careful assessment of our manuscript. We are fully aware that this review process required a substantial investment of time and effort, and we are deeply grateful for their engagement. We also thank the eLife editors for enabling an open and constructive evaluation process of the highest standard.

We fully agree with the eLife assessment, including the concluding statement highlighting the limitations of our analysis. We also concur with most of the reviewers’ comments, which we have addressed in detail in the revised manuscript. Addressing these comments required extensive additional work, which explains the duration of the revision. This period was also valuable in allowing colleagues from the Drosophila community to provide feedback on our study, including identifying potential issues—for instance regarding SR-C1—that we have carefully re-examined.

Major revisions include the addition of new experimental data in the sections on Hemese, SR-C1, Sphinx1/2, and Caspar. These results largely confirm our initial conclusions, with the exception of SR-C1. We have therefore revised our interpretation of SR-C1, confirming earlier findings that it promotes bacterial binding, while maintaining that it does not function as a major phagocytic receptor. A table with new list of new reagents has been added at the end of the supplement (Table Supplement S4). We also add a comment on the fact that mutation in the serine protease MP1 (work from B.L.) does not affect wound melanization as initially proposed (Tang et al., 2006).

One final point: our study assesses replicability using alternative experimental approaches, and we cannot exclude the possibility that our conclusions may be inaccurate. This limitation is inherent to all reproducibility studies. Nonetheless, our work should encourage the community to exercise caution when interpreting certain previous claims, some of which have become widely accepted.

We thank the reviewers and editors for their constructive input, which has significantly improved the manuscript. At this stage, we are ready to proceed toward a version of record together with the eLife assessment (which may still evolve). We continue to believe that our reproducibility project is unique in its scope and depth. It not only provides quantitative insight into replicability (See companion article)—suggesting that replication rates may be higher in certain fields, consistent with the maturation of knowledge over recent decades—but also contributes to clarifying and refining a number of statements within the field. Although aware of the cost of assessing reproducibility (hard work for articles that are not quoted and statements that are not taking in account), I consider it as one of my most important and original works.

Public Reviews:

Reviewer #1 (Public review):

Summary:

This work revisits a substantial part of the published literature in the field of Drosophila innate immunity from 1959 to 2011. The strategy has been to restrain the analysis to some 400 articles and then to extract a main claim, two to four major claims and up to four minor claims totaling some 2000 claims overall. The consistency of these claims with the current state-of the-art has been evaluated and reported on a dedicated Web site known as ReproSci and also in the text as well as in the 28 Supplements that report experimental verification, direct or indirect, e.g., using novel null mutants unavailable at the time, of a selected set of claims made in several articles. Of note, this review is mostly limited to the manuscript and its associated supplements and does not integrally cover the ReproSci website.

Strengths:

One major strength of this article is that it tackles the issue of reproducibility/consistency on a large scale. Indeed, while many investigators have some serious doubts about some results found in the literature, few have the courage, or the means and time, to seriously challenge studies, especially if published by leaders in the field. The Discussion adequately states the major limitations of the ReproSci approach, which should be kept in mind by the reader to form their own opinion.

This study also allows investigators not familiar with the field to have a clearer understanding of the questions at stake and to derive a more coherent global picture that allows them to better frame their own scientific questions. Besides a thorough and up-to-date knowledge of the literature used to assess the consistency of the claims with our current knowledge, a merit of this study is the undertaking of independent experiments to address some puzzling findings and the evidence presented is often convincing, albeit one should keep in mind the inherent limitations as several parameters are difficult to control, especially in the field of infections, as underlined by the authors themselves. Importantly, some work of the lead author has also been re-evaluated (Supplements S2-S4). Thus, while utmost caution should be exerted, and often is, in challenging claims, even if the challenge eventually proves to be not grounded, it is valuable to point out potential controversial issues to the scientific community.

While this is not a point of this review, it should be acknowledged that the possibility to post comments on the ReproSci website will allow further readjustments by the community in the appreciation of the literature and also of the ReproSci assessments themselves and of its complementary additional experiments.

We praise the reviewer for this assessment of our project

Weaknesses:

Challenging the results from articles is, by its very nature, a highly sensitive issue, and utmost care should be taken when challenging claims. While the authors generally acknowledge the limitations of their approach in the main text and Supplements, there are a few instances where their challenges remain questionable and should be reassessed. This is certainly the case for Supplement S18, for which the ReproSci authors make a claim for a point that was not made in the publication under scrutiny. The authors of that study (Ramet et al., Immunity, 2001) never claimed that scavenger receptor SR-CI is a phagocytosis receptor, but that it is required for optimal binding of S2 cells to bacteria. Westlake et al. here have tested for a role of this scavenger receptor in phagocytosis, which had not been tested by Ramet et al. Thus, even though the ReproSci study brings additional knowledge to our understanding of the function of SR-CI by directly testing its involvement in phagocytosis by larval hemocytes, it did not address the major point of the Ramet et al. study, SR-CI binding to bacteria, and thus inappropriately concludes in Supplement S18 that "Contrary to (Ramet et al., 2001, Saleh et al., 2006), we find that SR-CI is unlikely to be a major Drosophila phagocytic receptor for bacteria in vivo." It follows that the results of Ramet et al. cannot be challenged by ReproSci as it did not address this program. Of note, Saleh et al. (2006) also mistakenly stated that SR-CI impaired phagocytosis in S2 cells and could be used as a positive control to monitor phagocytosis in S2 cells. Their assay appears to have actually not monitored phagocytosis but the association of FITC-labeled bacteria to S2 cells by FACS, as they did not mention quenching the fluorescence of bacteria associated with the surface with Trypan blue.

We have revised our evaluation of Sr-C1, as we acknowledge that we did not initially read Rämet et al. carefully. We incorrectly assumed that this study demonstrated a role for SR-C1 in phagocytosis, whereas it actually reports a defect in binding only. We have updated our assessment of SR-C1, validating the results from Rämet et al., 2001. We still mention our results on phagocytosis (See below for more information).

The inference method to assess the consistency of results with current knowledge also has limitations that should be better acknowledged. At times, the argument is made that the gene under scrutiny may not be expressed at the right time according to large-scale data or that the gene product was not detected in the hemolymph by a mass-spectrometry approach. While being in theory strong arguments, some genes, for instance, those encoding proteases at the apex of proteolytic activation cascades, need not necessarily be strongly expressed and might be released by a few cells. In addition, we are often lacking relevant information on the expression of genes of interest upon specific immune challenges such as infections with such and such pathogens.

The pattern of expression is always used as an element supporting our assessment but never as the central point of decision (See below for more information).

As regards mass spectrometry, there is always the issue of sensitivity that limits the force of the argument. Our understanding of melanization remains currently limited, and methods are lacking to accurately measure the killing activity associated with the triggering of the proPO activation cascade. In this study, the authors monitor only the blackening reaction of the wound site based on a semi-quantitative measurement. They are not attempting to use other assays, such as monitoring the cleavage of proPOs into active POs or measuring PO enzymatic activity. These techniques are sometimes difficult to implement, and they suffer at times from variability. Thus, caution should be exerted when drawing conclusions from just monitoring the melanization of wounds.

We employed approaches similar to those used in the original studies under evaluation. However, we acknowledge that our analysis primarily relied on cuticular melanization, which is more straightforward to monitor. We have revised the manuscript to clarify this limitation, particularly in the case of PGRP-LE.

Likewise, the study of phagocytosis is limited by several factors. As most studies in the field focus on adults, the potential role of phagocytosis in controlling Gram-negative bacterial infections is often masked by the efficiency of the strong IMD-mediated systemic immune response mediated by AMPs (Hanson et al, eLife, 2019). This problem can be bypassed in rare instances of intestinal infections by Gram-negative bacteria such as Serratia marcescens (Nehme et al., PLoS Pathogens, 2007) or Pseudomonas aeruginosa (Limmer et al. PNAS, 2011), which escape from the digestive tract into the hemocoel without triggering, at least initially, the systemic immune response. It is technically feasible to monitor bacterial uptake in adults by injecting fluorescently labeled bacteria and subsequently quenching the signal from noningested bacteria. Nonetheless, many investigators prefer to resort to ex vivo assays starting from hemocytes collected from third-instar wandering larvae as they are easier to collect and then to analyze, e.g., by FACS. However, it should be pointed out that these hemocytes have been strongly exposed to a peak of ecdysone, which may alter their properties. Like for S2 cells, it is thus not clear whether third-instar larval hemocytes faithfully reproduce the situation in adults. The phagocytic assays are often performed with killed bacteria. Evidence with live microorganisms is better, especially with pathogens. Assays with live bacteria require however, an antibody used in a differential permeabilization protocol. Furthermore, the killing method alters the surface of the microorganisms, a key property for phagocytic uptake. Bacterial surface changes are minimal when microorganisms are killed by X-ray or UV light. These limitations should be kept in mind when proceeding to inference analysis of the consistency of claims. Eater illustrates this point well. Westlake et al. state that:" [...] subsequent studies showed that a null mutation of eater does not impact phagocytosis". The authors refer here to Bretscher et al., Biology Open, 2015, in which binding to heat-killed E. coli was assessed in an ex vivo assay in third instar larvae. In contrast, Chung and Kocks (JBC, 2011) tested whether the recombinant extracellular N-terminal ligand-binding domain was able to bind to bacteria. They found that this domain binds to live Gram-positive bacteria but not to live Gram-negative bacteria. For the latter, killing bacteria with ethanol or heating, but not by formaldehyde treatment, allowed binding. More importantly, Chung and Kocks documented a complex picture in which AMPs may be needed to permeabilize the Gram-negative bacterial cell wall that would then allow access of at least the recombinant secreted Eater extracellular domain to peptidoglycan or peptidoglycan-associated molecules. Thus, the systemic Imd-dependent immune response would be required in vivo to allow Eater-dependent uptake of Gram-negative bacteria by adult hemocytes. In ex vivo assays, any AMPs may be diluted too much to effectively attack the bacterial membrane. A prediction is then that there should be an altered phagocytosis of Gramnegative bacteria in IMD-pathway mutants, e.g., an imd null mutant but not the hypomorphic imd[1] allele. This could easily be tested by ReproSci using the adult phagocytosis assay used by Kocks et al, Cell, 2005. At the very least, the part on the role of Eater in phagocytosis should take the Chung &Kocks study into account, and the conclusions modulated.

We agree that experimental conditions can always influence the outcome and may partly explain discrepancies in reproducibility. However, our approach is based on conceptual replication, with the aim of testing the generalizability of the original findings rather than reproducing them under identical conditions. We often used approaches quite similar to the initial statements.

In the case of Eater, our results challenge the conclusion from Kocks et al. that phagocytosis of Gram-negative bacteria is impaired in the absence of Eater, as this was not confirmed when using null eater mutants. Nevertheless, our data support the idea that Eater contributes to the phagocytosis of Gram-negative bacteria, likely in cooperation with NimC1.

Importantly, our findings are fully consistent with those of Chung and Knocks, who showed that the extracellular domain of Eater binds Gram-positive but not Gram-negative bacteria. Therefore, our work refines a specific aspect of the original conclusion, without questioning the overall significance of the initial Eater studies.

Another point is that some mutant phenotypes may be highly sensitive to the genetic background, for instance, even after isogenization in two different backgrounds. In the framework of a Reproducibility project, there might be no other option for such cases than direct reproduction of the experiment as relying solely on inference may not be reliable enough.

With respect to the experimental part, some minor weaknesses have been noted. The authors rely on survival to infection experiments, but often do not show any control experiments with mock-challenged or noninfected mutant fly lines. In some cases, monitoring the microbial burden would have strengthened the evidence. For long survival experiments, a check on the health status of the lines (viral microbiota, Wolbachia) would have been welcome. Also, the experimental validation of reagents, RNAi lines, or KO lines is not documented in all cases.

We thank the reviewer for their careful and constructive assessment. We agree with most of the points raised and have revised the manuscript accordingly. In particular, we have softened the wording throughout to make our evaluation less abrupt. We have also added a dedicated section on limitations at the end of the manuscript, highlighting potential sources of bias and the inherent constraints of our reproducibility approach.

In addition, we have expanded the description of the tools used and the validation of the RNAi experiments (see below). We consider it unlikely that factors such as Wolbachia or Nora virus significantly affect our conclusions, as our assays rely on short-term survival experiments, whereas these variables are more likely to influence ageing-related phenotypes. That said, we fully acknowledge that unrecognized parameters—such as environmental conditions (e.g., humidity), which we did not systematically control—could contribute to discrepancies. This limitation, however, applies broadly to most attempts at experimental reproduction.

More generally, many of the claims we challenge have not been revisited for over a decade. Our inability to validate some of them suggests that the underlying biology may be more complex than initially proposed. We recognize that some of our conclusions may be incorrect, and it would be surprising if all were entirely accurate. At the same time, reproducibility studies often face an asymmetry in standards of evidence, whereby contradicting a published claim requires a higher burden of proof than establishing it. We believe it is important to document and share such discrepancies. We also explicitly acknowledge in the revised manuscript that the ReproSci framework itself may contain errors. Even if a significant proportion of our assessments are not correct, we believe this work contributes meaningfully to clarifying ongoing debates in the field for most of them.

Finally, since the launch of the website, we have received three comments from the community—one addressing a major claim (Sr-C1) and two addressing more minor points— which have led us to refine our conclusions. The limited feedback we received suggest a broad agreement of the community with our assessment. It illustrates the value of maintaining an open, community-driven resource. The public and evolving nature of the project is, in our view, a key strength.

Reviewer #2 (Public review):

Summary:

The authors present an ambitious and large-scale reproducibility analysis of 400 articles on Drosophila immunity published before 2011. They extract major and minor claims from each article, assess their verifiability through literature comparison and, when possible, through targeted experimental re-testing, and synthesize their findings in an openly accessible online database. The goal is to provide clarity to the community regarding claims that have been contradicted, incompletely supported, or insufficiently followed up in the literature, and to foster broader community participation in evaluating historical findings. The manuscript summarizes the major insights emerging from this systematic effort.

Strengths:

(1) Novelty and community value: This work represents a rare example of a systematic, transparent, and community-facing reproducibility project in a specific research domain. The creation of a dedicated public platform for disseminating and discussing these assessments is particularly innovative.

(2) Breadth and depth: The authors analyze an impressive number of publications spanning multiple decades, and they couple literature-based assessments with new experimental data where follow-up is missing.

(3) Clarity of purpose: The manuscript carefully distinguishes between assessing evidential support for claims and judging the scientific merit of historical work. This helps frame the project as constructive rather than punitive.

(4) Metascientific relevance: The analysis identifies methodological and contextual factors that commonly underlie irreproducible claims, providing a useful guide for future study design and interpretation.

(5) Transparency: Supplementary datasets and the public website provide an exceptional degree of openness, which should facilitate community engagement and further refinement.

We praise the reviewer for this assessment of our project.

Weaknesses:

(1) Subjectivity in selection: Despite the authors' efforts, the choice of which papers and claims to highlight cannot be entirely objective. This is an inherent limitation of any retrospective curation effort, but it remains important to acknowledge explicitly.

We have added a section at the end of the discussion to discuss the limitation of our study.

(2) Emphasis on irreproducible claims: The manuscript focuses primarily on claims that are challenged or found to be weakly supported. While understandable from the perspective of novelty, this emphasis may risk overshadowing the value of claims that are well supported and reproducible.

We have added two sentences at the end of the introduction and at the beginning of the discussion that most claims are reproducible.

(3) Framing and language: Certain passages could benefit from more neutral phrasing and avoidance of binary terms such as "correct" or "incorrect," in keeping with the open-ended and iterative nature of scientific progress.

We have carefully checked the phrasing of our article to be more nuanced and avoid black-and-white assessments.

(4) Community interaction with the dataset: While the website is an excellent resource, the manuscript could further clarify how the community is expected to contribute, challenge, or refine the annotations, especially given the large volume of supplementary data.

This point is already addressed in the revised sentence: “We hope that the community accessible website will encourage researchers to share their perspectives and contribute data from diverse sources, thereby improving objectivity.” In addition, we have proactively engaged with principal investigators to motivate them to contribute to this effort by sharing unpublished results and information. However, it remains unclear to what extent scientists are genuinely interested in reproducibility, as has been noted in other studies on the topic. For example, articles that challenge previous findings are often under-cited, and the presence of contradictory evidence does not necessarily prevent researchers from continuing to cite the original claims. This is clearly a challenge of reproducibility study. Comments, evidence and corrections will not be integrated in the ReproSci website. We have already updated this database when revising this article and will continue to do it.

(5) Minor inconsistency: The manuscript states that papers from 1959-2011 were included, but the Methods section mentions a range beginning in 1940.

This should be aligned for clarity.

We have solved this discrepancy by correcting the method section. This should be 1959-2011. Thank you for spotting this mistake.

Impact and significance:

This contribution is likely to have a meaningful impact on both the Drosophila immunity community and the broader scientific ecosystem. It highlights methodological pitfalls, encourages transparent post-publication evaluation, and offers a reusable framework that other fields could adopt. The work also has pedagogical value for early-career researchers entering the field, who often struggle to navigate contradictory or outdated claims. By centralizing and contextualizing these discussions, the manuscript should help accelerate more robust and reproducible research.

Reviewer #3 (Public review):

Summary:

In this ambitious study, the authors set out to analyse the validity of a number of claims, both minor and major, from 400 published articles within the field of Drosophila immunity that were published before 2011. The authors were able to determine initially if claims were supported by comparing them to other published literature in the field and, if required, by experimentally testing 'unchallenged' claims that had not been followed up in subsequent published literature. Using this approach, the authors identified a number of claims that had contradictory evidence using new methods or taking into account developments within the field post-initial publication. They put their findings on a publicly available website designed to enable the research community to assess published work within the field with greater clarity.

Strengths:

The work presented is rigorous and methodical, the data presentation is high quality, and importantly, the data presented support the conclusions. The discussion is balanced, and the study is written considerately and respectfully, highlighting that the aim of the study is not to assign merit to individual scientists or publications but rather to improve clarity for scientists across the field. The approach carried out by the researchers focuses on testing the validity of the claims made in the original papers rather than testing whether the original experimental methods produced reproducible results. This is an important point since there are many reasons why the original interpretation of data may have understandably led to the claims made. These potential explanations for irreproducible data or conclusions are discussed in detail by the authors for each claim investigated.

The authors have generated an accompanying website, which provides a valuable tool for the Drosophila Immunity research community that can be used to fact-check key claims and encourages community engagement. This will achieve one important goal of this study - to prevent time loss for scientists who base their research on claims that are irreproducible. The authors rightly point out that it is impossible (and indeed undesirable) to avoid publication of irreproducible results within a field since science is 'an exploratory process where progress is made by constant course correction'. This study is, however, an important piece of work that will make that course correction more efficient.

Weaknesses:

I have little to recommend for the improvement of this manuscript. As outlined in my comments above, I am very supportive of this manuscript and think it is a bold and ambitious body of work that is important for the Drosophila immunity field and beyond.

We thank the reviewer for this positive assessment. This was indeed a huge amount of work with the hope this would be useful.

Reviewer #4 (Public review):

This is an important paper that can do much to set an example for thoughtful and rigorous evaluation of a discipline-wide body of literature. The compiled website of publications in Drosophila immunity is by itself a valuable contribution to the field. There is much to praise in this work, especially including the extensive and careful evaluation of the published literature.

However, there are also cautions.

We praise the reviewer for this assessment of our project.

One notable concern is that the validation experiments are generally done at low sample sizes and low replication rates, and often lack statistical analysis. This is slippery ground for declaring a published study to be untrue. Since the conclusions reported here are nearly all negative, it is essential that the experiments be performed with adequate power to detect the originally described effects. At a minimum, they should be performed with the same sample size and replication structure as the originally reported studies.

Many of the original claims we are assessing were obtained with lower sample size than our replicability experiments. Furthermore, we are often complementing our data with alternative approaches that are more robust (survival with additional bacterial strains, AMP kinetics with several time points, etc.). Although we can never claim for a total absence of an effect, our experimental designs are largely sufficient to demonstrate that we cannot report the major effects reported in the initial publications.

The first section of Results should be an overview of the general accuracy of the literature.

Of all claims made in the 400 evaluated papers, what proportion fell into each category of "verified", "unchallenged", "challenged", "mixed", or "partially verified"? This summary overview would provide a valuable assessment of the field as a whole. A detailed dispute of individual highlighted claims could follow the summary overview.

We have described the statistic of our analysis on claim validity in a companion article that will be published back-to-back with this article. We have preferred to divide assessment of claims and statistics on replicability in two articles. The present one is to provide an overview of the main claims that we considered to be fragile. Following the reviewer’s comment, we have added at the start of the manuscript a sentence stating that most of the claims were found to be validated, highlighting the solidity of the field with a link to the other article.

Section headings are phrased as declarative statements, "Gene X is not involved in process Y", which is more definitive phrasing than we typically use in scientific research. It implies proving a negative, which is difficult and rare, and the evidence provided in the present manuscript generally does not reach that threshold. A more common phrasing would be "We find no evidence that gene X contributes to process Y". A good model for this more qualified phrasing is the "We conclude that while Caspar might affect the Imd pathway in certain tissue-specific contexts, it is unlikely to act as a generic negative regulator of the Imd pathway," concluding the section on the role of Caspar. I am sure the authors feel that the softer, more qualified phrasing would undermine their article's goal of cleansing the literature of inaccuracies, but the hard declarative 'never' statements are difficult to justify unless every validation experiment is done with a high degree of rigor under a variety of experimental conditions. This caveat is acknowledged in the 3rd paragraph of the Discussion, but it is not reflected in the writing of the Results. The caveat should also appear in the Introduction.

We fully agree with the reviewer and we have softened the way we discuss all the claims in the result section.

The article is clear that "Claims were assessed as verified, unchallenged, challenged, mixed, or partially verified," but the project is called "reproducibility project" in the 7th line of the abstract, and the website is "ReproSci". The fourth line of the abstract and the introduction call some published research "irreproducible". Most of the present manuscript does not describe reproduction or replication. It describes validation, or independent experimental tests for consistency. Published work is considered validated if subsequent studies using distinct approaches yielded consistent results. For work that the authors consider suspicious, or that has not been subsequently tested, the new experiments provided here do not necessarily recreate the published experiment. Instead, the published result is evaluated with experiments that use different tools or methods, again testing for consistency of results. This is an important form of validation, but it is not reproduction, and it should not be referred to as such. I strongly suggest that variations of the words "reproducible" or "replication" be removed from the manuscript and replaced with "validation". This will be more scientifically accurate and will have the additional benefit of reducing the emotional charge that can be associated with declaring published research to be irreproducible.

We agree on this point. In response to the reviewer’s comment, we have clarified our terminology. Specifically, we now use the term “conceptual replicability” in the abstract and consistently refer to “replicability” and “irreplicability” throughout the manuscript. We hope this revised terminology improves clarity.

The manuscript includes an explanatory passage in the Results section, "Our project focuses on assessing the strength of the claims themselves (inferential/indirect reproducibility) rather than testing whether the original methods produce repeatable results (results/direct reproducibility). Thus, our conclusions do not directly challenge the initial results leading to a claim, but rather the general applicability of the claim itself." Rather than first appearing in Results, this statement should appear prominently in the abstract and introduction because it is a core element of the premise of the study. This can be combined with the content of the present Disclaimer section into a single paragraph in the Introduction instead of appearing in two redundant passages. I would again encourage the authors to substitute the word validation for reproduction, which would eliminate the need for the invented distinction between indirect versus direct reproduction. It is notable that the authors have chosen to title the relevant Methods section "Experimental Validation" and not "Replication".

The disclaimer has been moved at the end of the introduction and one sentence has been added in the abstract.

Experimental data "from various laboratories" in the last paragraph of the Introduction and the first paragraph of the Results are ambiguous. Since these new experiments are part of the central core of the manuscript, the specific laboratories contributing them should be named in the two paragraphs. If experiments are being contributed by all authors on the manuscript, it would suffice to say "the authors' laboratories". The attribution to "various labs" appears to be contradicted by the Discussion paragraph 2, which states "the host laboratory has expertise in" antibacterial and antifungal defense, implying a single lab. The claim of expertise by the lead author's laboratory is unnecessary and can be deleted if the Lemaitre lab is the ultimate source of all validation experiments.

The authors and laboratories that did the experiments are listed in the author list and are easy to identify for experts. At the same time, we did not want to highlight the specific authors to avoid a negative impact on their career. We were very happy that a small number of labs helped in our project. Since all the supplement were reviewed by Hannah Westlake (who has left the lab and the project) and myself (BL), our expertise was important as we did not want to test articles far from what we are doing in the lab. I rephrase the sentence to make it clear.

The passage on the controversial role of Duox in the gut is balanced and scholarly, and stands out for its discussion of multiple alternative lines of evidence in the published literature and supplement. This passage may benefit from research by multiple groups following up on the original claims that are not available for other claims, but the tone of the Duox section can be a model for the other sections.

Comments on other sections and supplements:

I understand the desire to explain how original results may have been obtained when they are not substantiated by subsequent experiments. However, statements such as "The initial results may have been obtained due to residual impurities in preparations of recombinant GNBP1" and "Non-replicable results on the roles of Spirit, Sphinx and Spheroide in Toll pathway activation may be due to off-target effects common to first-generation RNAi tools" are speculation. No experimental data are presented to support these assertions, so these statements and others like them (currently at the end of most "insights" sections) should not appear in Results. I recognize that the authors are trying to soften their criticism of prior studies by providing explanations for how errors may have occurred innocently. If they wish to do so, the speculative hypotheses should appear in the Discussion.

The statement in Results that "The initial claim concerning wntD may be explained by a genetic background effect independent of wntD" similarly appears to be a speculation based on the reading of the main text Results. However, the Discussion clarifies that "Here, we obtained the same results as the authors of the claim when using the same mutant lines, but the result does not stand when using an independent mutant of the same gene, indicating the result was likely due to genetic background." That additional explanation in the Discussion greatly increases reader confidence in the Result and should be explained with reference to S5 in the Results. Such complete explanations should be provided everywhere possible without requiring the reader to check the Supplement in each instance.

In some cases, such as "The results of the initial papers are likely due to the use of ubiquitous overexpression of PGRP-LE, resulting in melanization due to overactivation of the Imd pathway and resulting tissue damage", the claim to explain the original finding would be easy to test. The authors should perform those tests where they can, if they wish to retain the statements in the manuscript. Similarly, the claim "The published data are most consistent with a scenario in which RNAi generated off-target knockdown of a protein related to retinophilin/undertaker, while Undertaker itself is unlikely to have a role in phagocytosis" would be stronger if the authors searched the Drosophila genome for a plausible homolog that might have been impacted by the RNAi construct, and then put forth an argument as to why the off-target gene is more likely to have generated the original phenotype than the nominally targeted gene. There is a brief mention in S19 that junctophilin is the authors' preferred off-target candidate, but no evidence or rationale is presented to support that assertion. If the original RNAi line is still available, it would be easy enough to test whether junctophilin is knocked down as an offtarget, and ideally then to use an independent knockdown of junctophilin to recapitulate the original phenotype. Otherwise, the off-target knockdown hypothesis is idle speculation.

A good model is the passage on extracellular DNA, which states, "experiments performed for ReproSci using the original DNAse IIlo hypomorph show that elevated Diptericin expression in the hypomorph is eliminated by outcrossing of chromosome II, and does not occur in an independent DNAse II null mutant, indicating that this effect is due to genetic background (Supplementary S11)." In this case, the authors have performed a clear experiment that explains the original finding, and inclusion of that explanation is warranted. Similar background replacement experiments in other validations are equally compelling.

We believe that offering possible explanations for discrepancies between results is valuable for readers. For this reason, we have generally retained these elements in the Results section, with the exception of PGRP-SD. In that specific case, we removed the sentence stating that we could not identify the expected mutation in the original PGRP-SD mutants (see below). Although these points could have been moved to the Discussion, doing so would have made it difficult to directly associate each explanation with the corresponding claim. We therefore consider that keeping them in the Results section provides greater clarity. Our hypotheses are grounded in well-established considerations. It is known, for example, that early generations of RNAi constructs often exhibited off-target effects, that commercially available LPS preparations (e.g., from Sigma) were sometimes contaminated, and that genetic background can significantly influence immunological outcomes. It is therefore essential to consider and discuss such confounding factors, particularly those that were not fully appreciated at the time the field emerged.

Identifying motivated collaborators and coordinating experimental validation proved to be extremely time-consuming, making it impractical to systematically provide experimental verification for every discrepancy. As a result, most of our explanations remain speculative, except for the cases of WntD and DNase II, where the observed differences can be attributed to genetic background effects.

The statement "Analysis of several fly stocks expected to carry the PGRP-SDdS3 mutation used in the initial study revealed the presence of a wild-type copy PGRP-SD, suggesting that either the stock used in this study did not carry the expected mutation, or that the mutation was lost by contamination prior to sharing the stock with other labs" provides a documentable explanation of a potential error in the original two manuscripts, but the subsequent "analysis of several fly stocks" needs citations to published literature or explanation in the supplement. It is unclear from this passage how the wildtype allele in the purportedly mutant stocks could have led to the misattribution of function to PGRP-SD, so that should be explained more clearly in the manuscript.

We have removed this statement in the revised version from the result section

The originally claimed anorexia of the Gr28b mutation is explained as having been "likely obtained due to comparison to a wild-type line with unusually high feeding rates". This claim would be stronger if the wildtype line in question were named and data showing a high rate of feeding were presented in the supplement or cited from published literature. Otherwise, this appears to be speculation.

The wild-type fly stocks we used are named in the supplement.

In the section "The Toll immune pathway is not negatively regulated by wntD", FlyAtlas is cited as evidence that wntD is not expressed in adult flies. However, the FlyAtlas data is not adequately sensitive to make this claim conclusively. If the present authors wish to state that wntD is not expressed in adults, they should do a thorough test themselves and report it in the Supplement.

Alternatively, the statement "data from FlyAtlas show that wntD is only expressed at the embryonic stage and not at the adult stage at which the experiments were performed by (Gordon et al., 2005a)" could be rephrased to something like "data from FlyAtlas show strong expression of wntD in the embryo but not the adult" and it should be followed by a direct statement that adult expression was also found to be near-undetectable by qPCR in supplement S5. That data is currently "not shown" in the supplement, but it should be shown because this is a central result that is being used to refute the original claim. This manuscript passage should also describe the expression data described in Gordon et al. (2005), for contrast, which was an experimental demonstration of expression in the embryo and a claim "RT-PCR was used to confirm expression of endogenous wntD RNA in adults (data not shown)."

We agree on this but the expression pattern provided from fly atlas and other genomic resource is an additional element that reinforce our conclusion. For instance, the observation that the expression pattern of WntD is limited to early embryo is consistent with a role in the regulation of Toll pathway in D/V patterning but not immunity. The use of the expression pattern is not the key element of our assessments that rely on the use of loss-of-function mutation. We have rephrased the text in the manuscript according to Reviewer’s suggestion.

Inclusion of the section on croquemort is curious because it seems to be focused exclusively on clearance of apoptotic cells in the embryo, not on anything related to immunity. The subsection is titled "Croquemort is not a phagocytic engulfment receptor for apoptotic cells or bacteria", but the text passage contains no mention of phagocytosis of bacteria, and phagocytosis of bacteria is not tested in the S17 supplement. I would suggest deleting this passage entirely if there is not going to be any discussion of the immune-related phenotypes.

The reviewer is correct and we have in the revised version removed ‘bacteria’ from the title. We have kept the section S17 because this statement ‘Crq recognize and uptake apoptotic cells’ (Science, Immunity)’ is still a source of confusion while the role of crq is more downstream. We agree that efferocytosis might not considered as part of innate immunity but we consider these articles were important in the Drosophila immunity community at that time.

The claim "Toll is not activated by overexpression of GNBP3 or Grass: Experiments performed for ReproSci find that contrary to previous reports, overexpression of GNBP3 (Goear et al., 2006) or Grass (El Chamy et al., 2008) in the absence of immune challenge does not effectively activate Toll signaling (Supplementaries S6, S7)" is overly strongly stated unless the authors can directly repeat the original published studies with identical experimental conditions. In the absence of that, the claim in the present manuscript needs to be softened to "we find no evidence that..." or something similar. The definitive claim "does not" presumes that the current experiments are more accurate or correct than the published ones, but no explanation is provided as to why that should be the case. In the absence of a clear and compelling argument as to why the current experiment is more accurate, it appears that there is one study (the original) that obtained a certain result and a second study (the present one) that did not. This can be reported as an inconsistency, but the second experiment does not prove that the first was an error.

We have softened our statement and revised the supplement document. The title of the section is now ‘Toll is not strongly activated by overexpression of GNBP3 or Grass’. However we want to keep these supplements. The comment of the reviewer applies to all our assessment as we could be wrong. We are using experimental validation and not replication, although in this present case, we are using very similar approach to the described in the original study. Of note, the fact that over-expression of GNBP3 does not consistently activate Drs was already stated in Buchon et al 2019 and we spend quite sometimes in attempts to repeat this experiment. Finally, the Ferrandon team that produce this claim can easily repeat the experiment. This does not affect the main conclusion of their landmark article on GNBP3.

The same comment applies to the refutation of the roles for Edin and IRC. Even though the current experiments are done in the context of a broader validation study, this does not automatically make them more correct. The present work should adhere to the same standards of reporting that we expect in any other piece of science.

We fully agree with the reviewer but the comments he/she raised apply to all the assessments made in our article and nearly all the reproducibility experiments. Our assessment does not state that we are right but that we fail to conceptually reproduce the claim. This is clearly mentioned in our article. We hope to see clarification in the future. It may be one day shown that i) IRC indeed regulates intestinal immunity, ii) PGRP-LE will be shown to have an extracellular form, iii) 18W could indeed be a PRR for LPS (maybe in a specific tissues), iv) PGRPSD will be shown to function upstream of Toll, v) that Crq indeed binds apoptotic cell to internalize them… Our study highlights statements that are source of debate, but this is far from being clear. The authors of these challenged claims have the opportunity to contradict us.

The statement "Furthermore, evidence from multiple papers suggests that this result, and other instances where mutations have been found to specifically eliminate Defensin expression, is likely due to segregating polymorphisms within Defensin that disrupt primer binding in some genetic backgrounds and lead to a false negative result (Supplementary S20)" should include citations to the multiple papers being referenced. This passage would benefit from a brief summary of the logic presented in S20 regarding the various means of quantifying Defensin expression.

We appreciate the value of citing some of the papers underlying this claim. Key papers in question are discussed at length in Supplement S20, and the original papers do not realize the issue we are reporting. We therefore modified the text as follows: "Furthermore, this result, and other instances where mutations have been found to specifically eliminate Defensin expression, is likely due to segregating polymorphisms within Defensin that disrupt primer binding in some genetic backgrounds, leading to false negative results (Brennan 2007,Neyen 2014 and see Supplementary S20)”. The hypothesis we raise, namely that defensin function may involve specific polymorphisms that are absent from the reference Drosophila genome, is an important consideration that should be communicated to the community.

In S22 Results, the statement "For general characterization of the IrcMB11278 mutant, including developmental and motor defects and survival to septic injury, see additional information on the ReproSci website" is not acceptable. All necessary information associated with the paper needs to be included in the Supplement. There cannot be supporting data relegated to an independent website with no guaranteed stability or version control. The same comment applies to "Our results show that eiger flies do not have reduced feeding compared to appropriate controls (See ReproSci website)" in S25.

The ReproSci website contains additional data that we could not display in the supplement but may be useful to scientists. We believe that it is worth to mention them. We have however changed the writing stating ‘Experiments reported in the ReproSci website’ rather than ‘See ReproSci website’ to make it clear that the data are not part of the supplement.

For IRC: We have added a new section that addresses the general characterization of the IrcMB11278 mutant in the revised version (Supplement 22 Figure 2 and 3 with associated text). We do not refer to the ReproSci website anymore.

Supplement S21 appears to show a difference between the wildtype and hemese mutants in parasitoid encapsulation, which would support the original finding. However, the validation experiment is performed at a small sample size and is not replicated, so there can be no statistical analysis. There is no reported quantification of lamellocytes or total hemocytes. The validation experiment does not support the conclusion that the original study should be refuted. The S21 evaluation of hemese must either be performed rigorously or removed from the Supplement and the main text.

To address reviewers’ comment, we generated two new Hemese null mutants, Hemese^JP187 and Hemese^JP828, carrying deletions in the central region of the gene. Using these lines, we show that wild-type and Hemese mutant larvae display comparable levels of lamellocytes and similar numbers of melanized capsules following wasp infestation. We further quantified lamellocyte differentiation and included appropriate statistical analyses. We have removed the previous results obtained with the Hemese^SK2 mutant, which yielded similar observations. By reproducing our previous findings with independent mutant lines and by providing quantitative analyses, we strengthen our conclusion that Hemese does not act as a negative regulator of lamellocyte differentiation upon wasp infestation.

In S22, the second sentence of the passage "Due to the fact that IrcMB11278 flies always survived at least 24h prior to death after becoming stuck to the substrate by their wings, we do not attribute the increased mortality in Ecc15-fed IrcMB11278 flies primarily to pathogen ingestion, but rather to locomotor defects. The difference in survival between sucrose-fed and Ecc15-fed IrcMB11278 flies may be explained by the increased viscosity of the Ecc15-containing substrate compared to the sucrose-containing substrate" is quite strange. The first sentence is plausible and a reasonable interpretation of the observations. But to then conclude that the difference between the bacterial treatment versus the control is more plausibly due to substrate viscosity than direct action of the bacteria on the fly is surprising. If the authors wish to put forward that interpretation, they need to test substrate viscosity and demonstrate that fly mortality correlates with viscosity. Otherwise, they must conclude that the validation experiment is consistent with the original study.

The viscosity of a vial can easily be assessed by direct observation. Here, we provide an information that may guide further research but this is by no way a strong point of our article. Thus, we did not do any change to address this comment. We agree that the function of IRC should be entirely re-visited. We have however changed the name viscosity for stickiness to be more neutral.

In S27, the visualization of eiger expression using a GFP reporter is very non-standard as a quantitative assay. The correct assay is qPCR, as is performed in other validation experiments, and which can easily be done on dissected fat body for a tissue-specific analysis. S27 Figure 1 should be replaced with a proper experiment and quantitative analysis. In S27 Figure 2, the authors should add a panel showing that eiger is successfully knocked down with each driver>construct combination. This is important because the data being reported show no effect of knockdown; it is therefore imperative to show that the knockdown is actually occurring. The same comment applies everywhere there is an RNAi to demonstrate a lack of effect.

Eiger expression: Previous RNA-seq (Flyseq, Troha et al., 2018) or Affymetrix array using poly (A)- RNA (De Gregorio et al., 2001) have never identified eiger as an immune-induced gene. We have used a previously characterized GFP reporter gene using the same approach done by the author to attempt to see an induction in the fat body without success. Our conclusions have been nuanced.

Eiger RNAi KD: The two RNAi lines we are using have already been used in many studies assessing the function of eiger ((#108814, reference here, #45253 reference here)

The Drosomycin expression data in S3 Figure 2A look extremely noisy and are presented without error bars or statistical analysis. The S4 claim that sphinx and spheroid are not regulators of the Toll pathway because quantitative expression levels of these genes do not correlate with Toll target expression levels is an extremely weak inference. The RNAi did not work in S4, so no conclusion should be inferred from those experiments. Although the original claims in dispute may be errors in both cases, the validation data used to refute the original claims must be rigorous and of an acceptable scientific standard.

S3: The inducibility of antimicrobial peptide genes is high, albeit very variable. Importantly, we do not observe any inhibition of Drs expression at the two time points (24 and 48 h) following infection with two distinct bacteria, M. luteus and E. faecalis. Although each experiment was performed once, this corresponds to four independent tests challenging the claim from my lab that “Spheroide is required for activation of the Toll pathway.” Furthermore, if Spheroide played a significant role in Toll pathway activation, increased susceptibility to E. faecalis, B. subtilis, and B. bassiana would be expected. However, both survival data (three independent experiments) and Drs expression profiles (four conditions) consistently indicate that Spheroide is not required for Toll pathway activation. For clarity, we have removed the data related to S. aureus.

S4: To address the reviewer’s comments and reinforce our conclusion, we generated a deletion removing both sphinx 1 and sphinx 2 and analyzed Toll pathway activity in the absence of these two serine proteases. We find that flies lacking sphinx 1 and sphinx 2 exhibit wild-type induction of Drosomycin following M. luteus infection, as well as normal survival upon E. faecalis challenge. These new data provide strong evidence supporting our claim that, in contrast to our previous report (Kambris et al., 2006), Sphinx 1 and Sphinx 2 do not regulate the Toll pathway. Accordingly, we have replaced the earlier RNAi-based results with data obtained from loss-of-function mutants.

In S6 Figure 1, it is inappropriate to plot n=2 data points as a histogram with mean and standard errors. If there are fewer than four independent points, all points should be plotted as a dot plot. This comment applies to many qPCR figures throughout the supplement. In S7 Figure 1, "one representative experiment" out of two performed is shown. This strongly suggests that the two replicates are noisy, and a cynical reader might suspect that the authors are trying to hide the variance. This also applies to S5 Fig 3. Particularly in the context of a validation study, it is imperative to present all data clearly and objectively, especially when these are the specific data that are being used to refute the claim.

S6: The figure 1 of S6 shows all the points. Collectively, this represents 6 replications using 3 drivers of the claim ‘over-expression of GNBP3 efficiently activate the Toll pathway’. The observation, we are now reporting in S6, was already mentioned in Buchon et al 2009 (PNAS). To address reviewer’s concern, we have removed the standard deviation. Finally, our conclusion is rather soft ‘Overexpression of GNBP3 either ubiquitously or in the fat body does not effectively activate the Toll pathway’. At most, we find similar to (El Chamy et al., 2008) that overexpression may produce ‘weak but detectable’ activation of Toll’.

S7: We could not address this point. The point stands, there is no condition where overexpression of native Grass corresponds with higher Drosomycin expression

Other comments:

In S26, the authors suggest that much of the observed melanization arises from excessive tissue damage associated with abdominal injection contrasted to the lesser damage associated with thoracic injection. I believe there may be a methodological difference here. The Methods of S27 are not entirely clear, but it appears that the validation experiment was done with a pinprick, whereas the original Mabary and Schneider study was done with injection via a pulled capillary. My lab group (and I personally) have extensive experience with both techniques. In our hands, pinpricks to the abdomen do indeed cause substantial injury, and the physically less pliable thorax is more robust to pinpricks. However, capillary injections to the abdomen do virtually no tissue damage - very probably less than thoracic injections - and result in substantially higher survivals of infection even than thoracic injections. Thus, the present manuscript may infer substantial tissue damage in the original study because they are employing a different technique.

The reviewer is correct that injection and pinprick injury do not induce the same type of injury and there are differences across labs. We still believe that our approach is valuable. The point is that we confirmed a role of eiger in melanization but not due to its expression in the fat body. It is important to underline that our ReproSci is a conceptual replication project and that we never directly challenge the original observation but rather the robustness of the claim. Injection with a pulled capillary was attempted — in our hands, this caused extensive trauma and killed over 80% of flies it was attempted on. The pinprick on the other hand caused very little trauma. The first sentence of the Results/discussion section states this point.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

It is questionable whether all the studies relevant to the field of assessment have been identified, starting with the own publications from the lead authors. Indeed, Buchon et al, Genes & Development, 2009, Buchon et al., Cell Host&Microbe, 2009, Buchon et al., BMC Biology, 2010 have not been included in the 400 articles, even though one of them is cited when discussing the role of Duox in the intestinal host defense. Other missing articles that fulfill the criteria set by the authors include, but may not be limited to, Chung et al. JBC, 2011, Nehme et al., PLoS One, 2011, Cronin et al., Science, 2009, Limmer et al. 2011.

In our selection, we did not choose articles dealing with intestinal homeostasis and stem cells as well as microbiota/symbionts (Buchon 2009a,b and 2010 Cronin 2009). We also did not analyze articles centered on virulence factor (Limmer 2011). I agree that we missed Chung et al. JBC, 2011 and Nehme et al., PLoS One, 2011 that were published in 2011. Table S1 provide all the information on the article we selected and the ones we removed from the first search.

One area of the field that would have benefited from further insights of ReproSci is that of innate immunity memory or priming (Pham et al., PLoS Pathogens, 2007, has been included in the 400 articles). That being said, the scope of this article is already considerable, and this is just a suggestion for future scrutiny.

The reviewer should recognize that this study (Pham et al.) is inherently complex to reproduce. The field of innate immune priming has also matured considerably since the first publications. Importantly, the set of articles containing “non-validated claims” does not fully overlap with the category of studies that might be considered as weak or problematic.

A major issue in science is the exaggeration of claims, which our approach does not capture. As a result, some articles that are strongly promoted yet make relatively trivial claims— often a source of frustration within the community—may still be classified as valid under our framework. This represents an important limitation of our approach.

For the Supplements, it would be better to show all the data points, especially with respect to RTqPCR data. The nature of the error bars (SD, SE) is never indicated except for one exception (Figure 5, S28). When introducing or using novel lines affecting gene expression, such as RNAi lines or KO mutants, there are often no indications as to how these lines have been validated.

This is especially critical for negative results.

Errors bars: The errors bars were standard deviation. Sorry for this lacks of clarity. This is now indicated in the supplement. Experiments were done in multiple laboratories requiring complex coordination. For this reason, changing all the graphs was too complicated and could not be done for all the figures in the revised version. However data points are shown in many figures of the original draft and all the new figures of the revised version.

For RNAi validation: Concerning the RNAi validation:

(a) Sphinx ½: We have extended our work on Sphinx using a newly generated double

mutant that remove both Sphinx1 and 2. Thus our conclusion does not rely anymore only the use of RNAi.

(b) S12: Hep RNAi : We are using standard Hep-RNAi and BskDN fly tools that have been validated in many studies.

Articles validating the HepRNAi (BDSC35210) can be found on this link. This line has also been validated in Figure 1 of the revised version of Supplement S12.

Articles validating the BskDN (BDSC6409) can be found on this link.

Of note, the Bloomington number of Hep RNAi was miss-annotated and has been corrected in the revised version.

(a) S16. Dscam: The Trip RNAi lines has been used in other articles (ex. Bui et al., “Adjacent neuronal fascicle guides motoneuron dendritic branching 2024 (eNeuro)).

(b) S23. Duox. We are using two RNAi lines including the original RNAi construct used in the article we assessed (Ha et al., 2005).

(c) Eiger: we are using two distinct UAS-RNAi constructs that have been validated (#108814, reference here, #45253 reference here).

Loss-of-function mutations:

For previously described mutants: we used some previously described mutants available in stock centers or from other labs. These include Spheroide^D104, wntD mutants Irc^MB11278, NOS^Δall and Gr28b. See references in the supplement. We have always checked the genotypes of these mutants.

For newly generated mutants

spirit^DR32 see Figure 1 in S2

edin^KO: we have added a new figure describing the mutant in S14 D

ΔSphinx1/2 we have added a figure describing the mutant in S4

DNaseII^sk4: the exact frameshift mutation is indicated in S11

SR-CI^SK6 and Δ(Sr-CI,Sr-CIII): we have added a figure describing the mutant in S18

Hemese^JP187 and HemeseJP⁸²⁸ we have added a figure describing the mutant in S21

Listericin^Δ1 and Listericin^Δ2 mutation are described in Figure 1 in S15

We have now included in the revised supplement a table with all the new tools generated in the framework of the ReproSci project (Supplementary Table 4).

The only uncharacterized mutant is PGRP-LE^Δ53, a gift from François Rouyer (Gif-sur-Yvette). But we also did our experiments with an established mutant: PGRP-LE¹¹².

Is the repeated use of "in vitro" to refer to cell culture studies appropriate? In vitro usually refers to experiments performed in the absence of any living organism or cell, e.g., biochemical reactions in a test tube.

Accordingly, we have replaced in vitro by in cell culture when appropriate

(A) MAIN TEXT

(1) Introduction:

PGRP-LC: Ramet et al, Nature 2002 reference is missing.

"[...]epithelial repair through stem cell proliferation" is a typical disease tolerance mechanism and therefore unlikely to "[...]contribute to DETERRING ingested pathogens". In addition, is "detterring" really the appropriate word?

The changes have been made.

(2) Results:

GNBP1: "and find no evidence" would read better as "and found no evidence". In addition, for GNBP3, the authors may also want to cite Mishima et al. (JBC, 2009) and possibly one on silkworm ßGRP (Takehasi et al., PNAS, 2009).

The changes have been made.

Wnt D: "Dif" and not "dif"=diffuse irregular facets

The changes have been made.

cGLR-STING pathway (Cai et al., 2022): subsequent studies indicated that cGLR ligands are RNA molecules, not DNA. Thus, whether such receptors would be able to detect naked DNA remains a remote possibility.

We agree and have amended the text accordingly

DSCAM1: the statement "not amenable to genetic studies" might be modulated into "not easily amenable to genetic studies" as exemplified by Dong et al. PLoS Biol, 2025 (which the authors may now add to their reference list as this article was published after submission of the current work) and all the literature on DSCAM and the Drosophila nervous system.

We agree and have amended the text accordingly

Psidin: "multiple papers suggest...". References are not given.

We have amended the text and reported to the supplement. Some references have been added.

NOS: "this study reports" should be "this study reported"; otherwise, the reader falsely believes that the authors refer to the Reprosci article. NOS expression: what about data from subsequent RNAseq studies and data from FlyCell Atlas?

We agree with the reviewer and used the past time. For simplicity, we did not discuss Nos expression pattern.

Eiger: the Kodra et al. reference appears to be missing in the reference list.

The Kodra reference has been added.

(3) Discussion:

Third source of irreproducible claims: besides off-target effects, a limitation of the RNAi approach is that one can never be sure that a null phenotype is obtained. Thus, when obtaining negative results, it may be caused by a hypomorphic effect.

This additional point has been added with an example that illustrates the point “Besides off-target effects, a limitation of the RNAi approach is that one can never be sure that it mimics a full null phenotype. As an example, the partial silencing of the serine protease gene Grass may explain why its role in the antifungal response was not detected using in vivo RNAi, but was revealed through the use of a null mutation (El Chamy et al., 2008; Kambris et al., 2006b)”.

(4) Reference list:

Cuttell et al, Gordon et al, 2005, and Melcarne et al, 2019 are duplicated.

Thank you for noticing it. Change has been made.

(5) Supplementary materials:

Table S2 and S3 appear to have been interchanged.

This has been corrected.

Ouyang et al: BioRXiv should be indicated.

This has been corrected.

(B) INDIVIDUAL SUPPLEMENTS:

(1) S1: enzymatic activity of GNBP1.

The number of independent experiments does not appear to be mentioned. With respect to the western blot shown in Figure 2A, it seems that the intensity of the band corresponding to activated ModSP is lower in lane 1 than in other lanes. The suggestion is to scan multiple blots to quantify the activation of this protein in different conditions. Do the authors know the nature of the high mobility band that appears solely when S. aureus peptidoglycan is added?

Regarding the lower intensity of the activated ModSP band in lane 1, a similar phenomenon has been reported in An evolutionarily conserved serine protease network mediates melanization and Toll activation in Drosophila (Fig. S2), where ModSP autoactivation was observed following incubation with PGRP-SA, GNBP1, and peptidoglycans. In current experimental design, the primary objective was to determine whether preincubation of peptidoglycans with GNBP1 further enhances ModSP activation. Therefore, our analysis focused on comparisons across different incubation time points rather than direct comparison with lane 1. Within this context, the lower intensity of the activated ModSP band in lane 1 is expected and does not affect the interpretation of the results

In response to the suggestion of scanning multiple blots for quantification, we note that no clear enhancement of ModSP autoactivation was observed across different incubation times. We also explored alternative incubation conditions, but none resulted in a detectable increase in activation. Thus, additional quantification would not change the overall conclusion.

(2) S2: Spirit

It would have been nice to display the spirit mRNA levels in the KO and KD mutants. Is the catalytic domain removed by the deletion and can the authors exclude a potential expression of a truncated Spirit from a cryptic translation initiation site upon leaky Gal4 expression of the transgene, hence the need for RTqPCR data using primers that map 3' to the transposon insertion?

We are using a deletion that remove all the Spirit isoforms that all start with the same ATG which was removed in the mutant, so it's very unlikely. There is an HSP70T = Terminator after the Gal4, which should exclude an initiation of translation after Gal4. However, we have verified the expected mutation by PCR.

Figure 2: Crystal cells appear to be present in spirit larvae. They, however, appear to be smaller, which may be difficult to measure. Quantification of the number of crystal cells is necessary.

We have removed this part in the revised version (Figure 2C and associated text) because it does not concern the assessed claims in Kambris et al et., 2006 that Spirit regulates the Toll pathway.

Figure 3: It is not clear if pooled data are presented for survival experiments.

Yes survivals show pooled data. We have updated figure legend to make this clearer.

(3) S4: Sphinx 1/2

In the absence of testing null mutant flies, the conclusion may be too strong. Can the authors totally exclude the expression of these proteases in a few cells? If they function as apical proteases, a minimal expression may be sufficient to trigger a proteolytic cascade.

To address the reviewer’s comments, we generated a deletion removing both sphinx 1 and sphinx 2 and analyzed Toll pathway activity in the absence of these two serine proteases. We find that flies lacking sphinx 1 and sphinx 2 exhibit wild-type induction of Drosomycin following M. luteus infection, as well as normal survival upon E. faecalis challenge. These new data provide strong evidence supporting our claim that, in contrast to our previous report (Kambris et al., 2006), Sphinx 1 and Sphinx 2 do not regulate the Toll pathway. Accordingly, we have replaced the earlier RNAi-based results with data obtained from loss-of-function mutants.

(4) S5: wntD

Figure 1, if any, appears to be missing.

Thank you for noticing this. This is now corrected Figure 2=>Figure 1 and Figure 3=> Figure

Fig. 3C-C': please, homogenize the color code with other panels (yw in blue and not suddenly in orange)

We have homogenized the color code in the revised version.

(5) S6-S7: Activation of Toll by overexpression of GNBP3 or protease genes The point is not framed appropriately: the overexpression studies were not intended to determine whether the overexpression of these genes activates the Toll pathway to levels of activation encountered during infection, but as tools for epistatic analysis, and in the case of S8, to identify novel protease genes that might be involved in Toll pathway activation. The results of the epistatic analysis are not disputed and, in some cases, have been validated by independent approaches (e.g., by hemolymph transfer experiments), and the hits of the protease screen have been validated by other laboratories, namely grass and SPE. In Figure S5B of Gottar et al, Cell, 2006, a level of only 30% of immunized was achieved, whereas it was about 70% in Figure 3A. Thus, the level of induction by overexpression of GNBP3 is variable but nevertheless sufficient for epistatic analysis both for Gottar et al. and for El Chamy et al., Nat. Immunol, 2008. Furthermore, levels of activation sufficient for epistatic analysis of Toll pathway activation or stimulation of the melanization proteolytic activation cascade upon the overexpression of either GNBP3 or GNBP1 together with PGRP-SA have been reached (Gobert et al., 2003; Gottar et al. 2006; El Chamy et al, 2008; Matskevich et al., Eur. J. Immunol., 2010). Thus, the overexpression of GNBP3 functions for genetic analysis purposes in two independent teams, that however, are working in the same research Unit. While one cannot exclude that enough peptidoglycan metabolites, e.g., TCT, are provided by the microbiota, it cannot be excluded that ß-(1-3)glucans might originate from the food or mycobiota, which may be distinct from that in the Reprosci laboratory. This illustrates the difficulty of controlling all parameters.

We fully agree that the notion that GNBP3 functions upstream of serine protease is validated. The point is that we cannot reproduce the observation that overexpression of GNBP3 trigger a strong Toll activation sufficient for epistatic analysis as shown in Gottar et al., 2006. The point is that ReproSci does not challenged any of the major claims of Gottar et al. 2006 but only a minor claim. The magnitude of gene induction relative to the unchallenged condition is an important consideration in the field of Drosophila immunity and can be misleading. For example, a gene described as being induced fivefold may appear significant, whereas the same gene can be induced up to 1,000-fold following infection. Therefore, absolute expression level compared to challenged level, rather than fold changes alone, should be carefully considered when interpreting immune gene activation.

We have done our studies with two different constructs. The observation that overexpression of a gene activate an immune pathway is by itself a result suggesting a concentration-dependent mode of activation. For instance, overexpression of ModSP is sufficient to activate the Toll pathway (Buchon 2009). This was not the case for GNBP3, even at low level. We cannot exclude that this could be the case in a specific background but at least not all background. Over-expression of GNBP3 is used in 3 panels of Gottar 2006 and this was a significant piece of data. On my side, my lab has lost significant amount of time to reproduce this without success.

Now we could be wrong in our assessment but we let the author of this study to show it.

To take in consideration Reviewer’s comment, we are softened our conclusions : ‘Overexpression of GNBP3 either ubiquitously or in the fat body does not effectively activate the Toll pathway’. At most, we find similar to (El Chamy et al., 2008) that overexpression may produce ‘weak but detectable’ activation of Toll’.

References:

Alphabetical order is not respected (Matskevich before Kim), and the Mishima reference is not optimal: it should be the JBC article in the same year that documents also the biochemistry of binding to ß-glucans.

We have done the changes in the revised version

(6) S8: PGRP-LE not in hemolymph

Fink et al., Mucosal Immunol. 2016 used the NP1-Gal4, which is not expressed in enteroendocrine cells, as stated in the text, but in enterocytes (and possibly the nervous system).

For controls, is the wild-type control the w[iso] Drosdel background?

Please provide the supplier of the GFP antibody.

We have addressed all the points in the revised version.

(7) S9: PGRP-LE and melanization

Figure 1D-E: A quantification would bolster the claim.

We agree that quantification of Figure 1D-E would reinforce the claims but we believe that our data are sufficient to state that PGRP-LE does not block the cuticular melanization upon septic injury (which is also consistent with an intracellular role). We have softened our conclusion.

(8) S10: PGRP-LE and bacillus

Please provide a description of the Bacillus subtilis strain.

This is a strain that derived from the Jean Lambert collection of Strasbourg and used in Lemaitre B PNAS 1997 (J.Millet and A. Klier, Pasteur Institute of Paris). We have checked the strain and confirm that it was indeed a B. subtilis strain that we name B subtillis FS.

It is not clear from the Mat & Meth whether the 2-3 independent replicates per genotype represent biological replicates in one experiment or correspond to several independent experiments. Are the pooled data displayed?

This information was on the methods. It has been copied to the figure caption.

(9) S11: DNAse II and regulation of AMP genes

The exact larval stage is not provided in S11, nor in the original study.

The experiment was done on wandering third-instar larvae as indicated in the material and methods

The number of flies for survival experiments is rather low, but this is not a major issue given the outcome of the experiment.

We agree with the reviewer.

What is the concentration of the injected DNA? As the solution was likely viscous, was the DNA sheared?

We have used a concentration of DNA of: 200 ng/ul, which is now indicated in the revised version of the Supplement. DNA was no sheared.

Figure 1A&D: A positive control of immunization would have been nice. 1D: At which time point was Diptericin expression measured by RTqPCR?

Unchallenged flies were used in Figure 1A while in Figure 1D Diptericin was measured 6 h after challenged. We agree that a bacterial challenge control would have been nice, but clearly the level of Diptericin in 1A corresponds to levels observed in unchallenged flies. Of note, we have tried several different concentrations, of more or less long "sizes" of DNA (short or very long fragments), and also different DNA sources (E. coli or Drosophila) but we did not see any effect on the activation of the Imd pathway.

DNAseII-deficient larvae have wild-type hemocyte numbers. His sub-title is not accurate as Figure 3 actually reports an INCREASED number of hemocytes in the DNase II mutant.

The reviewer is correct and we have adjusted the text.

(10) S12: JNK pathway and AMP gene expression

Hep RNAi lines and possibly also the Bsk-DN line should be validated by monitoring puckered mRNA levels after a stress that activates the JNK pathway. The absence of this control weakens the Reprosci conclusions.

As stated above, we are using standard Hep-RNAi and BskDN fly tools that have been validated in many studies.

Articles validating the HepRNAi (BDSC35210) can be found on this link. We have also validated the RNAi in new Figure 1 of Supplement S12.

Articles validating the BskDN (BDSC6409) can be found on this link

The Bloomington number of Hep RNAi was miss-annotated and has been corrected in the revised version

(11) S13: Caspar

There is clearly a trend for improved survival of the Caspar mutant in Figure 1A. Please, show the pooled data and appropriate statistical analysis. The legend to 1A mentions one overexpression strain that is not displayed and has likely not been performed because loft experiments were performed at 25{degree sign}C, whereas OE experiments should be performed at 29{degree sign}C, hence in separate experiments.

There was a mistake in the original figure legend when we mentioned the impact of overexpression of caspar on survival without showing the data (no effect was observed). The text has been removed in the revised version because it is not related to the claims we assessed from the Caspar article (Kim et al.,2006). To addressed reviewer’s comments, we now present the pooled data in Figure 1 of the revised Supplement S13. The conclusion is that we do not observe any increase host survival in caspar mutant related to wild-type consistent with our observation that the Imd pathway is not strikingly over-activated in absence of infection in caspar loss-of-function mutants.

Why was the c729-Gal4 driver chosen? Has it been validated as a bona fide fat body driver?

The use of c729-Gal4 was suggested by, and borrowed from, the laboratory of Prof. Gaiti Hasan, who had characterized and used it in adult fat body experiments (Subramanian M et al., 2013, Dis. Mod. & Mech). The BDSC number for the corresponding stock is BDSC_6983. Based on Flybase data, it is also expressed in somatic cells of male/female reproductive systems in the adult.

The RTqPCR experiments are not overwhelmingly convincing for a lack of data points: pooled data should be shown, inasmuch as there is a significant difference upon Caspar OE 6h after Ecc15 challenge.

We now show in the revised version of the Supplement S13 the pooled data from different experiments with individual points shown.

In conclusion and although our results are variable, they do not reproduce the results produced in the original article by (Kim et al., 2006) According to our results, we observe:

(1) no increase Dpt expression in absence of challenge both in caspar deficient larvae and adults.

(2) A possible inhibition of Dpt upon over-expression caspar at 6h in adult.

- A possible increased Dpt expression in caspar loss of function mutant larvae upon challenge.

The later may suggest an inhibition role upon overexpression of caspar that required further analysis. The text of the supplement has been amended to take all those points in consideration.

(12) S15: listericin

Introduction: The LLO (also referred to as hly) L. monocytogenes mutant does not prevent the entry of Listeria inside cells. The pore-forming toxin listeriolysin is required for pathogen escape from the phagosome.

There is no reference to LLO in the introduction of the S15 listericin section.

Has the STAT-92E RNAi line been validated? It is difficult to draw a definitive conclusion on the absence of the role of the JAK-STAT pathway in adults using an RNAi transgene because it may only imperfectly silence the expression of the target gene. "Contrary to Goto et al.2010, in our hands reduction of JAK-STAT activity through RNAi [...] in adult flies": Goto et al. apparently tested the JAK-STAT pathway only in S2 cells. This statement should therefore be modulated accordingly.

We have validated the STAT92 RNA in the revised version by confirming that Turandot gene expression is reduced in this mutant (Supplement 15 Figure 2 C-D). We have also validated the PGRP-LE¹¹² null mutant (Supplement 15 Figure 1C).

We have adjusted the conclusion: “Contrary to (Goto et al., 2010), we find that Listericin expression is not specifically dependent on PGRP-LE, and is not dependent on JAK-STAT signaling in flies. Of note, this could be the case in S2 cells where the initial experiments were done.

Antibacterial effects of listericin: It would be cautious not to rely solely on survival experiments, but also to monitor the bacterial titer to draw a definitive conclusion (assay used by Goto et al.). A control overexpressing GFP or a non-relevant peptide would have been welcome to control for potential metabolic effects that would decrease the effect of the overexpression. More importantly, Goto et al. used a Cg-Gal4 driver that is also expressed in hemocytes, which is likely not the case for the Lpp driver. Is it known if the c564 driver is also expressed in hemocytes and to the same level as the Cg-Gal4 driver?

We have used two fat body drivers to overexpress Listerin, Lpp and C564, the latter being expressed in hemocytes indeed. We agree that bacterial counting would provide a sensitive assay but in absence of any protective effect of Listericin overexpression, we do not expect any major titer change in L. monocytogenes growth. To reinforce our conclusion, we have generated Listericin null mutations (Fig 4C) and we have shown that they are not more susceptible than the wild-type to L. monocytogenes.

(13) S16: DSCAM1

The authors use an RNAi construct to knock down DSCAM1 expression. Which part of the transcripts is targeted? Did the authors verify that silencing was effective and would affect all DSCAM transcripts?

The DScam RNAI (BDSC #38945) that we are using has been used in other articles (link) and is validated in Kamiyama et al., Dev cell (Figure S4).

Data points should be shown in the figure.

Unfortunately, we could not address this point to the difficulty to reach the collaborator who provided the data.

Their conclusions would be strengthened by directly testing opsonization using the assay developed by Haller et al., EMBO Reports, 2018. Also, to derive the phagocytic index, the authors must have counted the number of hemocytes retrieved from bled larvae? Was there a decrease when DSCAM1 was silenced in hemocytes? The use of a hml-Gal4-Gal80ts driver would have allowed to bypass the issue of developmental effects.

We expect an opsonin to be abundant in the hemolymph but we did not find any secreted form of dScam in our proteomics analyses (Rommelaere 2024). 20 years after the publication of this landmark article in Science, the absence of any confirmation is puzzling and we are reluctant to do any additional experiment taking into consideration that phagocytosis assays are often variable.

(14) S18: SR-CI

The major issue with this supplement has been dealt with in the Public Review: no phagocytic receptor function was claimed in the Ramet et al, 2001 study.

We fully agree with the reviewer and with Mika Rämet and Monty Krieger (personal communication), and we apologize for this misunderstanding. In fact, Rämet et al. (2001) did not present data demonstrating a role for Sr-CI in phagocytosis per se in his article, but rather showed that this receptor is involved in bacterial binding. Our confusion arose from a subtitle in the Results section of their article (“SR-CI Binds Both Gram-Positive and Gram-Negative Bacteria and Is Necessary for Optimal Phagocytosis by S2 Cells”) and the article title that claim that Sr-CI is a pattern recognition receptor, which does not reflect the content of the article.

To clarify this point, we have revisited the original claim. Consistent with Rämet et al. (2001), we now observe a defect in hemocyte binding to bacteria in Sr-CI mutants. Thus, we validate the claim. Because Sr-CI is often assumed to function as a phagocytic receptor, we have also retained the experiments showing that it is not essential for the phagocytosis of E. coli or S. aureus. All experiments have been repeated during the revision process using a null single mutation and a double mutant removing both Sr-CI and Sr-CIII.

Introduction: Is it really adequate to mention a phagocytic receptor for a ligand, dsRNA, that gets endocytosed?

In the introduction, we summarized what is known on the Sr-CI, including its implication in the uptake of dsRNA. As suggested by the reviewer, we used the term endocytosis to refer to the ability to uptake dsRNA.

Methods: Have the authors excluded the potential off-target effect of CRISPR-Cas9 in other scavenger receptor genes? Monitoring their expression levels would also allow the detection of any compensatory effect in the null mutant by overexpression of other scavenger receptors.

We are now using two mutant lines: one carrying a frameshift mutation (SK6) that specifically affects Sr-CI, and another with a deletion removing both Sr-CI and Sr-CIII. We have carefully validated both mutations by genomic sequencing. As our results are now consistent with the original findings of Rämet et al. (2001), we believe that the analyses presented in the Supplementary Information are genetically well supported.

Results: Figure 1 is really confusing with so much variability in the data, which raises doubts about the reliability of the method. The reduction of the phagocytic index in B is not "mild". Again, one would like to see the individual data points and to know what the error bars are. For 1G, has any statistical analysis been performed? Finally, Panels A to G lack homogeneity in their presentation. Also, why are the absolute values of the y-axis varying so much from panel to panel (A-B vs C-D; E vs. F)?

We have repeated our experiments using a new set of mutants, both generated in the isogenic DrosDel background. In the revised version, we include additional experiments assessing the contribution of Sr-CI to hemocyte binding to bacteria. Consistent with the original report by Rämet et al. (2001), we observe similar results. We have revised the text accordingly and moderated our claims. In addition, we performed further biological replicates and now provide appropriate statistical analyses.

(15) S19: Undertaker

Undertaker has been identified through a deficiency screen that restricted the genomic zone of interest to eight genes. RNAi was then used to identify the candidate gene as being Undertaker. While an off-target effect of RNAi cannot be excluded, it cannot account for the results of the deficiency screen (junctophilin is on the second chromosome, whereas undertaker is on the third). The deficiency phenotype could be rescued by an Undertaker transgene. While overexpression can indeed provide a rescuing activity due to high levels of ectopic expression, why would it do so in the context of an 82F deficiency, unless this deficiency carries a second site mutation, which is a rather remote possibility.

Given that the deficiency line deletes at least 14 genes in a cluster, several of which are involved in growth and development, we assume that another gene(s) within the span of this deficiency is responsible for the effect on efferocytosis, or that some other mutation in the uncontrolled genetic background is responsible. The impact of Df(3R)3-4 on efferocytosis remains to be investigated.

The authors claim that Undertaker is not expressed at the right embryonic stage and hardly in S2 cells, which is correct according to large-scale data. However, Cuttell et al. successfully stained S2 cells with an antibody raised against retinophilin/undertaker by the investigators who studied the role of this gene in the eye (Mecklenburg et al., 2007). Should we trust more largescale datasets based on transcriptomics or a specially developed tool? (Both junctophilin and undertaker are at the limit of detection of the proteomic data available on FlyBase; equivalent signals in hemocytes were measured in FlyCellAtlas). Thus, the argument of the absence of expression is not definitive.

We agree on this but the expression pattern is an additional element that reinforce our conclusion. This is not the key element that relies on the use of loss-of-function mutation. Another element is the absence of follow-up study in the last 18 years.

The new phagocytosis data set generated by Reprosci shows an absence of impact of the undertaker loft mutation in larval hemocytes. Whether these data can be extrapolated to S2 cells, embryonic or adult hemocytes, remains debatable, as are the explanations put forth by Reprosci in their conclusion to explain by a possible off-target effect of RNAi on junctophilin. It would be interesting to determine the phenotype of junctophilin mutants in the ex vivo larval hemocyte assay.

We have analyzed the role of Undertaker using third instar larvae in an ex vivo assay and did not find any role in efferocytosis. I think that all our data and analysis of the literature is consistent with our statement that’ that undertaker is unlikely to have a role in phagocytosis’. Now, we can never exclude that Undertake may play a subtle role in this process. The role of Draper has been observed in larval hemocyte that represent macrophage of flies. We are using a null mutation in undertaker preventing the existence of off-targets. We have nuanced our conclusion in the article and add a sentence in the conclusion of the supplement: ‘We cannot however exclude that Undertaker play a role at a specific stage of development that we did not assess.’

(16) S20: Psidin

This supplement is duplicated

The duplicated supplement has been removed.

Phagocytosis assay: the authors use E. coli-GFP. How can they discriminate between internalization and simple binding at the surface of hemocytes? It would have been more appropriate to use a phalloidin, stained to another color rather than green. The suggestion here is to first use FITC-labeled bacteria, followed by Trypan blue treatment to quench the fluorescence of noninternalized bacteria. Second, pHrodo bacteria could be used to monitor the acidification of the phagosome in wt and psidin hemocytes.

We agree with the reviewer that this would be better. Because our observations are consistent with the data reported in this original article, we did not feel inclined to extend our analysis.

(17) S21: Hemese

The pie charts in Figure 1 would benefit from a statistical analysis. Why do the encapsulated eggs appear to be much larger in the hemese mutant? Could it be that more lamellocytes are recruited and make a thicker capsule? Should Figure 1C be imperatively quantified?

To extent our analysis, we generated two new Hemese null mutants, Hemese^JP187 and Hemese^JP828, carrying deletions in the central region of the gene. Using these lines, we show that wild-type and ^Hemese mutant larvae display comparable levels of lamellocytes and similar numbers of melanized capsules following wasp infestation. We further quantified lamellocyte differentiation and included appropriate statistical analyses. We have removed the previous results obtained with the Hemese^SK2 mutant, which yielded similar observations. By reproducing our previous findings with independent mutant lines and by providing quantitative analyses, we strengthen our conclusion that Hemese does not act as a negative regulator of lamellocyte differentiation upon wasp infestation.

(18) S22 IRC

IRC is actually not a catalase but a heme peroxidase. For the experiments on C. albicans, can the authors exclude that the IRC flies succumb because they are more sensitive to ethanol than wt or spz flies (sucrose is fermented by C. albicans): a control would be to use glycerol (nonfermentable) instead of sucrose solution.

We thank the reviewer and Carolina Barillas (personal communication) to inform us that IRC is not a catalase but an heme peroxidase. This is now included in the article and the supplement. It is clear that the name IRC for immune regulated catalase is misleading. We cannot exclude that the IRC flies succumb because they are more sensitive to ethanol than wt or spz flies but we did not test this interesting idea during the revision.

Do IRC mutants succumb to the ingestion of killed bacteria?

No, they get stuck in fly food and die.

(19) S23 DUOX

Introduction: When citing Kumar et al., the authors might also want to cite Bai et al. on the Bactrocera dorsalis peritrophic matrix.

This reference has been added

Results:

Figure 1: any statistical analysis? Data points are not shown for the lef panel, and error bars are not defined.

We have added in the revised version ‘When using the Mann-Whitney U test, we still observed a statistically significant difference in CFU counts at 6 hpi in Figure 2B, as well as at both 6 hpi and 24 hpi in Figure 2F. However, the magnitude of these differences is relatively small’. Error bars have been defined in the general revision of the supplements (see above).

Figure 2A shows only a limited reduction in Duox expression at the transcriptional level. "successfully" might be a bit of an overstatement.

We have removed the term ‘successfully’.

Figure 2E is too small.

We have increased the size of Figure 2E.

The authors might want to discuss the role of Duox in enterocytes destined to die as described by Amchelavsky et al., Cell Reports, 2020.

Good point, we have discussed this reference in the revised version.

The Sajjadian reference is incomplete.

The reference has been completed

(20) S24: NOS

Maybe the work from the Royet laboratory could be cited along with that of Neyen et al. and Zaidmann-Remy et al. in the Introduction.

Good points. We have added two references related to the work of the Royet lab (Bosco-Drayon et al., 2012; Charroux et al., 2017).

It is not clear from Rabinovich et al. (2016) which line should be the relevant wild-type control. Why use w[1118] in Figure 1 and Ore-R in Figure 2? A more definitive conclusion could be reached upon isogenization or testing a second null mutant in homozygous and transheterozygous conditions?

We agree that ideally, we should have used isogenic wild-type control but in absence of any effect of NOS mutants, we consider that the use of w[1118] and Oregon wild-type control is acceptable, considering that they behave similarly in the assay we have used.

(21) S25 eiger survival

Survival experiments: Are pooled data shown? Have the authors monitored the health status of their fly lines? In some of the survivals with late phenotypes, e.g., egr mutants and E. faecalis, this may be an issue, inasmuch as noninfected or mock-infected controls are not shown (have they been performed?).

The survival analysis showed the pooled of 40 flies and were often done with two sexes. They also include many controls. We cannot never exclude minor effects at late time points, but the critical message is that we cannot reproduced the previously published results.

The survival graphs are difficult to analyze: the authors should definitely avoid light colors such as yellow that do not show up well in a white background.

As stated above, these experiments were done by many scientists in different lab and it was difficult to homogenize the data. Therefore, we did not modify our graphs although we agree with the reviewers. We believe that line patterns and contrast differences between groups guarantee that the readers can still assess the data.

(22) S27: eiger humoral response

Introduction: Have the authors also checked the Flysickseq data from the Buchon lab?

There is no induction of eiger in Flysick. This information along with the reference Troha et al., have been added to S27.

Methods: Have the RNAi lines been validated, and how? Is one more efficient at silencing than the other? This set of data would complement Figure 1 with RTqPCR experiments.

The two RNAi lines we are using have already been used in many studies assessing the function of eiger ((#108814, reference here, #45253 reference here)

Figure 3 colors in survival graphs: see S25.

We did not modify our graphs although we agree with the reviewers. By increasing the magnification, the readers can still assess the data. As stated above, these experiments were done by many scientists in different labs and it was difficult to homogenize the data.

Would it have been worth to also test the transheterozygous Gr28b mutants to avoid any issue of second-site mutations?

We could have extended the genetics approach but, given that both us and another group (Sang) found no effect on feeding in an independent mutant, and extremely high feeding in the claimed 'anorexic' mutant, this would not be relevant to the claim. Future study may tell us if Gr28b has clearly a feeding phenotype.

Reviewer #2 (Recommendations for the authors):

(1) Adjust the discussion to better contextualize subjectivity: Because the choice of claims and papers inevitably involves subjective decisions, consider expanding the discussion to acknowledge this limitation more explicitly and explain how the companion metascience manuscript complements this work.

We have added a section at the end of the discussion to discuss the limitation of our study and we establish more link to the companion article.

(2) Refine language and avoid binary judgments: Terms such as "correct," "incorrect," or similar definitive formulations should be softened. Emphasizing uncertainty and openness to future revision will better reflect the iterative nature of scientific inquiry.

We are softening our language in several of our assessment to avoid binary judgement.

(3) Highlight reproducible findings as well: While the focus on irreproducible or challenged claims is understandable, it may be helpful to balance this by more clearly acknowledging wellsupported claims or areas of strong reproducibility to reinforce the positive impact of robust findings.

We have added two sentences at the end of the introduction and at the beginning of the discussion that most claims are reproducible and that we have focused here on nonreproducible claim.

(4) Clarify how the community can engage with the dataset: Because you provide extensive supplementary material and a large online resource, consider adding more explicit guidance on how researchers can contribute comments, evidence, or corrections, and how these contributions will be integrated.

This point is already addressed in the revised sentence: “We hope that the community-accessible website will encourage researchers to share their perspectives and contribute data from diverse sources, thereby improving objectivity.” In addition, we have proactively engaged with principal investigators to motivate them to contribute to this effort by sharing unpublished results and information. However, it remains unclear to what extent scientists are genuinely interested in reproducibility, as has been noted in other studies on the topic. For example, articles that challenge previous findings are often under-cited, and the presence of contradictory evidence does not necessarily prevent researchers from continuing to cite the original claims. This is clearly a challenge of reproducibility study. Comments, evidence and corrections will be integrated in the ReproSci website. We have already updated this database when revising this article and will continue to do it.

(5) Resolve the date-range inconsistency: The Introduction mentions analysis of papers from 1959-2011, whereas the Methods section cites 1940-2011. This discrepancy should be corrected for consistency.

We have solved this discrepancy by correcting the method section. This should be 1959-2011. Thank you for spotting this mistake.

Reviewer #4 (Recommendations for the authors):

(1) The "disclaimer" subsection should be incorporated into the Introduction, as it is central to the premise of the study.

The disclaimer has been moved at the end of the introduction and one sentence has been added in the abstract.

(2) The inconsistency of graphical representation and statistical analysis of survival and gene expression data across different supplements is distracting and makes the project feel cobbled together. A consistent and unified framework for analysis and presentation would feel more cohesive and rigorous.

The experiments were conducted across multiple laboratories and required substantial coordination. As a result, modifying the graphs at this stage would be technically complex and would require monumental effort for a tiny return. Therefore, we regret that we were unable to implement this change. The most important is that data and analyses are presented transparently, allowing readers to evaluate and interpret the results independently.

(3) The purported roles of eiger and Gr28b in immunity have nothing to do with each other, aside from both having been published by David Schneider's group. I would suggest not combining them into a single section unless there is to be a 'miscellaneous' section that contains work by multiple groups.

We have done two separate sections.

(4) It would be easier to comment on specific passages in the manuscript if line numbers had been included.

Sorry for this. We have included number of lines in the revised version.

(5) The use of the word "elegant" to describe melanization reactions on page 3 is a bit odd and feels out of place.

It has been removed

(6) The sentence "We conclude that PGRP-LE is an exclusively intracellular sensor, with a prominent role regulating the gut immune response (Bosco-Drayon et al., 2012; Neyen et al., 2012)" should be edited to read "as reported in (citations)".

We have edited the sentence.

(7) The sentence "Experiments performed for ReproSci and review of the literature suggest that JNK is unlikely to have a strong direct or systematic role in the regulation of Drosophila AMPs in vivo, and is not required in the adult fat body for AMP expression in response to infection (Supplementary S12)" lacks detail. I realize that the experiments are described in S12, but I would suggest a brief summary in the main text of the article as well.

We have provided more information in the article.

(8) The phrasing of "While many of the challenged claims discussed in this paper are known to be controversial by experts, or have fallen quietly out of current research interests, some are still a source of confusion. This is particularly true for young scientists new to the field of Drosophila immunity or scientists with primary interests outside of Drosophila immunity that use the field as a reference." could be edited for clarity. A more direct phrasing could help, such as "Even in the absence of published refutation, many of the challenged claims were already considered controversial by experts in the field. Others have quietly fallen out of the general current research interest. These may nevertheless still be a source of confusion for young scientists new to the field of Drosophila immunity or scientists with primary interests outside of Drosophila immunity that use the field as a reference."

We have changed the sentence accordingly.

(9) On Discussion page 15, the comma should be removed from "In this article we have not discussed a number of claims, that had no clear follow-up studies and remain unchallenged."

The coma has been removed.

(10) In Methods, the authors "acknowledge that our verification experiments could also be erroneous". It would be appropriate to also include such a disclaimer in the Introduction and/or Discussion.

The disclaimer has been moved at the end of the introduction and one sentence has been added in the abstract.

Author response:

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

eLife Assessment:

This important study presents an impressive large-scale effort to assess the reproducibility of published findings in the field of Drosophila immunity. The authors analyse 400 papers published between 1959 and 2011, and assess how many of the claims in these papers have been tested in subsequent publications. In a companion article they report the results of experiments to test a subset of the claims that, according to the literature, have not been tested. The present article also explores if various factors related to authors, institutions and journals influence reproducibility in this field. The evidence supporting the claims is solid, but there is considerable scope for strengthening and extending the analysis. The limitations inherent to evaluating reproducibility based on the published literature should also be acknowledged.

We have included in the abstract the limitation of evaluating replicability based on the published literature

Public Reviews:

Reviewer #1 (Public review):

Summary:

The authors set out on the ambitious task of establishing the reproducibility of claims from the Drosophila immunity literature. Starting out from a corpus of 400 articles from 1959 and 2011, the authors sought to determine whether their claims were confirmed or contradicted by previous or subsequent publications. Additionally, they actively sought to replicate a subset of the claims for which no previous replications were available (although this set was not representative of the whole sample, as the authors focused on suspicious and/or easily testable claims). The focus of the article is on inferential reproducibility; thus, methods don't necessarily map exactly to the original ones.

The authors present a large-scale analysis of the individual replication findings, which are presented in a companion article (Westlake et al., 2025. DOI 10.1101/2025.07.07.663442). In their retrospective analysis of reproducibility, the authors find that 61% of the original claims were verified by the literature, 7.5% were partialy verified, and only 6.8% were challenged, with 23.8% having no replication available. This is in stark contrast with the result of their prospective replications, in which only 16% of claims were successfully reproduced. The authors proceed to investigate correlates of replicability, with the most consistent finding being that findings stemming from higher-ranked universities (and possibly from very high impact journals) were more likely to be challenged.

Strengths:

(1) The work presents a large-scale, in-depth analysis of a particular field of science that includes authors with deep domain expertise of the field. This is a rare endeavour to establish the reproducibility of a particular subfield of science, and I'd argue that we need many more of these in different areas.

(2) The project was built on a collaborative basis (https://ReproSci.epfl.ch/), using an online database (https://ReproSci.epfl.ch/), which was used to organize the annotations and comments of the community about the claims. The website remains online and can be a valuable resource to the Drosophila immunity community.

(3) Data and code are shared in the authors' GitHub repository, with a Jupyter notebook available to reproduce the results.

We thank the reviewer for their positive comments.

Main concerns:

(1) Although the authors claim that "Drosophila immunity claims are mostly replicable", this conclusion is strictly based on the retrospective analysis - in which around 84% of the claims for which a published verification attempt was found. This is in very stark contrast with the findings that the authors replicate prospectively, of which only 16% are verified. Although this large discrepancy may be explained by the fact that the authors focused on unchallenged and suspicious claims (which seems to be their preferred explanation), an alternative hypothesis is that there is a large amount of confirmation bias in the Drosophila immunity literature, either because attempts to replicate previous findings tend to reach similar results due to researcher bias, or because results that validate previous findings are more likely to be published.

Both explanations are plausible (and, not being an expert in the field, I'd have a hard time estimating their relative probability), and in the absence of prospective replication of a systematic sample of claims - which could determine whether the replication rate for a random sample of claims is as high as that observed in the literature -, both should be considered in the manuscript.

I still believe that most of ‘verified’ claims are indeed solid, consistent with the feeling of increased knowledge in the Drosophila immunity. Of note, when I started in the field in the early 90, nearly all the articles in Drosophila developmental biology, the dominant field at that time, were solid. I agree that this may represent a past period. Still, perceived irreproducibility is high because affecting claims published in high-impact articles. To address the reviewer’s comments, we have included the possibility of confirmation bias in the discussion of the article.

(2) The fact that the analysis of factors correlating with reproducibility includes both prospective and retrospective replications also leads to the possibility of confusion bias in this analysis. If most of the challenged claims come from the authors' prospective replications, while most of the verified ones come from those that were replicated by the literature, it becomes unclear whether the identified factors are correlated with actual reproducibility of the claims or with the likelihood that a given claim will be tested by other authors and that this replication will be published.

We agree that the ReproSci is a human biased endeavor and may be subjected to bias, notably the one mentioned. Some verified claims might be considered as challenged and some challenged claims as verified. But this is likely not affecting most of our results. Our papers have been posted on a public archive and that the community could scrutinize our data (most authors have checked their claims!). Based on community feedback, we have had to change the status of three claims only: one verified claim became challenged, one challenged claim became unchallenged and one unchallenged became verified. We therefore did not expect major changes in our conclusions. We have provided an estimation of irreproducibility ranging from 10-20% and we believe this is a rather safe interval. This is still significant. The fact that the ReproSci project is a human endeavor, and therefore subject to inherent limitations, is already emphasized in the last section of the discussion.

(3) The methods are very brief for a project of this size, and many of the aspects in determining whether claims were conceptually replicated and how replications were set up are missing.

Some of these - such as the PubMed search string for the publications and a better description of the annotation process - are described in the companion article, but this could be more explicitly stated. Others, however, remain obscure. Statements such as "Claims were cross-checked with evidence from previous, contemporary and subsequent publications and assigned a verification category" summarize a very complex process for which more detail should be given - in particular because what constitutes inferential reproducibility is not a self-evident concept. And although I appreciate that what constitutes a replication is ultimately a case-by-case decision, a general description of the guidelines used by the authors to determine this should be provided. As these processes were done by one author and reviewed by another, it would also be useful to know the agreement rates between them to have a general sense of how reproducible the annotation process might be.

The same gap in methods descriptions holds for the prospective replications. How were labs selected, how were experimental protocols developed, and how was the validity of the experiments as a conceptual replication assessed? I understand that providing the methods for each individual replication is beyond the scope of the article, but a general description of how they were developed would be important.

We have extended the first section of the Result to mention that an extended Material and Methods can be found in the complementary article Westlake et al., eLife 2026 and on the ReproSci website indicated the resources described in the companion articles. Disagreement between the two authors were limited and mostly dealt with textual interpretation (the definition of the major claims, which can affect if they are verified or not). As mentioned above, our articles are now public since more 6 months and we got little request to change the status of a claim (only 3 over more than 1000). Of note many claims from some ancient articles are part of the common knowledge, are verified routinely by many labs in the field, and therefore were easy to categorize.

We also added a sentence to also underline that the scientific value of an article does not fully correlate with its status. A number of problematic articles filled with exaggeration or confused claims were still categorized as verified. Thus, we screen for replicability but they are many other publication issues we could not capture in our study. This point is now mentioned in the discussion.

(4) As far as I could tell, the large-scale analysis of the replication results was not preregistered, and many decisions seem somewhat ad hoc. In particular, the categorization of journals (e.g. low impact, high impact, "trophy") and universities (e.g. top 50, 51-100, 101+) relies on arbitrary thresholds, and it is unclear how much the results are dependent on these decisions, as no sensitivity analyses are provided.

Particularly, for analyses that correlate reproducibility with continuous variable (such as year of publication, impact factor or university ranking, I'd strongly favor using these variables as continuous variables in the analysis (e.g. using logistic regression) rather than performing pairwise comparisons between categories determined by arbitrary cutoffs. This would not only reduce the impact of arbitrary thresholds in the analysis, but would also increase statistical power in the univariate analyses (as the whole sample can be used in at once) and reduce the number of parameters in the multivariate model (as they will be included as a single variable rather than multiple dummy variables when there are more than two categories).

We did not pre-registered our study, which is quite different from other reproducibility projects. We did not know at the start how the project would unfold. Of note, I believe that ‘cleaning’ an extensive field by experts was by itself an achievement and represent another way to assess replicability, with its own limitation.

We agree that the cut-off can be seen as arbitrary. However, publication year has been modeled as a continuous variable through a spline (to allow for non-linearity) in the multivariate analysis. For journal and institutional ranking, we would like to defend and keep the categorical specifications in the main text for two reasons:

- Institution ranking: For institutional ranking, the largest institutional category is “Not Ranked” which we cannot assign a rank and ranks institutions individually only through the top 100. Below that it publishes bands (101-150, 151-200, 201-300, 301400, 401-500) of variable width, which are not straightforward to use continuously without making strong assumptions (e.g midpoint) unsupported by the data.

- Prestige: As mentioned by another reviewer there are career consequences attached to Nature, Science and Cell that are different from other journal, and the effect of moving from a journal from an IF 3 to 8 is different than from 30 to 35. We provide a sensitivity analysis in the supplementary information where we refit the multivariate model with log-transformed impact factor continuous predictor. We obtain very similar results than these in the main text, with the exception that the impact factor of the journal becomes significant. We describe and discuss this results in the supplementary information (section S5), while justifying why we keep the categorical model in the main text.

We are grateful to the reviewer for prompting these additions, which we agree strengthen the paper.

The text added in the SI states:

“As a sensitivity analysis, we refitted the multivariable hierarchical logistic model by replacing journal-impact-factor categories with log₂-transformed continuous impact factor, while retaining all other covariates and random intercepts from the primary analysis. University ranking was retained as a categorical variable because the 2010 Shanghai Academic Ranking reports individual ranks only for institutions ranked 1– 100 and otherwise reports rank bands (101–150, 151–200, 201–300, 301–400, and 401–500); moreover, 441 of 1,006 claims (43.8%) were from unranked institutions, which constitute a distinct group.

Each doubling of journal impact factor was associated with 1.51-fold higher odds that a claim was challenged (OR 1.51, 94% HDI 1.13–2.08). At the mean impact factors of the low-impact and trophy-journal tiers (4.4 and 61, respectively; approximately 3.8 doublings), the continuous model implies a trophy-versus-low-impact odds ratio of approximately 4.8. By contrast, the primary model directly estimated the trophy-versus-low-impact odds ratio as 1.75 (94% HDI 0.59–4.91). Although this wide interval includes 4.8, the point estimates differ between the two models. We interpret the larger implied trophy-journal effect in the continuous model cautiously because it assumes that the log-linear slope estimated predominantly from the many journals with lower impact factors (around 2–12) applies unchanged to the sparsely represented trophy journals (62 claims across Science, Nature, and Cell). We therefore retained the categorical journal analysis as the primary analysis because it directly estimates the trophy-journal comparison using claims published in those journals. Estimates for all other covariates were broadly similar to those in the primary model. In particular, the association with Top 50 university affiliation remained evident (OR 4.04, 94% HDI 1.57–10.08, compared with OR 3.68, 94% HDI 1.50–9.28 in the primary model)”.

[This response is referred later as “Response to categorical variable encoding”]

(5) The multivariate model used to investigate predictors of replicability includes unchallenged claims along with verified ones in the outcome, which seems like an odd decision. If the intention is to analyze which factors are correlated with reproducibility, it would make more sense to remove the unchallenged findings, as these are likely uninformative in this sense. In fact, based on the authors' own replications of unchallenged findings, they may be more likely to belong the "challenged" category than to the "unchallenged" one if they were to be verified.

We thank the reviewer for raising this comment, we agree that the classification of the unchallenged claims as not challenged is difficult given their nature. We refitted the multivariable analysis excluding unchallenged claims, with a classification of Challenged and Unchallenged (Verified, Partially Verified, Mixed). The results are shown in the supplementary section S4 and are extremely similar to the main model.

The text added in the SI states:

“We fit the multivariate model from the main text while excluding unchallenged claims from the analysis. The methods are similar and the convergence and diagnosis checks are good and not reported here for brevity. The model simultaneously adjusts for author demographics, laboratory attributes and journal or institutional prestige and predict a binary outcome for each claim: challenged or not challenged (including Verified, Partially Verified, Mixed). The re-analysis included 659 claims, of which 60 (9.1%) were challenged. The non-challenged reference group comprised of Verified (n=525), Partially Verified (n=64), Mixed (n=10). The Adjusted odds ratios and 94% highest-density intervals are reported in Figure S4. The results are very similar to the analysis with the unchallenged claims in the main text, with only university ranking (Top 50) being a significant predictor (OR 3.34 (1.28–9.01) vs the main text OR 3.68 (94% HDI 1.50– 9.28). The other variable with the biggest changes shows only modest differences:

- High-impact journal OR 1.12 (vs 1.31)

- Trophy journal OR 1.47 (vs 1.75)

- Post-doc OR 1.44 (vs 1.16) and their intervals still include 1. Note that the excluding unchallenged decision condition on follow-up, which is not random and might be influenced by our key variable (journal tier, institutional ranking) and bias results for this model.”

However, we did not replace the main model of the article by this particular model because when you chose only claim that are either verified or challenged (so you exclude unchallenged), the condition that made these claims included in this analysis could be influenced by a cofactor, so our odds ratios might be wrong.

[This response is referred later as “Response to unchallenged exclusion”]

Reviewer #2 (Public review):

Summary:

Lemaitre et al. conducted an analysis of 400 publications in the Drosophila immunity field (1959-2011), performing both univariable and multivariable analyses to identify factors that correlate with or influence the irreproducibility of scientific claims. Some of the findings are unexpected, for instance, neither the career stage of the PI nor that of the first author appears to matter that much, while others, such as the influence of institutional prestige or publication in "trophy journals," are more predictable. The results provide valuable insight into patterns of irreproducibility in academia and may help inform policies to improve research reproducibility in the field.

Strengths:

This study is based on a large, manually curated dataset, complemented by a companion paper (Westlake et al., 2025. DOI 10.1101/2025.07.07.663442) that provides additional details on experimentally documented cases. The statistical methods are appropriate, and the findings are both important and informative. The results are clearly presented and supported by accessible documentation through the ReproSci project.

We thank the reviewer for their assessment.

Weaknesses:

The analysis is limited to a specific field (immunity) and model system (Drosophila). Since biological context may influence reproducibility -- for example, depending on whether mechanisms are more hardwired or variable -- and the model system itself may contribute to these effects (as the authors note), it remains unclear to what extent these findings generalize to other fields or organisms. The authors could expand the discussion to address the potential scope and limitations of the study's generalizability.

We have added a limitation section at the end of the manuscript to discuss these points. We wrote:

“Finally, the findings we report may be specific to a particular field, model organism, and time period, and may be strongly influenced by factors idiosyncratic to their development. Because this analysis is limited to a single field (immunity) and model system (Drosophila), it remains unclear to what extent these findings generalize to other fields, organisms, or more recent studies.”

However, we believe that our study adds on the discussion on reproducibility by providing another approach. Our study also aligns with the feeling that knowledge of Drosophila innate immunity has increased so much in the last decades, and that science is still quite robust in many fields.

Reviewer #3 (Public review):

Summary:

The authors of this paper were trying to identify how reproducible, or not, their subfield (Drosophila immunity) was since its inception over 50 years ago. This required identifying not only the papers, but the specific claims made in the paper, assessing if these claims were followed up in the literature, and if so whether the subsequent papers supported or refuted the original claim. In addition to this large manually curated effort, the authors further investigated some claims that were left unchallenged in the literature by conducting replications themselves. This provided a rich corpus of the subfield that could be investigated into what characteristics influence reproducibility.

Strengths:

A major strength of this study is the focus on a subfield, the detailing of identifying the main, major, and minor claims - which is a very challenging manual task - and then cataloging not only their assessment of if these claims were followed up in the literature, but also what characteristics might be contributing to reproducibility, which also included more manual effort to supplement the data that they were able to extract from the published papers. While this provides a rich dataset for analysis, there is a major weakness with this approach, which is not unique to this study.

Weaknesses:

The main weakness is relying heavily on the published literature as the source for if a claim was determined to be verified or not. There are many documented issues with this stemming from every field of research - such as publication bias, selective reporting, all the way to fraud. It's understandable why the authors took this approach - it is the only way to get at a breadth of the literature - however the flaw with this approach is it takes the literature as a solid ground truth, which it is not. At the same time, it is not reasonable to expect the authors to have conducted independent replications for all of the 400 papers they identified.

However, there is a big difference trying to assess the reproducibility of the literature by using the literature as the 'ground truth' vs doing this independently like other large-scale replication projects have attempted to do. This means the interpretation of the data is a bit challenging.

We acknowledge that our analysis necessarily relies on the published literature; however, two important points should be considered. First, we assessed replicability more than a decade after the original studies, allowing us to evaluate whether their claims have withstood subsequent scrutiny. Second, the evaluation draws on the authors’ strong expertise in the field. Accordingly, the validity of published claims was not accepted uncritically but subjected to informed expert assessment. This is exemplified by the case of the proposed microbicidal role of Duox, which we classified as challenged despite the original article accumulating more than 600 citations.

Overall, our replicability analysis, like similar efforts, relies not only on literature but also on expert judgment. Of course it has inherent limitations, which are now more clearly articulated in the discussion.

Below are suggestions for the authors and readers to consider:

(1) I understand why the authors prefer to mention claims as their primary means of reporting what they found, but it is nested within paper, and that makes it very hard to understand how to interpret these results at times. I also cannot understand at the high-level the relationship between claims and papers. The methods suggest there are 3-4 major claims per paper, but at 400 papers and 1,006 claims, this averages to ~2.5 claims per paper. Can the authors consider describing this relationship better (e.g., distribution of claims and papers) and/or considering presenting the data two ways (primary figures as claims and complimentary supplementary figures with papers as the unit). This will help the reader interpret the data both ways without confusion. I am also curious how the results look when presented both ways (e.g., does shifting to the paper as the unit of analysis shift the figures and interpretation?). This is especially true since the first and last author analysis shows there is varying distribution of papers and claims by authors (and thus the relationship between these is important for the reader).

Articles can contain claims that we found replicable and other that we did not. Thus, we believe than an evaluation by claim is more precise. The extraction of the different claims relies on the reading of the article, but is a human enterprise. There are clearly some unavoidable biases at this step. Of note, the articles analyzed in this study are very different one from another (size, novelty, amount of data…).

However, we agree that the analysis at the article level is interesting, and we followed the reviewer suggestion and provided in Supplementary Section S6 a sensitivity analysis of using article-level effects for the multivariate analysis. We note that because only 43 articles (12.5%) contained at least one challenged claim, this analysis is less robust than the claim analysis. The text added in the SI states:

“Two claims in the same paper might not be independent, so we might want to incorporate an article random effect to the primary Bayesian formulation. However, due to the low number of claim per article (mostly one to four) and only 43 articles (12.5%) contained at least one challenged claim (and most articles contains only one to four claims), we could not manage to fit this model properly (we observe MCMC divergences). As a work-around sensitivity analysis, we repeated the analysis with the article as the unit. Each of 345 articles with complete covariate data (representing 869 major claims, 60 of the 69 challenged claims in the full dataset; the remaining 9 fell in articles excluded for missing covariates) contributed as outcome the proportion of its major claims classified as challenged. The model was a (frequentist) binomial-link fractional-response generalized linear model with HC3 standard errors (the intervals reported here are 94% confidence intervals rather than posterior credible intervals).

Each article contributed equally regardless of its number of claims. The Top-50 institutional effect remained significant under both analysis (OR 5.15, 94% CI 2.18– 12.15; versus a claim-level OR 3.68, 94% HDI 1.50–9.28). In this new model Trophy journals also showed had higher odds of challenged claims than low-impact journals (OR 2.90, 94% CI 1.24–6.78 vs a claim-level OR 1.75, 94% HDI 0.59–4.91). This impact was not significant in the primary model but became significant at using article-level analysis. Other estimates are consistent in direction and magnitude with the primary claim-level model. Model diagnostics were satisfactory.”

Moreover, we added Figure S6 which display visually the relationship between the claims and the article.

[This response is referred later as “Response to claim vs article level analysis”]

(2) As mentioned above, I think the biggest weakness is that the authors are taking the literature at face value when assigning if a claim was validated or challenged vs gathering new independent evidence. This means the paper leans more on papers, making it more like a citation analysis vs an independent effort like other large-scale replication projects. I highly recommend the authors state this in their limitations section.

We have now explicitly acknowledged this limitation in a dedicated section at the end of the revised manuscript. However, as noted above, we do not take the literature at face value. Notably, some of the claims we identify as challenged originate from highly cited articles, which could lead a naïve reader to assume their validity.

Ultimately, this replicabilty project remains a human, expert-driven effort aimed at determining which claims withstand scrutiny within a field. The broader community was invited to engage with and respond to these assessments and we did get some feedbacks. Importantly, claims were not evaluated in isolation but in the context of the entire body of knowledge, and all evaluations were made transparent and explicitly justified in the ReproSci database.

On top of that, I have questions that I could not figure out (though I acknowledge I did not dig super deep into the data to try). The main comment I have is How was verified (and challenged) determined? It seems from the methods it was determined by "Claims were cross-checked with evidence from previous, contemporary and subsequent publications and assigned a verification category". If this is true, and all claims were done this way - are verified claims double counted then? (e.g., an original claim is found by a future claim to be verified - and thus that future claim is also considered to be verified because of the original claim).

When two articles reported the same main claim and this claim was judged as “verified,” each instance was counted in the analysis. However, when validation came from studies published after 2011, the claim was counted only once. Thus, our study specifically evaluates the replicability of claims originating from a defined period (pre-2011).

We note that, in principle, repeated publication of the same finding across many articles could artificially inflate estimates of replicability. However, such cases appeared to be rare in practice, and studies reporting similar claims typically provided complementary evidence—for example, elucidating gene function through either genetic or biochemical approaches.

Related, did the authors look at the strength of validation or challenged claims? That is, if there is a relationship mapping the authors did for original claims and follow-up claims, I would imagine some claims have deeper (i.e., more) claims that followed up on them vs others. This might be interested to look at as well.

We did not perform a systematic mapping between original claims and subsequent follow-up studies. While this is an important and interesting aspect, it was considered beyond the scope of the present work. The current study already represents a substantial investment of time and effort, and the resulting database provides a valuable resource for future analyses. In particular, it could support a dedicated bibliometric study at a later stage.

(3) I recommend the authors add sample sizes when not present (e.g., Fig 4C).

The cited panel appears to correspond to Figure 5C in the revised numbering, as the current Figure 4 contains only panels A and B. We systematically checked the denominators of all figures and revised the captions to report the numbers of claims, authors or laboratories represented, together with the reasons for exclusions. We also added the numbers of authors and claims directly within the author-level scatter plots, with the observational unit explicitly identified.

I also find that the sample sizes are a bit confusing, and I recommend the authors check them and add more explanation when not complete, like they did for Fig 4A. For example, Fig 7B equals to 178 labs (how did more than 156 labs get determined here?), and yet the total number of claims is 996 (opposed to 1,006).

There are 156 labs total, 23 labs contributed publications during both junior and senior stages, and 11 claims lacked a junior/senior classification. This has been explicited in the caption.

Another example, is why does Fig 8B not have all 156 labs accounted for?

The panel does not include all 156 laboratories because we could obtain information about first author training for only 146 PI and laboratories while prior first-author status was unavailable or indeterminate for ten PI. This has been added to the caption.

(Related to Fig 8B, I caution on reporting a p value and drawing strong conclusions from this very small sample size - 22 authors).

The 22 authors are not the total sample size; they constitute the subgroup of PIs who had previously published a first-author paper on Drosophila immunity in another laboratory. In the submitted panel, they were compared with 117 PIs without this training history, giving 139 classified laboratories and 774 claims.

As a last example, Fig 8C has al 156 labs and 1,006 claims - is that expected? I guess it means authors who published before 1995 (as shown in Figure 8A continued to publish after 1995?) in that case, it's all authors? But the text says when they 'set up their lab' after 1995, but how can that be?

Thank you for identifying this inconsistency. Figure 8C intentionally includes the full cohort of 156 PIs and all 1,006 claims. Panel C compares research styles and does not impose a restriction based on year of entry into the field or year of claim publication. Thus, PIs who entered the field before 1995 are included together with all claims attributed to them; the panel is not restricted to claims published after 1995.

The statement that only PIs who established their laboratories after 1995 were included was an erroneous carryover from an earlier version of the analysis. We removed this restriction from the Results and revised the caption to state that exploratory PIs (n = 91) contributed 366 claims, whereas continuity PIs (n = 65) contributed 640 claims.

We also replaced references to the date when PIs “established their laboratory” with “year of entry into the field,” defined as the year of their first Drosophila-immunity publication as either first or last author. During the same check, we revised Panel B to include all 146 PIs eligible for the pre-PI training comparison, contributing 793 claims.

(4) Finally, I think it would help if the authors expanded on the limitations generally and potential alternative explanations and/or driving factors. For example, the line "though likely underestimated' is indicated in the discussion about the low rate of challenged claims, it might be useful to call out how publication bias is likely the driver here and thus it needs to be carefully considered in the interpretation of this. Related, I caution the authors on overinterpreting their suggestive evidence. The abstract for example, states claims of what was found in their analysis, when these are suggestive at best, which the authors acknowledge in the paper. But since most people start with the abstract, I worry this is indicating stronger evidence than what the authors actually have.

We have added a dedicated section on limitations at the end of the Discussion to explicitly acknowledge key constraints, and we also address these points throughout the Discussion where relevant. In addition, these limitations are now in the abstract.

The authors should be applauded for the monumental effort they put into this project, which does a wonderful job of having experts within a subfield engage their community to understand the connectiveness of the literature and attempt to understand how reliable specific results are and what factors might contribute to them. This project provides a nice blueprint for others to build from as well as leverage the data generated from this subfield, and thus should have an impact in the broader discussion on reproducibility and reliability of research evidence.

Thank you for this positive assessment!

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Comments and recommendations are provided in the order that they appear in the manuscript.

Introduction:

- In the second paragraph of the introduction, I don't think all the references refer to "molecular life sciences" (e.g. one of them is from ecology and evolution, for example). I'd also argue that Macleod et al. 2014 refers to risk of bias rather than to reproducibility per se.

We have corrected this in the revised version.

- The author use both "reproducibility" and "replicability", apparently as synonyms, but as definitions for these words vary across sources (e.g. https://arxiv.org/abs/1802.03311, https://www.nationalacademies.org/our-work/reproducibility-and-replicability-in-science, https://osf.io/br9sp/) it may be worth stating their definitions upfront.

Thank you for the references. We agree that the literature contains multiple, sometimes conflicting definitions of these terms, which can lead to confusion. In response to the reviewer’s comment, we have clarified our terminology. Specifically, we now use the term “conceptual replicability” in the abstract and consistently refer to “replicability” and “irreplicability” throughout the manuscript. We hope this revised terminology improves clarity.

- Why are analysis described as "exploratory" and "multivariate"? If it has not been preregistered, shouldn't the multivariate analysis be considered exploratory as well?

Thanks, we agree. The word “exploratory” is confusing as we use it for its structural meaning and not its epistemological meaning. We have replaced it throughout by “descriptive”, as to not imply that the multivariate analysis is preregistered by contrast.

Results:

Methodology and claim assessment

- The methods for the selection, annotation and classification of studies are described very cursorily here, and the Methods section doesn't add that much, but I'll keep these observations to the methods. Still, it's worth mentioning that it's hard to know how reproducible the annotation and classification process is from the information provided.

We have provided more information on the method section on the way to annotate and class claims. Of note, there is more information on the methods on the associated publication Westlake et al., 2025 and on the ReproSci website.

- "Then, experimental work was performed in several laboratories...". Once again, a much better description of how replications were set up and performed is needed.

We have provided information on the number of laboratories (nine) involved in the reproduction of 45 major claims. The laboratories involved in replication are listed in the author list. All the files associated with experimental replication can be found in the supplementary materials of Westlake et al 2025 or the ReproSci website.

- "These claims subjected to experimental validation were selected according to criteria such as appearing suspicious due to the absence of direct follow up or being straightforward to test experimentally". This is rather vague, but if no explicit criteria were set upfront this may be inevitable. Still, it would be useful to know who made this decision.

A first list of claims to be replicated was made by Hannah Westlake and Bruno Lemaitre. The claims that were selected to be replicated were tested by the labs and experimental workers that had the expertise required to test them. The choice of the claims to be tested was not random. Claims that were suspicious are claims that were already tested in the host laboratory without success, claims whose validity are debated at meeting, claims from highranked journal with no follow-up. This is now indicated in the method of the revised version.

Drosophila immunity claims are mostly reproducible

- The percentages given in the initial description of the results pool the results of the retrospective analysis of the literature and the prospective replications performed. As mentioned in the Public Review, I think these are rather distinct ways to assess reproducibility, and would recommend that these two analyses are described separately.

We agree with the reviewer but we believe that we have already well separated the results before and after experimental work in the revised version. This is clearly shown in Table 1. Our text says ‘Importantly, 6.8% of claims (69 out of 1006) were challenged. Among these, 44.9% (31 out of 69) were contested by published articles including 7.2% by the same authors, and 55.1% (38 out of 69) were challenged experimentally as part of the ReproSci project.’

- "These results may reflect the robust scientific standards and methodological rigor of Drosophila research...". Once again, as mentioned in the Public Review, I think publication bias is a plausible explanation, so this should be mentioned as an alternative.

We have mentioned publication bias in the revised version in the section on limitation. But an important point to underline is that this analysis did not take publication results as face fact. This is a critical analysis by experts in the field. As already mentioned, some claims like ‘Duox produces microbicidal ROS” ‘NO is a signaling molecule…’that have been mentioned in multiple articles were considered as challenged.

A second point is that it is likely that publications in some fields are more replicable than in other. Actually, we did not discuss ‘reproducibility issues’ when I started in the field 30 year ago because this was not perceived as an issue. It is normal that reproducibility rate varies according to fields. Nevertheless, we do find important claims with high visibility that are not replicable in our sample. Thus, our findings nuance the ‘reproducibility crisis narrative’ but we still believe that there is concern with reproducibility in life science. Last point, the criterium we have used in our study did not map all the problematic papers, notably some claims might be fundamentally verified but exaggerated in the original paper.

- It would be useful to break down the "partially verified" category somewhere. Illustrative examples of what is meant by "insightful data were accompanied by incomplete interpretations" or "incomplete data were paired with insightful interpretations" would be useful as well.

All the claims are listed in the public database with an explanation as to why they got affected to a category. The categories mixed and partially verified refer to claims that are more complex to categorize.

Here are are two examples from the ReproSci website:

Claim: Relish Rel mutants are very susceptible to bacterial and fungal infection. Partially verified

Assessment: Relish mutants are primarily susceptible to Gram-negative bacterial infections, and do not typically have increased susceptibility to Gram-positive bacteria and fungi which are primarily rebuffed by the Toll pathway, although Imd signaling may provide a minor contribution to defense against these. The high susceptibility of Relish mutant to fungi observed in this article is likely due to the presence of the ebony marker (Lemaitre et al., 1996) [here only one part of the statement has been verified]

Claim: PGRP-SC1a is required for Lys-type peptidoglycan recognition and Toll activation. Mixed

Assessment: A possible role for PGRP-SCs in Toll activity has been strongly debated. Challenged by (Bischoff et al., 2006) who found no effect of PGRP-SC RNAi on activation of Toll (Drs expression) in adult flies (although note that their data show a minor reduction of Drs expression in flies in response to E. faecalis). Supported by (Costechareyre et al., 2016) who used single -SC1 and -SC2 mutants to show that Toll activation (Drs expression) was reduced in -SC1 but particularly -SC2 mutants (~50%) in response to E. faecalis (although survival was not affected). The supplementary data of (Paredes et al., 2011) similarly show that Drs expression was reduced (50%) in response to M. luteus septic infection in PGRP-SCdelta flies (PGRP-SC1A/B -SC2 triple mutant), but concluded that this was due to a secondary effect of Imd overactivation. Note that the phenotype found by (Garver et al., 2006) was much stronger (complete ablation of Drs expression), which is not consistent with any subsequent results and argues for a secondary mutation in this line, although this is not consistent with the successful rescue of Drs expression by transgenic replacement of PGRP-SC1a. Downregulation of Toll in these mutants could be explained if the Toll pathway requires amidase activity of PGRP-SC for immunogenicity (e.g. the sugar backbone without stem peptides is a stronger elicitor than whole peptidoglycan), whereas similar cleavage reduces recognition by the Imd pathway (consistent with the demonstrated requirement of stem peptides for full stimulation of the Imd pathway (Chang et al., 2005; Stenbak et al., 2004)). See annotation for (Mellroth et al., 2003). [here the claim is mostly challenged but there are observations that go in the same directions]

As shown by these examples, category assessment was complex process and relied on human expertise. However, there was very little contestation from the community after the submission of our articles and the opening of the ReproSci website.

A significant fraction of unchallenged claims is non-reproducible

- Excluding the 45 unchallenged major claims that were experimentally tested, we categorized the remaining 240 unchallenged claims into three groups". No information is provided on that classification process (either here or in the methods). Who made these assessments (which seem quite subjective and dependent on field expertise), and how do you know if such judgments are reproducible across different evaluators?

This categorization was done by Hannah Westlake and reviewed by Bruno Lemaitre with few disagreements. This is now indicated in the revised version. The category ‘unchallenged logically consistent” and ‘‘unchallenged logically consistent’ refer to claims that although not directly verified are corroborated or in with current literature. See ReproSci for justifications.

Example from ReproSci website:

Claim: The minimal structure needed to activate the Toll pathway is a muropeptide dimer.

Assesment: Unchallenged logically consistent This is consistent with (Park et al., 2007) who show that on a linearized strand of peptidoglycan, the minimal motif is at least 3 dimers. But it is expected that a non-linearized dimer linked by the peptide bridge could serve as the minimal motif by clustering peptidoglycan.

Claim: eater null flies are susceptible to oral infection with Serratia marcescens Unchallenged logically consistent Inconsistent with the observation that Eater mutants successfully phagocytose Serratia marcescens (Bretscher et al., 2015). This may indicate that another factor affected by eater mutation is required for defense against S. marcescens, such as formation of lamellopodia and filopodia or adhesion of hemocytes to the body wall, or that Eater contributes to binding of Gram-negative bacteria but does not trigger phagocytosis in response to them as it does for Gram-positive bacteria.

Higher representation of challenged claims in trophy journals and from top universities

- Both impact factor and the Shanghai university ranking are continuous variables, but the authors opt to use them as categorical variables in the analysis (i.e. "low-impact", "highimpact", "trophy"; "Top 50", "51-100", "101+"). While there may be legitimate reasons to do this if they feel that these categories are a better descriptor of the underlying reality (e.g. perhaps Cell, Science and Nature are indeed in a category by themselves), it is an unusual decision that leads the comparison to ignore the distinctions between journals/universities within a category. Moreover, it also opens up the opportunity to analysis bias as categories can be set up in many different ways. Thus, if the analysis was not preregistered, I'd recommend that analyses using impact factor and ranking as quantitative variables are added as sensitivity analyses, as these seem to me to be the most natural/less ad hoc way to look at the issue.

See “Response to categorical variable encoding” above.

- As mentioned in the Public Review, the analysis here pools the results from the retrospective analysis based on the literature and the prospective one based on the performed replications. Although this may be justified from a sample size perspective (as the number of challenged claims is not that high), it would be useful to perform this analysis separately on the two sets of results as well, as different trends may be noticed. There are many biases that might come into play here (e.g. results from top institutions being more or less likely to have challenged/unchallenged claims published) and looking at the results separately could help in tearing apart these hypotheses.

The ReproSci project analyzes all the papers of a community during a period of time. As such, the total number of claims is limited and we believe that pooling the data was justified. We provide as sensitivity analysis in Supplement S7, a multivariate model with claims in their pre-experimental classification state:

“As a sensitivity analysis, we refitted the multivariable hierarchical logistic model using only the claim classifications available before experimental validation by the ReproSci project, as the choice of which claims to further validate could have been influenced by covariate (impact factor, university status). The 45 claims tested prospectively were therefore restored to their original “Unchallenged” classification, while all covariates and author-level random intercepts were retained from the primary analysis. The complete-case analysis included 869 claims, of which 28 (3.2%) were challenged. No predictor had a 94% highest-density interval excluding 1, including publication in trophy journals (OR 1.11, 94% HDI 0.33–3.77) and affiliation with a Top50 institution (OR 1.44, 94% HDI 0.48–3.94). Thus, the associations observed in the pooled analysis were not evident when using classifications based exclusively on the retrospective literature review, although estimates were imprecise because of the small number of challenged claims”

The irreproducibility rate has increased over time as the field has grown in popularity

- Again, why not use year as a continuous variable rather than using 5-year windows (as this would effectively include more information)? I think the categorization here is less ad hoc than in the journal/university case, but it is still an unusual decision. More important than this, however, is the fact that pairwise comparisons between periods is probably not an appropriate strategy to look for a time trend, as it excludes all information not related to the pair in each analysis. I'd strongly suggest substituting this for a straightforward regression with publication year as a continuous variable.

We thank the reviewer for this important suggestion. We agree that categorizing publication year into five-year periods may obscure temporal trends.

We therefore modelled publication year continuously using a spline in the multivariable analysis, thereby retaining the full temporal information while allowing for non-linearity. A straightforward linear regression would impose a linear trend, which may not adequately capture changes over time. We retained the five-year groupings solely for visualization.

- "The subsequent increase in unchallenged claims may reflect the rapid conceptual expansion of the field, which likely outpaced the growth in the number of researchers". Do we have data on the growth in the number of researchers in the field? If so, it might be interesting to cite this.

We do not have the number of researchers to assess the growth of the field, however we can see in Figure 8A an increase in the number of laboratories (as identified by last author name) after 1995. This together with the increase in the number of articles (Figure 3A) clearly show the expansion on of the field.

- Isn't a "rise in unchallenged claims" over time expected by chance, as older findings will have more time to have been verified by someone else? I understand that the 14-year window probably mitigates this effect, but it still probably exists in some degree and should be mentioned.

The reviewer is correct that the % unchallenged claims should increase over time, but this does not explain the very low number of unchallenged claims between 1992-2001.

First-author patterns of irreproducibility

- With 69 challenged claims and 289 first authors, it would be impossible to achieve "perfect equality" (e.g. a Gini index of 0.88). To verify how far the observed coefficient deviates from chance, it would be useful to obtain (perhaps via simulations) the Gini coefficient expected by chance given the number of challenged claims/authors, and perhaps derive a p value as well (e.g. the proportion of random permutations in which the index exceeds the observed value).

Very good observation, thank you, we provide this analysis for both first and last author, in the main text and in a supplementary table.

Added first author text:

“The distribution of challenged claims among first authors was highly unequal with a Gini coefficient of 0.881 (inequality index ranging from 0 -perfect equality- to 1 extreme inequality-, Figure 4B): the top 10% of first authors accounted for 73.9% of challenged claims, and the top 20% accounted for all challenged claims. This inequality exceeded that expected by chance (reassigning randomly the 69 challenged labels across individual claims, while preserving each author’s number of claims, p = 0.000001). It also remained greater than expected when claims from the same paper were kept together (p = 0.015; Supplementary Table Sx). The concentration of challenged claims among first authors cannot be explained solely by differences in the number of claims or by clustering within papers.”

Added last author text:

“Challenged claims were also unevenly distributed among leading authors (Gini coefficient = 0.856): the top 10% accounted for 71.0% of challenged claims and the top 20% accounted for 94.2%. The observed inequality exceeded that expected when challenged labels were reassigned across individual claims (p = 0.00081), but not when claims from the same paper were kept together (p = 0.127; Supplementary Table S9). The apparent concentration among leading authors could be explained by multiple challenged claims arising from the same papers.”

Added method text:

“We compared the observed Gini coefficients with two permutation analyses, each based on 1,000,000 permutations. First, we randomly reassigned the challenged labels across individual claims while keeping every claim attached to its original author. This preserved the number of claims contributed by each author. Second, we kept the challenged-claim pattern of each paper together and reassigned these patterns among papers containing the same number of claims. This additionally accounted for the possibility that claims from the same paper were challenged because of a shared problem. For each permutation, we recalculated the Gini coefficient across authors and calculated the p-value as the proportion of simulated coefficients that equalled or exceeded the observed coefficient. Full results are reported in Supplementary.”

- Claims in a single paper may not be fully independent from each other (as both could be irreproducible due to the same error), so it could be worth adding the article as a random variable here.

See answer above: [“Response to claim vs article level analysis”]

- In Fig. 4B, what defines the order of the dots between 0 and 250 (i.e. authors that have no challenged claims)? Is this merely arbitrary? This should be stated more clearly.

Thank you, the order was arbitrary, it has now been fixed by using a secondary sorting (verified claim proportion), and Authors tied on challenged-claim proportion are ordered by verified-claim proportion has been added the legend.

- In Fig. 5C, there are clearly less dots than there are authors. This is likely due to superposition (i.e. there are probably multiple circles with 1 article and 0% verified claims). Nevertheless, it means that the graph conveys an erroneous message. As the x axis is a discrete variable, it may be worth turning it into five categories (e.g. 1 to 5) and adding some jitter to each of them in order to let the reader know how many dots are in each category/%.

Thank you, this was indeed due to superposition. After trying to add a jitter, the graph was still confusing, so we changed the representation to show circle whose size depends on the number of authors. The graph now conveys the size of each block properly.

Lead-author patterns of irreproducibility

- The same comment concerning the Gini index made for the first authors also holds here.

We added a text, see answer above.

- In Fig. 6B, the same comment made for figure 4B also holds.

Thank you, the order was arbitrary, it has now been fixed by using a secondary sorting (verified claim proportion), and Authors tied on challenged-claim proportion are ordered by verified-claim proportion has been added the legend.

- The division between "senior" and "junior" PIs is rather ad hoc here. Once more, why not use "years from first last-author publication" as a continuous variable as a more neutral way to analyze this (as done in Fig. 8)? Also note that it is not clear whether "published a lastauthor article at least five years prior to the considered publication" means any article or one about Drosophila immunity (as in Fig. 8A), and which database was used to examine this (PubMed? Other?).

Senior and junior researchers were classified based on whether they had published a last-author article five years or more using Pubmed (for seniors). We did not specify articles in Drosophila immunity when considering seniority but only having a last author article five year before the publication.

- In Fig. 7C, the same comment made for Fig. 5C also holds, although the solution here is less obvious as there are more possible numbers for "number of articles".

Thank you. As in Fig. 5C, superposition obscured multiple authors occupying the same coordinates. We therefore revised Fig. 7C so that authors with the same number of articles and proportion of challenged claims are represented by a single circle. Circle size and the number shown inside indicate how many authors are represented.

- As far as I could tell, the data on Fig. 8A refers to when authors published their first first/last author papers on Drosophila immunity (which makes it different from Fig. 7, which refers to any article, but I could be mistaken). If this is the case, I'm not sure it's correct to talk about "the period when principal investigators established their laboratories" as mentioned in the text, as (a) they could have published a first author paper in somebody else's lab or (b) they could have started a lab and only later published a paper on Drosophila immunity. "Year of entry in the field" as in the figure legend seems more appropriate.

We have changed for ‘year of entry in the field’ as suggested by the reviewer

- In the same figure, the 1995 cutoff seems completely arbitrary. Why not analyze this as a regression with year of entry as a continuous variable?

The 1995 boundary is historical as it marks the expansion of Drosophila immunity from a marginal subject into a popular field. The expansion of the field at this specific time was probably driven by a combination of factors: major advances in Drosophila genetics and genomic resources and growing knowledge of antimicrobial peptides in the early 1990, a strong interest on innate immunity that drew attention on the power of Drosophila to answer key questions in this new area. These developments attracted new researchers to insect immunity, and the later discoveries of the IMD and Toll pathways in 1995 and 1996 gave the field an additional (and probably even stronger) boost. Our corpus holds 29 articles for 1959– 1994 (0.8 per year) against 371 for 1995–2011 (21.8 per year), and only 13 of the 156 PIs entered before 1995. The comparison is therefore a cohort contrast more than a contrast or search for a cutting point. Moreover, a regression would impose a linear relationship between the different years, which we believe is too constrained on regard of the observed data.

- "We hypothesized that these authors, having gained prior hands-on experience on Drosophila immunity, would be less prone to publishing irreproducible claims.". This is a possibility, but given that most of the sample is retrospective, it's also possible that the field is more prone to publicly challenging findings from newcomers.

Since we do not observe major difference in replicability between senior and junior PI, we still believe that training as first author in a traditional immunity laboratory compared to no training is significant.

Irreproducibility according to research styles

- The objective definition of "continuity" and "exploratory" PIs should be stated here for this to be interpretable (note that this is not clear in the Methods either).

We have better defined how we separate "continuity" and "exploratory" PIs in the methods and in the result section.

Multivariable analysis of predictors of claim irreproducibility

- As mentioned in the Public Review, does it make sense to include "unchallenged" along with "verified" in the outcome? If the objective is to reduce the analysis to a "verified/not verified" claim, wouldn't it make more sense to remove the unchallenged findings (as these are likely uninformative, and based on the authors' own replications may be more related to the "challenged" category than to the "unchallenged" one?

See above, “Response to unchallenged exclusion”

- As stated previously, why not include journal impact factor, university ranking, year of first paper and year of first Drosophila immunity paper, as continuous variables rather than categorical ones (which would effectively lead to a model with less parameters when there are more than 2 categories). Particularly, there is more information to be gained from adding a single variable than from performing individual comparisons between categories when these have a natural order.

See above, “Response to categorical variable encoding”

Discussion:

- As "conceptual reproducibility" is somewhat of a vague concept, it seems important to discuss (both in the Methods and Discussion) how this was operationalized. Although it's obvious some decisions of what constitutes a direct replication will vary on a case-by-case basis, general guidelines on how these criteria were set are needed.

We have defined in the methods used to categorize article claims as well as the link with the other companion article. In the ReproSci database, all the assessment are justified allowing to see how we classified claims.

- "Contrary to the more dramatic narratives...". Here, it is important to emphasize the key differences between this and the cited references: (a) the fact that the majority of the replicability of the sample was found on the basis of a retrospective sample and (b) the fact that the study is dealing with conceptual rather than direct replications. Also, the possibility of confirmation bias should be mentioned as an alternative hypothesis in the last sentence of this paragraph.

This is a good point and we have highlighted that methodological differences between our study and other studies could explain differences in replicability rates.

- "findings that, despite being published, have never been independently tested". A more accurate description may be "have never been independently confirmed or refuted in the published literature", as many (and perhaps most - see Baker 2016) replication attempts may go unpublished, as the following sentences themselves indicate.

We have changed the text according to the reviewer’s suggestion.

- The description of how findings came to be regarded as "suspicious" here is interesting - and an important part of how the sample was determined. In this sense, I'd consider this as part of the methods. Even though defining what makes something "suspicious" may not be completely systematic, a general description of the method that led the researchers to arrive at this list (e.g. the process that seems to be hinted at in this paragraph) deserves a thorough description.

The description of how findings came to be regarded as "suspicious" is now detailed in the methods.

- "Our results suggest the status of a claim being "unchallenged" is not a reliable proxy for its validity". I agree, but this is statement is in direct contradiction with the authors' decision to include unchallenged claims along with validated ones in the binary outcome of the multivariate model.

See above, “Response to unchallenged exclusion”

- "Trophy journals are more likely to publish articles with challenged claims than high or lowimpact, although the difference was not significant." Again, a single analysis using a continuous measure of impact should provide more statistical evidence than the pairwise comparisons.

See above, “Response to categorical variable encoding”

- "However, this higher rate of follow-up work cannot fully explain by itself the higher proportion of challenged claims in trophy journals." Why not, exactly? I don't remember seeing an objective analysis of it.

If we remove the unchallenged claims, we still observe higher rate of irreplicability in trophy journal: 15.85% in trophy journal versus 9% in high-impact and 8.1% in low-impact. So we believe that the higher rate of irreplicability in trophy journals cannot be explained by a lower level of unchallenged.

- The very large paragraph on pages 21-22 could be split into two, one about journals and the other about universities.

This has been done.

- "Our data align with the broader narrative of increasing rates of non-reproducible science.". Does it? The time trend did not seem very clear to me (and I would argue that it was not analyzed properly).

As indicated in the text, we observed an increase in the rate of irreplicable claims over time; however, this trend did not reach statistical significance. We are confident in the robustness of our analysis and therefore did not pursue this question further. While our findings align with concerns about non-replicable science, they also offer a more nuanced perspective, showing that in some fields, replicability remains significantly high.

- "A similar but more acute pattern was observed during the SARS-CoV-2 pandemic." References should be provided here.

We have added this reference to suggest that articles published on SARS-CoV-2 pandemic are overall less reliable than others: An alarming retraction rate for scientific publications on Coronavirus Disease 2019 (COVID-19) Nicole Shu Ling Yeo-The https://doi.org/10.1080/08989621.2020.1782203

- Some of the trends discussed here (e.g. time, continuity vs. exploratory style are not supported (even as a trend) by the multivariate model, and this caveat should be mentioned. An odds ratio of 0.89 with a very wide confidence interval may be too weak in terms of evidence strength to merit a whole paragraph in the introduction discussing it.

We did not mention the question of time horizon or the distinction between continuity and exploratory research styles in the Introduction; however, we believe these issues merit consideration in the Discussion. In particular, the contrast between continuity-driven and exploratory approaches is noteworthy. Although we found no significant difference in the rate of challenged claims between these approaches, there was a significant difference in the rate of unchallenged claims, which are subsequently more likely to be challenged. This finding is important in the current funding landscape, where many agencies prioritize short-term, exploratory projects. Such incentives may inadvertently contribute to issues of irreproducibility.

- There are many other limitations beyond those mentioned, in particular the fact that much of the analysis is retrospective and based on a potentially biased literature. The fact that the analysis does not seem to be preregistered and is dependent on a lot of ad hoc decisions also merits discussion. This should definitely be explored in more detail in the Limitations section.

These limitations are now discussed in the limitation section at the end of the discussion. We agree on the fact that our analysis was not preregistered and that some of our conclusions are raised after analyzing the data. This article is part of a more global project including the databases with all the information. However, full objectivity when analyzing literature is not unachievable, and these critics are inherent to all reproducibility projects.

Methods:

Selected articles, annotation and experimental validation:

- "In brief, a list of 400 publications published before 2011 was generated using a curated search string on the publicly available PubMed database.". Please state that the search string is available in the companion article (e.g. https://doi.org/10.1101/2025.07.07.663442) or include it here.

This is now stated.

- "Selected primary articles were annotated by a single researcher".

By "annotation", do the authors mean the extraction of claims? This is not self-evident. Also, what does the "review" process entails? Do the authors have any data on agreement?

We do not have data on agreement but overall, there were few discrepancies. We agree that the way to section article in separate claims could affect the conclusion in a number of cases. All the data are public and we did not have any request from the community. The fact that this project depends from arbitrage from the two annotators is mentioned in the limitations.

- "Claims were cross-checked with evidence from previous, contemporary and subsequent publications and assigned a verification category."

How was this process performed? This seems to be quite complex and there's hardly any information about it. And once again, do the authors have any data on how reproducible this process would be when performed by different people?

All the data, notably claim assessment and justifications, are available on the website. Findings cross-checking the claim could be identified by knowledge of the authors, checking articles that quotes the articles. This was an enormous amount of work with human arbitrage. We expected more feedback from the community. The reaction of the community will be described in a companion article later.

- The authors mentioned that annotations and verifications were made available for comments on the community, but how were these comments incorporated if different opinions were voiced? Can the authors provide data on how frequent these comments were, and how often they were incorporated?

All data is available on the website, where members of the community can publicly comment on our assessments. The authors can see these comments on the ReproSci website

Table 1:

- Again, the three "partially verified" categories in Table 1 seem to refer to very different situations and it would be interesting to break these down somewhere.

We agree that categories ‘mixed’ and ‘partially verified’ are complex. They represent situations where a decision was not easy. We prefer not to break down those categories in multiple sub-categories.

First and last author classification:

- What does "status of first author" mean?

Status means their position: technician, PhD student, Post-doc, PI….

- "PIs were manually classified as..." - there seems to be something missing in this sentence (e.g. "as senior or junior on the basis of whether they have...")

We have added PIs: PIs were manually classified as senior or junior PIs on the basis on having published an article in Pubmed as last author more than five year ago.

- The distinction between continuity and exploratory is not explained in objective terms. Is there any objective definition of what it means to "continue to work in the field". Publishing a paper in the last X years? And what counts as a "transient" incursion?

We have better explained in the methods this distinction.

Statistical analysis:

- Can the authors define exactly what they mean by "weakly informative priors"?

Weakly informative prior are Bayesian prior distribution that are meant to be vague as to let the data dominate the results (vs the prior belief of the scientist). They can be seen as very close to flat priors, which are not used here because they cause numerical convergence issues.

- The authors mention a lot of variables included in the multivariable analysis, but little information is provided on the categorization. What are "low, high and trophy journals"? What university rankings are used?

We used Shanghai Ranking’s 2010 Academic Ranking of World Universities as our ranking of university. Our binning of ranking in categories make the analysis less susceptible to changes in ranking system. We selected the Shanghai ranking as it primarily evaluates research output and awards (where Times also evaluate teaching, and QS also employer reputation), which we believe represent better the variable than may affect irreplaceability. For the categorization, please see answer above: “Response to categorical variable encoding”

- "Exact formulas (...) are available in the public repository". What repository do authors mean? The project website? The GitHub repository? Please specify and provide a direct link if possible.

We added a link to the main text (it was only in the supplementary document). The Supplementary document contains information on how to reproduce the results.

Reviewer #2 (Recommendations for the authors):

Specific comments:

Some methodological details related to the main conclusions of the paper are missing.

We have extended the methodological section and also better link this article to the companion article.

- Impact factor: It is unclear which year(s) of journal impact factors were used. Trophy journals are defined as those with an impact factor >50 (Science, Nature, and Cell), but according to Figure 2B, there are only three such journals. Are "trophy journals" limited to these three, or are others included that meet the >50 impact factor threshold?

These are the 2022 impact factor, we made that clear in the main text. Moreover, only 3 journals in our datasets had an impact factor >50: Nature, Cell, and Science (so the Trophy Journal category is limited to these 3, but not by definition). This is explicit in Table S1: List of journals with impact factor and claim assessment.

- University ranking: Similarly, please clarify which year(s) of university ranking data were used. Since rankings vary depending on the system (e.g., QS, Times, Shanghai), were the conclusions consistent across multiple ranking sources?

We used Shanghai Ranking’s 2010 Academic Ranking of World Universities as our ranking of university. Our binning of ranking in categories make the analysis less susceptible to changes in ranking system. We selected the Shanghai ranking as it primarily evaluate research output and awards (where Times also evaluate teaching, and QS also employer reputation), which we believe represent better the variable than may affect irreplaceability.

Reviewer #3 (Recommendations for the authors):

Table S4 - for leading author there is a variable of 'historical lab after 1998 continuity' - should that be 1995?

Correct, we changed this label to Trained in Historical laboratory (Comparison restricted to claims published after 1995) to make it more explicit.

This is interesting to me because it shows how bots are not automatically "bad" or "good" as their actions are dependent on how they are operated. With the example of the Gender Pay Gap Bot, it holds companies accountable by using actual databases instead of spreading misinformation. This makes me think of how we decide when to put criticism on bots.

I found this passage interesting because it explains how the way we view people can actually influence their behavior and opportunities. A label may seem small, but over time it can affect how a student is treated and how they view their own abilities. This made me think about how important it is for teachers to recognize each student’s potential instead of making assumptions based on labels or stereotypes. I wonder how schools can make sure that labels are used to support students rather than limit what they believe they can accomplish.

Author response:

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

eLife Assessment:

This important study reports a novel phenomenon of maternal growth during pregnancy that is independent of growth hormone (GH), adding a new dimension to maternal biology of reproduction. The evidence is convincing and supported by state-of-the-art methodologies conducted in mice and persuasive observations in humans with hereditary isolated GH deficiency. Revised discussion should focus on possible mechanisms, including the role of IGF2, and on directions for future research.

We thank the editors for these valuable suggestions. In response, we assessed hepatic Igf2 mRNA expression. As shown in Author response image 1, hepatic Igf2 mRNA expression was higher in Ghrhr^lit/lit mice but was not significantly affected by pregnancy. However, we recognize that IGF-2 is produced by multiple tissues, particularly at the maternal-fetal interface, as well as by other maternal tissues, exerting endocrine or paracrine effects. Therefore, we believe that hepatic Igf2 expression alone provides only a limited view of the potential contribution of IGF-2 to the maternal adaptations induced by pregnancy. For this reason, we chose not to include these data in the revised manuscript. Instead, we expanded the Discussion to address the potential role of IGF-2 in the observed phenotypes and to highlight important directions for future research, as suggested.

Author response image 1.

Public Reviews:

Reviewer #1 (Public review):

This work evaluates the impact of reproductive history on growth, body weight and body composition in mammals. In mice, somatic growth is stimulated by the first pregnancy while the second pregnancy increases body weight mainly by increasing adiposity. To probe the role of pituitary growth hormone (GH), the key regulator of somatic growth in these processes, was addressed by comparing the impact of reproduction on growth in normal ("wild type") and genetically GH-deficient females and by detailed characterization of the profile of fluctuations in circulating GH levels in both types of animals. Additional studies addressed the possible role of other endocrine pathways (ghrelin and estrogen) in the pregnancy-related growth. Surprisingly, reproduction-related growth was independent of GH, ghrelin and estrogen. To determine whether these results may apply ("translate") to human physiology, data on various parameters of somatic growth were collected from women with hereditary GH deficiency. The findings indicate that GH-independent stimulation of growth by reproductive events also occurs in women.

Use of multiple animal models, rigorous characterization of GH levels in normal and GH-deficient females, and inclusion of data derived from a unique and well-characterised population of people with hereditary isolated GH deficiency and no GH replacement therapy are important strengths of these elegant and innovative studies. The results address a broader and clinically significant issue of permanent changes in body size, composition and function that result from pregnancy and lactation. This work also provides important background for further studies aimed at the identification of the mechanism involved and the role of specific reproductive events in the regulation of growth.

We sincerely thank the reviewer for this thoughtful and highly positive evaluation of our work and for recognizing its novelty, rigor, and potential physiological and clinical significance.

Reviewer #2 (Public review):

This manuscript describes the fascinating phenomenon of growth hormone (GH)-independent growth occurring in the mother during pregnancy. This growth was most pronounced in dwarf mice that are lacking the receptor for growth hormone-releasing hormone (GHRH) and therefore showing isolated GH deficiency. However, the pregnancy-induced growth could also be observed in wild-type mice, suggesting that it is a normal part of the maternal adaptation to pregnancy. The study falls short of identifying the mechanism(s) driving this pregnancy-induced growth response, but it certainly reveals a novel insight into maternal physiology. The authors have completed a range of experiments in mice to prove that, as well as being GH independent, the pregnancy-induced growth also did not require GH signaling in the liver (i.e. not another pregnancy-specific ligand operating through the GHR to promote IGF). They also provided complementary data from a population of humans with untreated isolated GH deficiency that are broadly consistent with the hypothesis. While it is important to consider the significant species differences between rodents and humans, both in terms of growth physiology and also in terms of evolution of placental somato-mammotrophic hormones, this unique population are a valuable resource and adds credence to the study. Overall, I find this a compelling research story, but disappointingly unfinished. There are some areas where additional information could improve the ability to interpret the data, and some additional concepts that could be considered in the discussion. There are also areas where additional experiments might provide important insights. However, I think that such suggestions can be considered as appropriate for future research, rather than delaying consideration of the current manuscript.

Main comments:

(1) Data in Figure 1 are remarkable - not so much the growth in pregnancy in the wildtype mice, because while elevated GH is well known in pregnancy, but growth in the dwarf mice is indicative of GH-independent growth. From these data, it seems that there is good evidence that growth in pregnancy is an adaptive function. However, it is possible that growth is achieved in dwarf mice and that in wildtype mice may have been mediated through different mechanisms. The dwarf mice showed an increase in liver and plasma IGF1, suggestive of an additional ligand driving IGF in pregnancy. One could hypothesize that such an effect could be mediated by an additional pregnancy-specific ligand activating the GH receptor. In humans, placental growth hormone could be such a ligand, but as far as we know, there is no placental GH in mice. In contrast, the wildtype animals showed suppression of liver and circulating IGF1, and low levels of pSTAT5 in the liver during pregnancy. These data (in Figure 5) are very surprising. Given the high circulating GH in pregnancy, as well as high placental lactogen (which would be expected to activate STAT5 in the liver through the Prlr), the low levels of pSTAT5 are unexpected and would seem to indicate some sort of acquired insensitivity to GH. Is this entirely driven by down-regulation of STAT5b protein, or could there be activation of other, negative regulators of STAT signalling, such as SOCS? What is causing such a profound suppression of STAT5? Regardless of the mechanism, this suggests that pregnancy-induced growth in wildtype mice is independent of circulating IGF1 (potentially a different mechanism or in addition to that seen in IGHD mice).

We thank the reviewer for this insightful comment. The mechanisms underlying the reduced hepatic STAT5b protein expression observed during pregnancy remain unknown. Previous studies have also reported desensitization of hepatic JAK2/STAT5 GH signaling during pregnancy, associated with increased expression of negative regulators of STAT signaling, including CIS (Miquet et al., Am J Physiol Endocrinol Metab 289–E607, 2005). In the current manuscript, we also observed increased Cish mRNA expression in the liver of pregnant mice. We have incorporated this information into the revised manuscript. In addition, we expanded the Discussion to acknowledge the possibility that pregnancy-induced growth may occur through distinct mechanisms in wild-type and GH-deficient mice and that, in wild-type mice, this response may involve liver-derived IGF-1-independent mechanisms.

The data shown in Figure 6 are a major strength of the study, showing that the pregnancy-induced changes are not specific to one particular transgenic model, but still occur in a variety of models affecting GH through different approaches. Given the pregnancy-specific nature of the changes, however, it seems an oversight not to have evaluated the role of placental lactogens. Prlr is highly expressed in the liver, but the function of this hormone in the liver is not well established. Could the extremely high levels of PL be mediating this growth response? Given the low expression of STAT5 in the liver and the fact that plasma IGF1 is not markedly elevated, it seems more likely that this growth response may be mediated by locally produced IGF1 in target tissues.

We thank the reviewer for this important suggestion. Although we were not able to investigate the role of prolactin receptor signaling using mouse models in the present study, we agree that prolactin may contribute to pregnancy-induced growth. Accordingly, we revised the Discussion to acknowledge this possibility and to include the potential roles of placental lactogens and locally produced IGF-1 as additional mechanisms that may underlie pregnancy-induced body growth.

I think these possibilities could be addressed by an expanded discussion of species variation in placental hormones, to highlight that humans have expansion of the GH locus, but rodents have expansion of the prolactin axis (see Soares, M. J. The prolactin and growth hormone families: pregnancy-specific hormones/cytokines at the maternal-fetal interface. Reprod Biol Endocrinol 2, 51, 2004). Importantly, placental GH and chorionic somatomammotropins (CSM) in humans are all variants of the GH gene, but CSM have preferential activity at Prlr. This seems to be a fundamental species difference in pregnancy biology, but has been interpreted as an example of convergent evolution, with conservation of prolactin and GH-like functions at the maternal-fetal interface, mediated by different mechanisms, likely contributing to the metabolic adaptations of the mother (see Newbern D, Freemark M. Placental hormones and the control of maternal metabolism and fetal growth. Curr Opin Endocrinol Diabetes Obes. 2011; 18: 409-416). While the preceding function has focused on explaining the evolution of placental lactogens (either prolactin or GH variants), the present data suggest that there are also mechanisms to maintain growth in pregnancy, independent of GH (even in the absence of a placental GH).

Thank you very much for this observation and suggestion. In the Introduction, we succinctly mention species-specific differences in the GH locus (see Introduction). Since our study focused primarily on mice, we believe expanding on this information would detract from the study's focus, especially given that such details are available in other publications. However, we have added a sentence to the discussion noting that, despite significant species-specific differences in the GH locus, there has been evolutionary conservation in the maintenance of pregnancy-induced growth, potentially involving distinct mechanisms in rodents and humans, though both appear to be GH-independent.

“However, important differences are observed between humans and rodents. Humans, but not rodents, possess the GH2 gene, which encodes the placental growth hormone (GH) variant, whose production progressively replaces pituitary GH (derived from the GH1 gene) secretion during pregnancy (Liao et al., 2018). In contrast, rodents maintain pituitary GH secretion throughout gestation (Gatford et al., 2017; Liao et al., 2018). Additionally, human GH, both pituitary and placental variants, as well as chorionic somatomammotropins, can activate both the GH receptor (GHR) and the prolactin receptor (PrlR), explaining their lactogenic effects. In contrast, murine GH activates only the GHR (Bartke and Kopchick, 2015).”

(2) The human data are very interesting, and my initial impression was that it seemed unlikely to be the same phenomenon. Was there any real evidence for "growth" in pregnancy? Pubertal maturation of long bone growth might be expected to prevent further growth in adulthood. However, these issues were appropriately discussed, and it seems well justified to evaluate this unique population of women with IGHD who underwent pregnancy. It would be very interesting to know if these women experienced elevated IGF1 during pregnancy, indicative of placental GH contributing to growth. Mechanistically, this might be more like the dwarf mouse situation of IGHD, that the situation in wildtype mice (associated with liver insensitivity to GH and low IGF1).

We thank the reviewer for this comment. Unfortunately, the pregnancies of the women with IGHD occurred with limited medical assistance, and no additional clinical information is available, particularly regarding changes in circulating IGF-1 levels during pregnancy. Therefore, the evidence presented and discussed in the current manuscript represents the only information currently available on pregnancy-induced growth in this unique population.

(3) It would be useful to include investigations that isolate the effects of pregnancy and the placental hormones. Such studies could include evaluating growth in pseudopregnant mice with IGHD (pregnancy-like changes in hormones but lacking the placental contribution) and in IGHD animals that experience pregnancy but not lactation (pups removed at birth). I accept that this might be too large an additional study to add for the present manuscript.

We thank the reviewer for this valuable suggestion and agree that this experiment could provide valuable information regarding the role of placental hormones in pregnancy-induced growth. Interestingly, previous work has shown that female mice housed with vasectomized males exhibit increased body weight compared with non-reproductive females, although this increase is substantially smaller than that observed in females with successive litters (Garratt et al., Proc Natl Acad Sci U S A 117:15748–15754, 2020). We discuss this study in the current manuscript. However, this study did not provide additional information on whether this increase reflects greater adiposity, enhanced body growth, or both. Unfortunately, we are unable to perform these time-intensive experiments. We appreciate the reviewer's understanding and agree that this important question should be addressed in future studies.

(4) It is an important and translationally relevant observation that pregnancy increased the risk of long-term weight gain, and that after the first pregnancy, the pregnancy-induced growth response was more directed to promoting fat deposition. Does this provide any mechanistic insight? Could a metabolic adaptation result in growth?

We thank the reviewer for this thoughtful comment. At present, we do not have additional data to explain the mechanisms underlying the pregnancy-induced increases in body growth and adiposity or to determine whether these processes are mechanistically linked. In the revised manuscript, we have expanded the Discussion to address potential mechanisms that may contribute to the observed post-pregnancy growth, including hormonal and metabolic factors, while acknowledging that these possibilities remain speculative and require further investigation.

Reviewer #3 (Public review):

Summary:

The study describes an increase in body growth and body composition in both mice and women. In mice, the impact on growth is mainly seen during the first pregnancy, and the changes postpartum on body composition are also different during the first and second pregnancies. The study has used various knock-out models in the growth hormone axis to understand these changes as well as some gene expression analysis related to GH, IGF-1 and estrogen signalling pathways.

Strengths:

(1) The inclusion of various knock-out mouse models that allow for exploration of mechanisms related to the above-mentioned changes.

(2) The investigation of gene expression of GHR, IGF-1R and ER pathways.

Weaknesses:

The human findings are dependent on the patient's recollection of bodily changes after their pregnancies.

Conclusion:

The authors have partly achieved their aim of describing changes in growth and body composition that remain after pregnancy and the mechanisms behind these changes. This study may have importance for a wide variety of research areas as well as in the clinical setting. The study is also unique in its attempt to bridge findings in mice to a unique human model of congenital GH deficiency.

We sincerely thank the reviewer for the thoughtful evaluation of our study, for recognizing its novelty and potential significance, and for highlighting the strengths of our experimental approach. We have revised the manuscript to further acknowledge the limitations of the human data, as suggested.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

The findings presented in this study are novel, exciting and important. I believe it would help the readers to include a diagram showing the timing of the various measurements and tissue collection in relation to conception, parturition and weaning. It would also be helpful to expand the discussion to include the author's thoughts on the possible role of various placental hormones, pituitary prolactin, metabolic changes and/or other factors in the observed growth. Finally, humans from whom the data were obtained should probably be referred to as individuals or subjects rather than patients.

We thank the reviewer for these helpful suggestions. We included Figure 7 in the revised manuscript, which summarizes the study's experimental timeline. Additionally, we expanded the Discussion as recommended and replaced the term "patients" with "subjects" throughout the manuscript.

Reviewer #2 (Recommendations for the authors):

In addition to my comment above about addressing the different evolution of placental hormones, the following minor suggestions are provided:

(1) Abstract line 23 "most" could be "some" (because lots of evidence that pregnancy-induced adaptations are long-term - e.g. brain structure, maternal behavior, endocrine changes) - see below.

Done.

(2) Is "reproductive experience" the best term? Or is it "pregnancy"? (likely specifically due to the presence of placental hormones and/or maternal patterns of hormones, rather than other aspects of "reproductive experience) e.g. mating, parturition or lactation?

We appreciate the reviewer's point. However, because we cannot exclude potential contributions of mating, parturition, or lactation to the observed increases in body growth and adiposity, we prefer to retain the term "reproductive experience," as the mice in the present study underwent all of these processes rather than pregnancy alone.

(3) Potentially, the introduction could add references to brain changes in humans in pregnancy (this is a particularly topical area of research where long-term changes have been reported; e.g. Pritschet L, Taylor CM, Cossio D, Faskowitz J, Santander T, Handwerker DA, Grotzinger H, Layher E, Chrastil ER, Jacobs EG. Neuroanatomical changes observed over the course of a human pregnancy. Nat Neurosci. 2024 Nov;27(11):2253-2260; Martínez-García M, Paternina-Die M, Barba-Müller E, Martín de Blas D, Beumala L, Cortizo R, Pozzobon C, Marcos-Vidal L, Fernández-Pena A, Picado M, Belmonte-Padilla E, Massó-Rodriguez A, Ballesteros A, Desco M, Vilarroya Ó, Hoekzema E, Carmona S. Do Pregnancy-Induced Brain Changes Reverse? The Brain of a Mother Six Years after Parturition. Brain Sci. 2021 Jan 28;11(2):168. There is also a significant literature on long-term effects of reproductive experience (Bridges RS. Long-term alterations in neural and endocrine processes induced by motherhood in mammals. Horm Behav. 2016 Jan;77:193-203).

We thank the reviewer for this helpful suggestion. Accordingly, we incorporated these references into the Introduction to further emphasize the long-term effects of reproductive experience.

(4) Figure 1: Why show body weight as a "delta" for primiparous animals, and "absolute "values for multiparous? Similarly, it seems that body length is an informative readout for these experiments, but this is only reported for one model, and most models are only shown as body weight and lean mass.

We thank the reviewer for this comment. For the primiparous mice, we chose to present the change (Δ) in body weight and lean mass because it more directly illustrates the effects of the first reproductive experience relative to each animal's baseline while avoiding redundant presentation of both absolute and Δ values, as both analyses yielded the same statistical conclusions. For the multiparous mice, absolute values were presented to facilitate comparison with the corresponding images and to allow direct comparison of body size between wild-type and Ghrhr^lit/lit mice. Regarding body length, these measurements were collected only in the multiparous cohort and were not obtained after the first reproductive experience. Therefore, we are unable to provide body length data for the primiparous groups.

(5) It seems it would be better to present all of the mouse data first, then the supporting human data.

Done.

(6) The manuscript includes a high-quality investigation of GH secretion - particularly the pulsatile secretion of GH. Is it possible to have matching IGF data (at least multiple time points in pregnancy)?

We agree with the reviewer that serial measurements of circulating IGF-1 during pregnancy would provide valuable additional information. Unfortunately, this analysis is not feasible because the limited blood volume collected during the study did not allow sufficient sample storage for additional measurements.

(7) Line 221 - "GHRH signaling is required for pregnancy-induced increases in GH secretion...". Can you actually make that conclusion, or is it possible that the lack of GHRH developmentally has permanently altered the pituitary gland, so it cannot respond to other GH secretagogues?

We thank the reviewer for this important comment. We agree that the congenital absence of GHRH signaling may cause developmental alterations in the pituitary that impair the response to other GH secretagogues. Therefore, we cannot distinguish whether the lack of pregnancy-induced increases in GH secretion reflects the absence of GHRH signaling per se or the developmental defects resulting from GHRH deficiency. We removed the aforementioned phrase from Results and have revised the Discussion to acknowledge this important limitation and to clarify that the observed phenotype may be secondary to impaired pituitary development.

(8) Line 238 - "GHR signaling stimulates hepatic insulin-like growth factor 1 (IGF-1) secretion, particularly by activating the signal transducer and activator of transcription 5b (STAT5b) pathway" for this point, should probably cite: Davey HW, Xie T, McLachlan MJ, Wilkins RJ, Waxman DJ, Grattan DR. STAT5b is required for GH-induced liver IGF-I gene expression. Endocrinology. 2001 Sep;142(9):3836-41.

Thank you for this suggestion; we added this reference.

(9) Line 240 - "GH action in the liver is not only controlled by the pattern of GH secretion...". should probably cite Waxman's work regarding patterns of GH secretion (e.g reviewed in Waxman DJ, O'Connor C. Growth hormone regulation of sex-dependent liver gene expression. Mol Endocrinol. 2006 Nov;20(11):2613-29.).

This reference was included in this sentence.

(10) Methods: Check statistics - some of the analysis should have been repeated measures?

We thank the reviewer for this comment. We carefully re-evaluated all statistical analyses and did not identify any experiment for which a repeated-measures analysis would have been appropriate. Therefore, no changes to the statistical analyses were necessary.

Reviewer #3 (Recommendations for the authors):

(1) Introduction: The context of the sentence "Furthermore, historically, females have been underrepresented in studies" is unclear.

We thank the reviewer for this observation. Our intention was to emphasize that, because pregnancy is unique to females and females have historically been underrepresented in biomedical research, pregnancy-related physiology has received comparatively less attention. However, we agree that this statement was not essential in this context. Thus, we have removed it from the revised manuscript.

(2) Introduction: Based on the paper, the main aim seems to be to study the lasting effects of pregnancy on the mother and not primarily to study the hormonal changes during pregnancy.

We thank the reviewer for this helpful observation. We agree that our study primarily focuses on the long-term effects of pregnancy on the maternal organism rather than the hormonal changes that occur during pregnancy. Accordingly, we revised this sentence to better reflect the main objective of the study: “Therefore, the goal of this study is to investigate the lasting effects of pregnancy on the maternal organism and the possible involvement of the somatotrophic axis in these changes.”

(3) Other endocrine factors could affect the changes seen after pregnancy in mice and humans, such as the insulin level and activation of the IR.

We thank the reviewer for this valuable suggestion. In the revised manuscript, we expanded the Discussion to acknowledge the potential contribution of several endocrine factors, including insulin signaling, to pregnancy-induced growth.

(4) The receptor activation in tissues other than the liver has not been studied, such as in the growth plate, adipose tissue and muscle.

We thank the reviewer for this important comment. We agree with this point and have addressed this possibility in the revised Discussion.

(5) Information on the age of the patient at the time of pregnancy could be included as well as the patient's height and weight before pregnancy and at follow-up.

This information was added as Table 1.

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.

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.

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.

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.

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.

I think social media has its pros and cons. If we want to enjoy its convenience and entertainment, we also need to recognize that not every risk can be eliminated. Developers cannot predict every harmful use, but they should keep improving safeguards to prevent known problems from that harm to be spread. Still, some damage to privacy or reputation may be irreversible by the time they respond. However, I don’t think all the responsibility should fall on developers. People who use technology to harm others should also be held accountable. Even strong safety measures cannot prevent every robbery or murder in the society we lived in , and online spaces face a similar problem. We need to learn how to navigate online risks, just as we do in reallife, while still expecting developers to address foreseeable harms.

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.

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.

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.