Author Response

We thank all three Reviewers and the editors for the time and effort they put in reading and critiquing the manuscript. Our revised manuscript includes new data and analyses that address the original concerns. These include, 1) a new Supplemental Figure characterizing Cre expression and cellular phenotypes in the hippocampus, 2) new tables that give a more comprehensive picture of the EEG recordings and statistical analyses, 3) addition of whole cell electrophysiology data, and 4) rewriting to ensure that we do not state that either mTORC1 or mTORC2 hyperactivation is sufficient to cause epilepsy. We discuss the issue of statistical power to detect reduction in generalized seizure rate in the responses below. These suggestions and additions have improved the paper and we hope they will raise both significance and strength of support for the conclusions.

Reviewer #1 (Public Review):

Hyperactivation of mTOR signaling causes epilepsy. It has long been assumed that this occurs through overactivation of mTORC1, since treatment with the mTORC1 inhibitor rapamycin suppresses seizures in multiple animal models. However, the recent finding that genetic inhibition of mTORC1 via Raptor deletion did not stop seizures while inhibition of mTORC2 did, challenged this view (Chen et al, Nat Med, 2019). In the present study, the authors tested whether mTORC1 or mTORC2 inhibition alone was sufficient to block the disease phenotypes in a model of somatic Pten loss-of-function (a negative regulator of mTOR). They found that inactivation of either mTORC1 or mTORC2 alone normalized brain pathology but did not prevent seizures, whereas dual inactivation of mTORC1 and mTORC2 prevented seizures. As the functions of mTORC1 versus mTORC2 in epilepsy remain unclear, this study provides important insight into the roles of mTORC1 and mTORC2 in epilepsy caused by Pten loss and adds to the emerging body of evidence supporting a role for both complexes in the disease development.

Strengths:

The animal models and the experimental design employed in this study allow for a direct comparison between the effects of mTORC1, mTORC2, and mTORC1/mTORC2 inactivation (i.e., same animal background, same strategy and timing of gene inactivation, same brain region, etc.). Additionally, the conclusions on brain epileptic activity are supported by analysis of multiple EEG parameters, including seizure frequencies, sharp wave discharges, interictal spiking, and total power analyses.

Weaknesses:

(1) The sample size of the study is small and does not allow for the assessment of whether mTORC1 or mTORC2 inactivation reduces seizure frequency or incidence. This is a limitation of the study.

We agree that this is a minor limitation of the present study, however, for several reasons we decided not to pursue this question by increasing the number of animals. First, we performed a power analysis of the existing data. This analysis showed that we would need to use 89 animals per group to detect a significant difference (0.8 Power, p= 0.05, Mann-Whitney test) in the frequency of generalized seizures in the Pten-Raptor group and 31 animals per group in the Pten-Rictor group versus Pten alone. It is simply not feasible to perform video-EEG monitoring on this many animals for a single study. Second, even if we did do enough experiments to detect a reduction in seizure frequency, it is clear that neither Rptor nor Rictor deletion provides the kind normalization in brain activity that we seek in a targeted treatment. Both Pten-Rptor and Pten-Rictor animals still have very frequent spike-wave events (Fig. 3D) and highly abnormal interictal EEGs (Fig. 4), suggesting that even if generalized seizures were reduced, epileptic brain activity persists. This is in contrast to the triple KO animals, which have no increase in SWD above control level and very normal interictal EEG.

(2) The authors describe that they inactivated mTORC1 and mTORC2 in a new model of somatic Pten loss-of-function in the cortex. This is slightly misleading since Cre expression was found both in the cortex and the underlying hippocampus, as shown in Figure 1. Throughout the manuscript, they provide supporting histological data from the cortex. However, since Pten loss-of-function in the hippocampus can lead to hippocampal overgrowth and seizures, data showing the impact of the genetic rescue in the hippocampus would further strengthen the claim that neither mTORC1 nor mTORC2 inactivation prevents seizures.

Thank you for pointing out this issue. Cre expression was observed in both the cortex and the dorsal hippocampus in most animals, and we agree that differences in cortical versus hippocampal mTOR signaling could have differential contributions to epilepsy. We initially focused our studies on the cortex because spike-and-wave discharge, the most frequent and fully penetrant EEG phenotype in our model, is associated with cortical dysfunction. In our revised submission we have included a new Figure that quantifies Cre expression in the hippocampal subfields, as well as pS6, pAkt and soma size. These new data show that the amount of Cre expression in the hippocampus is not related to the occurrence of generalized seizures. The pattern of cell size changes in hippocampal neurons is the same as observed in cortical neurons. The levels of pS6 and pAkt are not much changed in the hippocampus, likely due to the sparse Cre expression there. We interpret these findings as supporting the conclusion that the reason we do not see seizure prevention by mTORC1 or mTORC2 inactivation is not due to hippocampal-specific dysfunction.

(3)Some of the methods for the EEG seizure analysis are unclear. The authors describe that for control and Pten-Raptor-Rictor LOF animals, all 10-second epochs in which signal amplitude exceeded 400 μV at two time-points at least 1 second apart were manually reviewed, whereas, for the Pten LOF, Pten-Raptor LOF, and Pten-Rictor LOF animals, at least 100 of the highest- amplitude traces were manually reviewed. Does this mean that not all flagged epochs were reviewed? This could potentially lead to missed seizures.

We reviewed at least 48 hours of data from each animal manually. All seizures that were identified during manual review were also identified by the automated detection program. It is possible but unlikely that there are missed seizures in the remaining data. We have added these details to the Methods of the revised submission.

(4) Additionally, the inclusion of how many consecutive hours were recorded among the ~150 hours of recording per animal would help readers with the interpretation of the data.

Thank you for this recommendation. Our revised submission includes a table with more information about the EEG recordings in the revised version of the manuscript. The number of consecutive hours recorded varied because the wireless system depends on battery life, which was inconsistent, but each animal was recorded for at least 48 consecutive hours on at least two occasions.

(5) Finally, it is surprising that mTORC2 inactivation completely rescued cortical thickness since such pathological phenotypes are thought to be conserved down the mTORC1 pathway. Additional comments on these findings in the Discussion would be interesting and useful to the readers.

We agree that the relationship between mTORC2, cortical thickness, and growth in general is an interesting topic with conflicting results in the literature. We didn’t add anything to the Discussion along these lines because we are up against word limits, but comment here that soma size was increased 120% by Pten inactivation and partially normalized to a 60% increase from Controls by mTORC2 inactivation (Fig. 2C). We and others have previously shown that mTORC2 inactivation (Rictor deletion) in neurons reduces brain size, neuron soma size, and dendritic outgrowth (PMIDs: 36526374, 32125271, 23569215). In our revised submission we also include new data showing that the membrane capacitance of Pten-Ric LOF neurons is normal. Thus, we do not find it completely surprising that mTORC2 inactivation reduces the cortical thickness increase caused by Pten loss. There may still be a slight increase in cortical thickness in Pten-Rictor animals, but it is statistically indistinguishable from Controls.

Reviewer #2 (Public Review):

Summary:

The study by Cullen et al presents intriguing data regarding the contribution of mTOR complex 1 (mTORC1) versus mTORC2 or both in Pten-null-induced macrocephaly and epileptiform activity. The role of mTORC2 in mTORopathies, and in particular Pten loss-off-function (LOF)-induced pathology and seizures, is understudied and controversial. In addition, recent data provided evidence against the role of mTORC1 in PtenLOF-induced seizures. To address these controversies and the contribution of these mTOR complexes in PtenLOF-induced pathology and seizures, the authors injected a AAV9-Cre into the cortex of conditional single, double, and triple transgenic mice at postnatal day 0 to remove Pten, Pten+Raptor or Rictor, and Pten+raptor+rictor. Raptor and Rictor are essentially binding partners of mTORC1 and mTORC2, respectively. One major finding is that despite preventing mild macrocephaly and increased cell size, Raptor knockout (KO, decreased mTORC1 activity) did not prevent the occurrence of seizures and the rate of SWD event, and aggravated seizure duration. Similarly, Rictor KO (decreased mTORC2 activity) partially prevented mild macrocephaly and increased cell size but did not prevent the occurrence of seizures and did not affect seizure duration. However, Rictor KO reduced the rate of SWD events. Finally, the pathology and seizure/SWD activity were fully prevented in the double KO. These data suggest the contribution of both increased mTORC1 and mTORC2 in the pathology and epileptic activity of Pten LOF mice, emphasizing the importance of blocking both complexes for seizure treatment. Whether these data apply to other mTORopathies due to Tsc1, Tsc2, mTOR, AKT or other gene variants remains to be examined.

Strengths:

The strengths are as follows: 1) they address an important and controversial question that has clinical application, 2) the study uses a reliable and relatively easy method to KO specific genes in cortical neurons, based on AAV9 injections in pups. 2) they perform careful video-EEG analyses correlated with some aspects of cellular pathology.

Weaknesses:

The study has nevertheless a few weaknesses: 1) the conclusions are perhaps a bit overstated. The data do not show that increased mTORC1 or mTORC2 are sufficient to cause epilepsy. However the data clearly show that both increased mTORC1 and mTORC2 activity contribute to the pathology and seizure activity and as such are necessary for seizures to occur.

We agree that our findings do not directly show that either mTORC1 or mTORC2 hyperactivity are sufficient to cause seizures, as we do not individually hyperactivate each complex in the absence of any other manipulation. We interpreted our findings in this model as suggesting that either is sufficient based on the result that there is no epileptic activity when both are inactivated, and thus assume that there is not a third, mTOR-independent, mechanism that is contributing to epilepsy in Pten, Pten-Raptor, and Pten-Rictor animals. In addition, the histological data show that Raptor and Rictor loss each normalize activity through mTORC1 and mTORC2 respectively, suggesting that one in the absence of the other is sufficient. However, we agree that there could be other potential mTOR-independent pathways downstream of Pten loss that contribute to epilepsy. We have revised the manuscript to reflect this.

(2) The data related to the EEG would benefit from having more mice. Adding more mice would have helped determine whether there was a decrease in seizure activity with the Rictor or Raptor KO.

Please see response to Reviewer 1’s first Weakness.

(3) It would have been interesting to examine the impact of mTORC2 and mTORC1 overexpression related to point #1 above.

We are not sure that overexpression of individual components of mTORC1 or mTORC2 would result in their hyperactivation or lead to increases in downstream signaling. We believe that cleanly and directly hyperactivating mTORC1 or especially mTORC2 in vivo without affecting the other complex or other potential interacting pathways is a difficult task. Previous studies have used mTOR gain-of-function mutations as a means to selectively activate mTORC1 or pharmacological agents to selectively activate mTORC2, but it not clear to us that the former does not affect mTORC2 activity as well, or that the latter achieves activation of mTORC2 targets other than p-Akt 473, or that it is truly selective. We agree that these would be key experiments to further test the sufficiency hypothesis, but that the amount of work that would be required to perform them is more that what we can do in this Short Report.

Reviewer #3 (Public Review):

Summary: This study investigated the role of mTORC1 and 2 in a mouse model of developmental epilepsy which simulates epilepsy in cortical malformations. Given activation of genes such as PTEN activates TORC1, and this is considered to be excessive in cortical malformations, the authors asked whether inactivating mTORC1 and 2 would ameliorate the seizures and malformation in the mouse model. The work is highly significant because a new mouse model is used where Raptor and Rictor, which regulate mTORC1 and 2 respectively, were inactivated in one hemisphere of the cortex. The work is also significant because the deletion of both Raptor and Rictor improved the epilepsy and malformation. In the mouse model, the seizures were generalized or there were spike-wave discharges (SWD). They also examined the interictal EEG. The malformation was manifested by increased cortical thickness and soma size.

Strengths: The presentation and writing are strong. The quality of data is strong. The data support the conclusions for the most part. The results are significant: Generalized seizures and SWDs were reduced when both Torc1 and 2 were inactivated but not when one was inactivated.

Weaknesses: One of the limitations is that it is not clear whether the area of cortex where Raptor or Rictor were affected was the same in each animal.

Our revised submission includes new data showing that the area of affected cortex and hippocampus are similar across groups. (Figure 1A and Supplementary Figure 1)

Also, it is not clear which cortical cells were measured for soma size.

Soma size was measured by dividing Nissl stain images into a 10 mm2 grid. The somas of all GFP-expressing cells fully within three randomly selected grid squares in Layer II/III were manually traced. Three sections per animal at approximately Bregma -1.6, -2,1, and -2.6 were used. As Cre expression was driven by the hSyn promoter these cells include both excitatory and inhibitory cortical neurons.

Another limitation is that the hippocampus was affected as well as the cortex. One does not know the role of cortex vs. hippocampus. Any discussion about that would be good to add.

See response to Reviewer 1’s second Weakness.

It would also be useful to know if Raptor and Rictor are in glia, blood vessels, etc.

Raptor and Rictor are thought to be ubiquitously active in mammalian cells including glia and endothelial cells. Previous studies have shown that mTOR manipulation can affect astrocyte function and blood vessel organization, however, our study induced gene knockout using an AAV that expressed Cre under control of the hSyn promoter, which has previously been shown to be selective for neurons. Manual assessment of Cre expression compared with DAPI, NeuN, and GFAP stains suggested that only neurons were affected.

Recommendations for the authors: please note that you control which revisions to undertake from the public reviews and recommendations for the authors

Reviewer #1 (Recommendations For The Authors):

In addition to the comments in the public review, it is recommended that the authors provide a more representative figure for p-Akt staining in the Pten LOF condition in Figure 1 D2. The current figure is not convincing.

Thanks for the suggestion. We have replaced the images with zoomed in panels that beter demonstrate the difference.

Additionally, in the last paragraph of the discussion, there is a reference error to an incorrect paper (reference 18) that should be corrected.

Thanks, corrected.

Reviewer #2 (Recommendations For The Authors):

Major comments:

Comment 1: Some statements need clarifications or changes.

(1) Abstract: "spontaneous seizures and epileptiform activity persisted despite mTORC1 or mTORC2 inactivation alone but inactivating both mTORC1 and mTORC2 normalized pathology." Did inactivation of one only also normalized the pathology? Did inactivating both normalized the seizures? Pathology is not equal to seizures.

We have altered this statement to avoid ambiguity.

(2) Abstract: "These results suggest that hyperactivity of both mTORC1 and mTORC2 are sufficient to cause epilepsy,". Based on the abstract, it is not clear that it is sufficient. It is necessary.

We have altered this statement by removing the term “sufficient.”

(3) "Thus, there is strong evidence that hyperactivation of mTORC1 downstream of PTEN disruption causes the macrocephaly, epilepsy, early mortality, and synaptic dysregulation observed in humans and model organisms [17]" I would suggest adding that the strongest evidence is that mTOR GOF mutations lead to the same pathology and epilepsy, suggesting mTORC1 is sufficient. The other findings suggest that it is necessary.

Unless we misunderstand the Reviewer’s point, we believe this viewpoint is already encompassed by the proceeding text that “These phenotypes resemble those observed in models of mTORC1- specific hyperactivation.”

(4) Introduction (end): "suggesting that hyperactivity of either complex can lead to neuronal hyperexcitability and epilepsy".

Comment 2: I do not agree with the title based on comment 1 above. You did not provide evidence that the mTORCs cause seizures. Your data suggest that they are necessary for seizures or contribute to seizures, but there is no evidence that mTORC2 can induce seizure.

We softened the title by replacing “cause” with “mediate.”

Comment 3: Fig. 1B. Could you beter describe the affected regions. I can see other regions than just the cortex and hippocampus.

Almost all affected cell bodies were in the cortex and hippocampus. The virus in the image is cell-filling and as such projections from affected neurons throughout the brain can also be seen. We have clarified this in the figure legend.

Comment 4: I feel unease about the number of animals recorded for EEG to assess seizure frequency. There is not enough power to draw clear conclusions. So, please make sure to not oversell your findings since it is all-or-nothing data (seizure or no seizure) in this case and the seizure frequency could very well be decreased with single mTOR LOF, but it is impossible to conclude. Maybe discuss this limitation of your study.

We have addressed this in the public comments response.

Minor:

(1) Pten LOF: define the abbreviation.

Done

(2) Make sure that gene name in mice are not capitalized and italicized.

OK

(3) Fig 1C: could you specify in the results where the analysis was done.

Detail added to Methods (to keep Results concise for word limit)

(4) In the subtitle: "Concurrent mTORC1/2 inactivation, but neither alone, rescues epilepsy and interictal EEG abnormalities in focal Pten LOF". Replace "rescues" but prevents. This is not a rescue experiment since the LOF is done at the same time.

OK

(5) "GS did not appear to be correlated with mTOR pathway activity (Supplementary Figure 2)." Please can you do proper correlation analysis, by plotting all the values as a function of seizure frequency independent of the condition? There is also no correlation between pAKt and seizures.

Here are those data in Author response image 1. They are now part of Supplementary Figure 2.

Author response image 1.

Reviewer #3 (Recommendations For The Authors):

Figures 1 D, and E show images that are too small to judge. Where are the layers? Please add marks.

We replaced these images with larger zoomed in images to show group differences more clearly. The images no longer show multiple differentiable cortical layers.

If Fig 1 characterizes the model, where is the seizure data? When did they start? Where did they start? Was the focus of the cortical area affected by PTEN loss of function?

Updated figure name to reflect content. Information about the seizure phenotypes is included in Figure 3.

Figure 2 The font size for the calibration is too small. The correlations are hard to see. Colors are not easy to discriminate.

We edited the figure to correct these problems.

Figure 3 shows a clear effect on generalized seizures but the text of the Results does not reflect that.

We wanted to be cautious about interpreting these data based on the issue raised by other reviewers that they are underpowered to detect seizure reduction in the Pten-Raptor and Pten-Rictor groups. We have updated the language to atempt to strike a beter balance between over- and under-interpretation. We also performed an additional analysis of the occurrence of generalized seizures to emphasize that only Control and PtRapRic animals have significantly lower seizure occurrence that Pten LOF mice (Fig 3C).

For interictal power, was the same behavioral state chosen? Was a particular band affected?

Epochs to be analyzed were selected automatically and were agnostic to behavioral state. Band-specific effects are outlined in Figure 4B and Table [2].

There is no information about whether the model exhibits altered sleep, food intake, weight, etc.

We didn’t collect information on food intake. It would be possible to look at sleep from the EEG, but that is not something that we are prepared to do at this point. Weight at endpoint was not different between genotypes but we did not collect longitudinal data on weight.

Were the sexes different?

Included in new Table [1]

Where were EEG electrodes and were they subdural or not?

Additional detail on this has been added to Methods. The screws are placed in the skull but above the dura.

How long were continuous EEG records- the method just says 150 hr. per mouse in total.

Included in new Table [1]

The statistics don't discuss power, normality, whether variance was checked to ensure it did not differ significantly between groups, or whether data are mean +- sem or sd. For ANOVAs, were there multifactorial comparisons and what were F, df, and p values? Exact p for post hoc tests?

We have added a new table (Table [3]) that gives information on the exact test used, F, p values, and exact p for post hoc tests. Information regarding power, normality, variance, post- tests and multiple comparisons corrections have been added to Methods section “Statistical Analysis.”

Author Response

Reviewer #1 (Public Review):

Summary:

Visual Perceptual Learning (VPL) results in varying degrees of generalization to tasks or stimuli not seen during training. The question of which stimulus or task features predict whether learning will transfer to a different perceptual task has long been central in the field of perceptual learning, with numerous theories proposed to address it. This paper introduces a novel framework for understanding generalization in VPL, focusing on the form invariants of the training stimulus. Contrary to a previously proposed theory that task difficulty predicts the extent of generalization - suggesting that more challenging tasks yield less transfer to other tasks or stimuli - this paper offers an alternative perspective. It introduces the concept of task invariants and investigates how the structural stability of these invariants affects VPL and its generalization. The study finds that tasks with high-stability invariants are learned more quickly. However, training with low-stability invariants leads to greater generalization to tasks with higher stability, but not the reverse. This indicates that, at least based on the experiments in this paper, an easier training task results in less generalization, challenging previous theories that focus on task difficulty (or precision). Instead, this paper posits that the structural stability of stimulus or task invariants is the key factor in explaining VPL generalization across different tasks

Strengths:

• The paper effectively demonstrates that the difficulty of a perceptual task does not necessarily correlate with its learning generalization to other tasks, challenging previous theories in the field of Visual Perceptual Learning. Instead, it proposes a significant and novel approach, suggesting that the form invariants of training stimuli are more reliable predictors of learning generalization. The results consistently bolster this theory, underlining the role of invariant stability in forecasting the extent of VPL generalization across different tasks.

• The experiments conducted in the study are thoughtfully designed and provide robust support for the central claim about the significance of form invariants in VPL generalization.

Weaknesses:

• The paper assumes a considerable familiarity with the Erlangen program and the definitions of invariants and their structural stability, potentially alienating readers who are not versed in these concepts. This assumption may hinder the understanding of the paper's theoretical rationale and the selection of stimuli for the experiments, particularly for those unfamiliar with the Erlangen program's application in psychophysics. A brief introduction to these key concepts would greatly enhance the paper's accessibility. The justification for the chosen stimuli and the design of the three experiments could be more thoroughly articulated.

Response: We appreciate the reviewer's feedback regarding the accessibility of our paper. In response to this feedback, we plan to enhance the introduction section of our paper to provide a concise yet comprehensive overview of the key concepts of Erlangen program. Additionally, we will provide a more thorough justification for the selection of stimuli and the experimental design in our revised version, ensuring that readers understand the rationale behind our choices.

• The paper does not clearly articulate how its proposed theory can be integrated with existing observations in the field of VPL. While it acknowledges previous theories on VPL generalization, the paper falls short in explaining how its framework might apply to classical tasks and stimuli that have been widely used in the VPL literature, such as orientation or motion discrimination with Gabors, vernier acuity, etc. It also does not provide insight into the application of this framework to more naturalistic tasks or stimuli. If the stability of invariants is a key factor in predicting a task's generalization potential, the paper should elucidate how to define the stability of new stimuli or tasks. This issue ties back to the earlier mentioned weakness: namely, the absence of a clear explanation of the Erlangen program and its relevant concepts.

Response: Thanks for highlighting the need for better integration of our proposed theory with existing observations in the field of VPL. Unfortunately, the theoretical framework proposed in our study is based on the Klein’s Erlangen program and is only applicable to geometric shape stimuli. For VPL studies using stimuli and paradigms that are completely unrelated to geometric transformations (such as motion discrimination with Gabors or random dots, vernier acuity, spatial frequency discrimination, contrast detection or discrimination, etc.), our proposed theory does not apply. Some stimuli employed by VPL studies can be classified into certain geometric invariants. For instance, orientation discrimination with Gabors (Dosher & Lu, 2005) and texture discrimination task (F. Wang et al., 2016) both belong to tasks involving Euclidean invariants, and circle versus square discrimination (Kraft et al., 2010) belongs to tasks involving affine invariance. However, these studies do not simultaneously involve multiple geometric invariants of varying levels stability, and thus cannot be directly compared with our research. It is worth noting that while the Klein’s hierarchy of geometries, which our study focuses on, is rarely mentioned in the field of VPL, it does have connections with concepts such as 'global/local', 'coarse/fine', 'easy/difficulty', 'complex/simple': more stable invariants are closer to 'global', 'coarse', 'easy', 'complex', while less stable invariants are closer to 'local', 'fine', 'difficulty', 'simple'. Importantly, several VPL studies have found ‘fine-to-coarse’ or ‘local-to-global’ asymmetric transfer (Chang et al., 2014; N. Chen et al., 2016; Dosher & Lu, 2005), which seems consistent with the results of our study.

In the introduction section of our revised version and subsequent full author response, we will provide a clear explanation of the Erlangen program and elucidate how to define the stability of new stimuli or tasks. In the discussion section of our revised version, we will compare our results to other studies concerned with the generalization of perceptual learning and speculate on how our proposed theory fit with existing observations in the field of VPL.

• The paper does not convincingly establish the necessity of its introduced concept of invariant stability for interpreting the presented data. For instance, consider an alternative explanation: performing in the collinearity task requires orientation invariance. Therefore, it's straightforward that learning the collinearity task doesn't aid in performing the other two tasks (parallelism and orientation), which do require orientation estimation. Interestingly, orientation invariance is more characteristic of higher visual areas, which, consistent with the Reverse Hierarchy Theory, are engaged more rapidly in learning compared to lower visual areas. This simpler explanation, grounded in established concepts of VPL and the tuning properties of neurons across the visual cortex, can account for the observed effects, at least in one scenario. This approach has previously been used/proposed to explain VPL generalization, as seen in (Chowdhury and DeAngelis, Neuron, 2008), (Liu and Pack, Neuron, 2017), and (Bakhtiari et al., JoV, 2020). The question then is: how does the concept of invariant stability provide additional insights beyond this simpler explanation?

Response: We appreciate the alternative explanation proposed by the reviewer and agree that it presents a valid perspective grounded in established concepts of VPL and neural tuning properties. However, performing in the collinearity and parallelism tasks both require orientation invariance. While utilizing the orientation invariance, as proposed by the reviewer, can explain the lack of transfer from collinearity or parallelism to orientation task, it cannot explain why collinearity does not transfer to parallelism.

As stated in the response to the previous review, in the revised discussion section, we will compare our study with other studies (including the three papers mentioned by the reviewer), aiming to clarify the necessity of the concept of invariant stability for interpreting the observed data and understanding the mechanisms underlying VPL generalization.

• While the paper discusses the transfer of learning between tasks with varying levels of invariant stability, the mechanism of this transfer within each invariant condition remains unclear. A more detailed analysis would involve keeping the invariant's stability constant while altering a feature of the stimulus in the test condition. For example, in the VPL literature, one of the primary methods for testing generalization is examining transfer to a new stimulus location. The paper does not address the expected outcomes of location transfer in relation to the stability of the invariant. Moreover, in the affine and Euclidean conditions one could maintain consistent orientations for the distractors and targets during training, then switch them in the testing phase to assess transfer within the same level of invariant structural stability.

Response: Thanks for raising the issue regarding the mechanism of transfer within each invariant conditions. We plan to design an additional experiment that is similar in paradigm to Experiment 2, aiming to examine how VPL generalizes to a new test location within a single invariant stability level.

• In the section detailing the modeling experiment using deep neural networks (DNN), the takeaway was unclear. While it was interesting to observe that the DNN exhibited a generalization pattern across conditions similar to that seen in the human experiments, the claim made in the abstract and introduction that the model provides a 'mechanistic' explanation for the phenomenon seems overstated. The pattern of weight changes across layers, as depicted in Figure 7, does not conclusively explain the observed variability in generalizations. Furthermore, the substantial weight change observed in the first two layers during the orientation discrimination task is somewhat counterintuitive. Given that neurons in early layers typically have smaller receptive fields and narrower tunings, one would expect this to result in less transfer, not more.

Response: We appreciate the reviewer's feedback regarding the clarity of our DNN modeling experiment. We acknowledge that while DNNs have been demonstrated to serve as models for visual systems as well as VPL, the claim that the model provides a ‘mechanistic’ explanation for the phenomenon still overstated. In our revised version,

We will attempt a more detailed analysis of the DNN model while providing a more explicit explanation of the findings from the DNN modeling experiment, emphasizing its implications for understanding the observed variability in generalizations.

Additionally, the substantial weight change observed in the first two layers during the orientation discrimination task is not contradictory to the theoretical framework we proposed, instead, it aligns with our speculation regarding the neural mechanisms of VPL for geometric invariants. Specifically, it suggests that invariants with lower stability rely more on the plasticity of lower-level brain areas, thus exhibiting poorer generalization performance to new locations or stimulus features within each invariant conditions. However, it does not imply that their learning effects cannot transfer to invariants with higher stability.

Reviewer #2 (Public Review):

The strengths of this paper are clear: The authors are asking a novel question about geometric representation that would be relevant to a broad audience. Their question has a clear grounding in pre-existing mathematical concepts, that, to my knowledge, have been only minimally explored in cognitive science. Moreover, the data themselves are quite striking, such that my only concern would be that the data seem almost too clean. It is hard to know what to make of that, however. From one perspective, this is even more reason the results should be publicly available. Yet I am of the (perhaps unorthodox) opinion that reviewers should voice these gut reactions, even if it does not influence the evaluation otherwise. Below I offer some more concrete comments:

(1) The justification for the designs is not well explained. The authors simply tell the audience in a single sentence that they test projective, affine, and Euclidean geometry. But despite my familiarity with these terms -- familiarity that many readers may not have -- I still had to pause for a very long time to make sense of how these considerations led to the stimuli that were created. I think the authors must, for a point that is so central to the paper, thoroughly explain exactly why the stimuli were designed the way that they were and how these designs map onto the theoretical constructs being tested.

(2) I wondered if the design in Experiment 1 was flawed in one small but critical way. The goal of the parallelism stimuli, I gathered, was to have a set of items that is not parallel to the other set of items. But in doing that, isn't the manipulation effectively the same as the manipulation in the orientation stimuli? Both functionally involve just rotating one set by a fixed amount. (Note: This does not seem to be a problem in Experiment 2, in which the conditions are more clearly delineated.)

(3) I wondered if the results would hold up for stimuli that were more diverse. It seems that a determined experimenter could easily design an "adversarial" version of these experiments for which the results would be unlikely to replicate. For instance: In the orientation group in Experiment 1, what if the odd-one-out was rotated 90 degrees instead of 180 degrees? Intuitively, it seems like this trial type would now be much easier, and the pattern observed here would not hold up. If it did hold up, that would provide stronger support for the authors' theory.

It is not enough, in my opinion, to simply have some confirmatory evidence of this theory. One would have to have thoroughly tested many possible ways that theory could fail. I'm unsure that enough has been done here to convince me that these ideas would hold up across a more diverse set of stimuli.

Response: (1) We appreciate the reviewer’s feedback regarding the justification for our experimental designs. We recognize the importance of thoroughly explaining how our stimuli were designed and how these designs correspond to the theoretical constructs being tested. In our revised version, we will enhance the introduction of Erlangen program and provide a more detailed explanation of the rationale behind our stimulus designs, aiming to enhance the clarity and transparency of our experimental approach for readers who may not be familiar with these concepts.

(2) We appreciate the reviewer’s insight into the design of Experiment 1 and the concern regarding the potential similarity between the parallelism and orientation stimuli manipulations.

The parallelism and orientation stimuli in Experiment 1 were first used by Olson & Attneave (1970) to support line-based models of shape coding and then adapted to measure the relative salience of different geometric properties (Chen, 1986). In the parallelism stimuli, the odd quadrant differs from the rest in line slope, while in the orientation stimuli, in contrast, the odd quadrant contains exactly the same line segments as the rest but differs in direction pointed by the angles. The result, that the odd quadrant was detected much faster in the parallelism stimuli than in the orientation stimuli, can serve as evidence for line-based models of shape coding. However, according to Chen (1986, 2005), the idea of invariants over transformations suggests a new analysis of the data: in the parallelism stimuli, the fact that line segments share the same slope essentially implies that they are parallel, and the discrimination may be actually based on parallelism. Thus, the faster discrimination of the parallelism stimuli than that of the orientation stimuli may be explained in terms of relative superiority of parallelism over orientation of angles—a Euclidean property.

The group of stimuli in Experiment 1 has been employed by several studies to investigate scientific questions related to the Klein’s hierarchy of geometries (L. Chen, 2005; Meng et al., 2019; B. Wang et al., n.d.). Due to historical inheritance, we adopted this set of stimuli and corresponding paradigm, despite their imperfect design.

(3) Thanks for raising the important issue of stimulus diversity and the potential for "adversarial" versions of the experiments to challenge our findings. We acknowledge the validity of your concern and recognize the need to demonstrate the robustness of our results across a range of stimuli. We plan to design additional experiments to investigate the potential implications of varying stimulus characteristics, such as different rotation angles proposed by the reviewer, on the observed patterns of performance.

Author Response

We would like to thank the editors and reviewers who took their valuable time to evaluate the manuscript from various perspectives. We are delighted that our technique was found appealing to biologists and imaging technologists. However, we received several comments that the principles and effectiveness of our techniques are often vague and difficult to understand. They also pointed out that the explanations and representations for several figures were not appropriate. We will revise the manuscript to address these issues and make the manuscript more clear and rigorous.

Author Response

We thank both the editors and the Reviewers for their thoughtful comments and recommendations, that will certainly help us improve the manuscript. Below we address in a brief format some of the comments made, and then outline the changes to the manuscript that we plan to implement in the revision.

We see three interrelated issues in the comments of the Reviewers:

• the length and complexity of the manuscript;

• the link to previously proposed formalisms;

• the impact of adopting the proposed information-theoretic framework.

With regard to all of these issues, we would first like to highlight that the overall goal of our effort was to integrate con tributions to understanding the mechanisms underlying cognitive control across multiple different disciplines, using the information theoretic framework as a common formalism, while respecting and building on prior efforts as much as possible. Accordingly, we sought to be as explicit as possible about how we bridge from prior work using information theory, as well as neural networks and dynamical systems theory, which contributed to length of the original manuscript. While we continue to consider this an important goal, we will do our best to shorten and clarify the main exposition by reorganizing the manuscript as suggested by Reviewer #1 (i.e., in a way that is similar to what we did in our previous Nature Physics paper on multitasking). Specifically, we will move a substantially greater amount of the bridging material to the Supple mentary Information (SI), including the detailed discussion of the Stroop task, and the description of the link to Koechlin & Summerfield’s [L1] information theory formalism. We will also now include an outline of the full model at the beginning of the manuscript, that includes control and learning, and then more succinctly describe simplifications that focus on specific issues and applications in the remainder of the document.

Along similar lines, we will revise and harmonize our presentation of the formalism and notations, to make these more consistent, clearer and more concise throughout the document. Again, some of the inconsistencies in notation arose from our initial description of previous work, and in particular that of Koechlin & Summerfield[L1] that was an important inspiration for our work but that used slightly different notations. An important motivation for our introduction of new notation was that their formulation focused on the performance of a single task at a time, whereas a primary goal of our work was to extend the information theoretic treatment to simultaneous performance of multiple tasks. That is, in focusing on single tasks, Koechlin & Summerfield could refer to a task simply as a direct association between stimuli and responses, whereas we required a way of being able to refer to sets of tasks performed at once (”multitasks”), which in turn required specification of internal pathways. Moreover, they do not provide a mechanism to compute the conditional information Q(a|s) of a response/action s conditioned to a stimulus s does not provide a way to compute it explicitly. Our formalism instead provides a way to explicitly unpack this expression in terms of the efficacies –automatic (Eq. 5) or controlled (Eq. 15)– which can also account for the competition between different stimuli {s1, s2, . . . sn}. It also describes explicitly the competition between multiple tasks (Eq. 18, and Eq. 25 for multiple layers), because different ways of processing schemes for the same combinations of stimuli/responses can incur different levels of internal dependencies and thus require different control strategies.

To mitigate any confusion over terminology we will, as noted above, move a detailed discussion of Koechlin & Summer- field’s formulation, and how it maps to the one we present, to the SI, while taking care to introduce ours clearly at the beginning of the main document, and use it consistently throughout the remainder of the document. We will also make an important distinction – between informational and cognitive costs – more clearly, that we did not do adequately in the original manuscript.

Finally, to more clearly and concretely convey what we consider to be the most important contributions, we will restrict the number of examples we present to ones that relate most directly to the central points (e.g., the effect and limits of control in the presence of interference, and the differences in control strategy under limited temporal horizons). Accompanying our revision, we will also provide a full point-by-point response to the comments and questions raised by the Reviewers. We summarize some the key points we will address below.

PRELIMINARY REPLY TO THE REPORT OF REVIEWER #1

We want to thank the Reviewer for the time and effort put into reviewing our paper and constructive feedback that was provided. We also thank the Reviewer for recognizing the need for a clear computational account of how ”control” manages conflicts by scheduling tasks to be executed in parallel versus serially, and for the positive evaluation on our “efforts of the authors to give these intuitions a more concrete computational grounding.”. As noted in the general reply above, we regret the lack of clarity in several parts of the manuscript and in our introduction and use of the formalism. We consider the following to be the main points to be addressed:

• the role of task graphs and their mapping to standard neural architectures

• the description of entropy and related information-theoretic concepts;

• confusing choice of symbols in our notation between stimuli/responses and serialization/reconfiguration costs;

• missing definition of response time;

Regarding the first part point, we acknowledge that the network architectures we focus on do not draw direct inspiration from conventional machine learning models. Instead, our approach is rooted in the longstanding tradition of using (often simpler, but also more readily interpretable) neural network models to address human cognitive function and how this may be implemented in the brain [L2]; and, in particular, the mechanisms underlying cognitive control (e.g., [L3, L4]). In this context, we emphasize that, for analytical clarity, we deliberately abstract away from many biological details, in an effort to identify those principles of function that are most relevant to cognitive function. Nevertheless, our network architecture is inspired by two concepts that are central to neurobiological mechanisms of control: inhibition and gain modulation. Specifi- cally, we incorporate mutual inhibition among neural processing units, a feature represented by the parameter β. This aspect of our model is consistent with biologically inspired frameworks of neural processing, such as those discussed by Munakata et al. (2011)[L5], reflecting the competitive dynamics observed in neural circuits. Moreover, we introduce the parameter ν to represent a strictly modulatory form of control, akin to the role of neuromodulators in the brain. This modulatory control adjusts the sensitivity of a node to differences among its inputs (e.g., Servan-Schreiber, Printz, & Cohen, (1990)[L6]; Aston-Jones & Cohen (2005)[L7]). Finally, as the Reviewer notes, additional hidden layers can improve expressivity in neural networks, enabling the efficient implementation of more complex tasks, and are a universal feature of biological and artificial neural systems. We thus examined multitasking capability under the assumption that multiple hidden layers are present in a network; irrespective of whether they are needed to implement the corresponding tasks.

Regarding the second point, as noted above, we believe that the confusion arose from our review of the work by Koechlin & Summerfield. In their formalism, in which an action a is chosen (from a set of potential actions) with probability p(a), the cost of choosing that action is − log p(a). This is usually referred to as the information content or, alternatively, the localized entropy [L8]. As the Reviewer correctly observed, the canonical (Shannon) entropy is actually the expectation lEa[− log p(a)] over the localized entropies of a set of actions. In summarizing their formulation, we misleadingly stated that ”they used standard Shannon entropy formalism as a measure of the information required to select the action a.” We will now correct this to state: “[..] they used local entropy (− log p(a)) as a measure of the information required to select the action a, that can be treated as the cost of choosing that action.” We follow this formulation in our own, referring to informational cost as Ψ, and generalizing this to include cases in which more than one action may be chosen to perform at a time.

Regarding the third point, the confusion is due to our use of the letters S and R for both the stimulus and response units (in Sec. II.B) and then serialization and reconstruction costs (in eqs 31-33). We will fix this by renaming the serialization and reconstruction costs more explicitly as S er and Rec.

Finally, we realized we never explicitly stated the expression of the response time we used, but only pointed to it in the literature. In the manuscript we used the expression given in Eq. 53 of [L9], which provides response times as function of the error rates ER and the number of options .

PRELIMINARY REPLY TO THE REPORT OF REVIEWER #2

We want to thank the Reviewer for recognizing our effort to ”rigorously synthesize ideas about multi-tasking within an information-theoretic framework” and its potential. We also thank the Reviewer for the careful comments.

To our best understanding, and similarly to Reviewer #1, the main comments of the Reviewer are on:

• the length and density of the paper;

• the presentation of the Koechlin & Summerfield’s formalism, and the mismatch/lack of clarity of ours in certain points;

• the added value of the information theoretic formalism.

Regarding the first two points, which are common to Reviewer #1, we plan to move a significant part of the manuscript to the Supplementary Information, both to improve readability and make the manuscript shorter, as well as to provide one consistent and cleaner formalism (in particular with regards to the typos and errors highlighted by the Reviewer). In par- ticular, with respect to the comment on Eq. 4-5-6, we will clarify that the probability p[ fi j] is the probability that a certain input dimension (i in this case) is selected by on node j to produce its response (averaged over the individual inputs in each input dimension). We will also take care to make sure that the definition and domain of the various probabilities and probability distributions we use are clearly delineated (e.g. where the costs computed for tasks and task pathways come from).

Regarding the third point, we hope that our work offers value in at least two ways: i) it helps bring unity to ideas and descriptions about the capacity constraints associated with cognitive control that have previously been articulated in different forms (viz., neural networks, dynamical systems, and statistical mechanical accounts); and ii) doing so within an information theoretic framework not only lends rigor and precision to the formulation, but also allows us to cast the allocation of control in normative form – that is, as an optimization problem in which the agent seeks to minimize costs while maximizing gains. While we do not address specific empirical phenomena or datasets in the present treatment, we have done our best to provide examples showing that: a) our information theoretic formulation aligns with treatments using other formalisms that have been used to address empirical phenomena (e.g., with neural network models of the Stroop task); and b) our formulation can be used as a framework for providing a normative approach to widely studied empirical phenomena (e.g., the transition from control-dependent to automatic processing during skill acquisition) that, to date, have been addressed largely from a descriptive perspective; and that it can provide a formally rigorous approach to addressing such phenomena.

[L1] E. Koechlin and C. Summerfield, Trends in cognitive sciences 11, 229 (2007).

[L2] J. L. McClelland, D. E. Rumelhart, P. R. Group, et al., Explorations in the Microstructure of Cognition 2, 216 (1986).

[L3] J. D. Cohen, K. Dunbar, and J. L. McClelland, Psychological Review 97, 332 (1990).

[L4] E. K. Miller and J. D. Cohen, Annual review of neuroscience 24, 167 (2001).

[L5] Y. Munakata, S. A. Herd, C. H. Chatham, B. E. Depue, M. T. Banich, and R. C. O’Reilly, Trends in cognitive sciences 15, 453 (2011).

[L6] D. Servan-Schreiber, H. Printz, and J. D. Cohen, Science 249, 892 (1990).

[L7] G. Aston-Jones and J. D. Cohen, Annu. Rev. Neurosci. 28, 403 (2005).

[L8] T. F. Varley, Plos one 19, e0297128 (2024).

[L9] T. McMillen and P. Holmes, Journal of Mathematical Psychology 50, 30 (2006).

Author Response

Reviewer #1 (Public Review):

This study used a multi-day learning paradigm combined with fMRI to reveal neural changes reflecting the learning of new (arbitrary) shape-sound associations. In the scanner, the shapes and sounds are presented separately and together, both before and after learning. When they are presented together, they can be either consistent or inconsistent with the learned associations. The analyses focus on auditory and visual cortices, as well as the object-selective cortex (LOC) and anterior temporal lobe regions (temporal pole (TP) and perirhinal cortex (PRC)). Results revealed several learning-induced changes, particularly in the anterior temporal lobe regions. First, the LOC and PRC showed a reduced bias to shapes vs sounds (presented separately) after learning. Second, the TP responded more strongly to incongruent than congruent shape-sound pairs after learning. Third, the similarity of TP activity patterns to sounds and shapes (presented separately) was increased for non-matching shape-sound comparisons after learning. Fourth, when comparing the pattern similarity of individual features to combined shape-sound stimuli, the PRC showed a reduced bias towards visual features after learning. Finally, comparing patterns to combined shape-sound stimuli before and after learning revealed a reduced (and negative) similarity for incongruent combinations in PRC. These results are all interpreted as evidence for an explicit integrative code of newly learned multimodal objects, in which the whole is different from the sum of the parts.

The study has many strengths. It addresses a fundamental question that is of broad interest, the learning paradigm is well-designed and controlled, and the stimuli are real 3D stimuli that participants interact with. The manuscript is well written and the figures are very informative, clearly illustrating the analyses performed.

There are also some weaknesses. The sample size (N=17) is small for detecting the subtle effects of learning. Most of the statistical analyses are not corrected for multiple comparisons (ROIs), and the specificity of the key results to specific regions is also not tested. Furthermore, the evidence for an integrative representation is rather indirect, and alternative interpretations for these results are not considered.

We thank the reviewer for their careful reading and the positive comments on our manuscript. As suggested, we have conducted additional analyses of theoretically-motivated ROIs and have found that temporal pole and perirhinal cortex are the only regions to show the key experience-dependent transformations. We are much more cautious with respect to multiple comparisons, and have removed a series of post hoc across-ROI comparisons that were irrelevant to the key questions of the present manuscript. The revised manuscript now includes much more discussion about alternative interpretations as suggested by the reviewer (and also by the other reviewers).

Additionally, we looked into scanning more participants, but our scanner has since had a full upgrade and the sequence used in the current study is no longer supported by our scanner. However, we note that while most analyses contain 17 participants, we employed a within-subject learning design that is not typically used in fMRI experiments and increases our power to detect an effect. This is supported by the robust effect size of the behavioural data, whereby 17 out of 18 participants revealed a learning effect (Cohen’s D = 1.28) and which was replicated in a follow-up experiment with a larger sample size.

We address the other reviewer comments point-by-point in the below.

Reviewer #2 (Public Review):

Li et al. used a four-day fMRI design to investigate how unimodal feature information is combined, integrated, or abstracted to form a multimodal object representation. The experimental question is of great interest and understanding how the human brain combines featural information to form complex representations is relevant for a wide range of researchers in neuroscience, cognitive science, and AI. While most fMRI research on object representations is limited to visual information, the authors examined how visual and auditory information is integrated to form a multimodal object representation. The experimental design is elegant and clever. Three visual shapes and three auditory sounds were used as the unimodal features; the visual shapes were used to create 3D-printed objects. On Day 1, the participants interacted with the 3D objects to learn the visual features, but the objects were not paired with the auditory features, which were played separately. On Day 2, participants were scanned with fMRI while they were exposed to the unimodal visual and auditory features as well as pairs of visual-auditory cues. On Day 3, participants again interacted with the 3D objects but now each was paired with one of the three sounds that played from an internal speaker. On Day 4, participants completed the same fMRI scanning runs they completed on Day 2, except now some visual-auditory feature pairs corresponded with Congruent (learned) objects, and some with Incongruent (unlearned) objects. Using the same fMRI design on Days 2 and 4 enables a well-controlled comparison between feature- and object-evoked neural representations before and after learning. The notable results corresponded to findings in the perirhinal cortex and temporal pole. The authors report (1) that a visual bias on Day 2 for unimodal features in the perirhinal cortex was attenuated after learning on Day 4, (2) a decreased univariate response to congruent vs. incongruent visual-auditory objects in the temporal pole on Day 4, (3) decreased pattern similarity between congruent vs. incongruent pairs of visual and auditory unimodal features in the temporal pole on Day 4, (4) in the perirhinal cortex, visual unimodal features on Day 2 do not correlate with their respective visual-auditory objects on Day 4, and (5) in the perirhinal cortex, multimodal object representations across Days 2 and 4 are uncorrelated for congruent objects and anticorrelated for incongruent. The authors claim that each of these results supports the theory that multimodal objects are represented in an "explicit integrative" code separate from feature representations. While these data are valuable and the results are interesting, the authors' claims are not well supported by their findings.

We thank the reviewer for the careful reading of our manuscript and positive comments. Overall, we now stay closer to the data when describing the results and provide our interpretation of these results in the discussion section while remaining open to alternative interpretations (as also suggested by Reviewer 1).

(1) In the introduction, the authors contrast two theories: (a) multimodal objects are represented in the co-activation of unimodal features, and (b) multimodal objects are represented in an explicit integrative code such that the whole is different than the sum of its parts. However, the distinction between these two theories is not straightforward. An explanation of what is precisely meant by "explicit" and "integrative" would clarify the authors' theoretical stance. Perhaps we can assume that an "explicit" representation is a new representation that is created to represent a multimodal object. What is meant by "integrative" is more ambiguous-unimodal features could be integrated within a representation in a manner that preserves the decodability of the unimodal features, or alternatively the multimodal representation could be completely abstracted away from the constituent features such that the features are no longer decodable. Even if the object representation is "explicit" and distinct from the unimodal feature representations, it can in theory still contain featural information, though perhaps warped or transformed. The authors do not clearly commit to a degree of featural abstraction in their theory of "explicit integrative" multimodal object representations which makes it difficult to assess the validity of their claims.

Due to its ambiguity, we removed the term “explicit” and now make it clear that our central question was whether crossmodal object representations require only unimodal feature-level representations (e.g., frogs are created from only the combination of shape and sound) or whether crossmodal object representations also rely on an integrative code distinct from the unimodal features (e.g., there is something more to “frog” than its original shape and sound). We now clarify this in the revised manuscript.

“One theoretical view from the cognitive sciences suggests that crossmodal objects are built from component unimodal features represented across distributed sensory regions.8 Under this view, when a child thinks about “frog”, the visual cortex represents the appearance of the shape of the frog whereas the auditory cortex represents the croaking sound. Alternatively, other theoretical views predict that multisensory objects are not only built from their component unimodal sensory features, but that there is also a crossmodal integrative code that is different from the sum of these parts.9,10,11,12,13 These latter views propose that anterior temporal lobe structures can act as a polymodal “hub” that combines separate features into integrated wholes.9,11,14,15” – pg. 4

For this reason, we designed our paradigm to equate the unimodal representations, such that neural differences between the congruent and incongruent conditions provide evidence for a crossmodal integrative code different from the unimodal features (because the unimodal features are equated by default in the design).

“Critically, our four-day learning task allowed us to isolate any neural activity associated with integrative coding in anterior temporal lobe structures that emerges with experience and differs from the neural patterns recorded at baseline. The learned and non-learned crossmodal objects were constructed from the same set of three validated shape and sound features, ensuring that factors such as familiarity with the unimodal features, subjective similarity, and feature identity were tightly controlled (Figure 2). If the mind represented crossmodal objects entirely as the reactivation of unimodal shapes and sounds (i.e., objects are constructed from their parts), then there should be no difference between the learned and non-learned objects (because they were created from the same three shapes and sounds). By contrast, if the mind represented crossmodal objects as something over and above their component features (i.e., representations for crossmodal objects rely on integrative coding that is different from the sum of their parts), then there should be behavioral and neural differences between learned and non-learned crossmodal objects (because the only difference across the objects is the learned relationship between the parts). Furthermore, this design allowed us to determine the relationship between the object representation acquired after crossmodal learning and the unimodal feature representations acquired before crossmodal learning. That is, we could examine whether learning led to abstraction of the object representations such that it no longer resembled the unimodal feature representations.” – pg. 5

Furthermore, we agree with the reviewer that our definition and methodological design does not directly capture the structure of the integrative code. With experience, the unimodal feature representations may be completely abstracted away, warped, or changed in a nonlinear transformation. We suggest that crossmodal learning forms an integrative code that is different from the original unimodal representations in the anterior temporal lobes, however, we agree that future work is needed to more directly capture the structure of the integrative code that emerges with experience.

“In our task, participants had to differentiate congruent and incongruent objects constructed from the same three shape and sound features (Figure 2). An efficient way to solve this task would be to form distinct object-level outputs from the overlapping unimodal feature-level inputs such that congruent objects are made to be orthogonal from the representations before learning (i.e., measured as pattern similarity equal to 0 in the perirhinal cortex; Figure 5b, 6, Supplemental Figure S5), whereas non-learned incongruent objects could be made to be dissimilar from the representations before learning (i.e., anticorrelation, measured as patten similarity less than 0 in the perirhinal cortex; Figure 6). Because our paradigm could decouple neural responses to the learned object representations (on Day 4) from the original component unimodal features at baseline (on Day 2), these results could be taken as evidence of pattern separation in the human perirhinal cortex.11,12 However, our pattern of results could also be explained by other types of crossmodal integrative coding. For example, incongruent object representations may be less stable than congruent object representations, such that incongruent objects representation are warped to a greater extent than congruent objects (Figure 6).” – pg. 18

“As one solution to the crossmodal binding problem, we suggest that the temporal pole and perirhinal cortex form unique crossmodal object representations that are different from the distributed features in sensory cortex (Figure 4, 5, 6, Supplemental Figure S5). However, the nature by which the integrative code is structured and formed in the temporal pole and perirhinal cortex following crossmodal experience – such as through transformations, warping, or other factors – is an open question and an important area for future investigation.” – pg. 18

(2) After participants learned the multimodal objects, the authors report a decreased univariate response to congruent visual-auditory objects relative to incongruent objects in the temporal pole. This is claimed to support the existence of an explicit, integrative code for multimodal objects. Given the number of alternative explanations for this finding, this claim seems unwarranted. A simpler interpretation of these results is that the temporal pole is responding to the novelty of the incongruent visual-auditory objects. If there is in fact an explicit, integrative multimodal object representation in the temporal pole, it is unclear why this would manifest in a decreased univariate response.

We thank the reviewer for identifying this issue. Our behavioural design controls unimodal feature-level novelty but allows object-level novelty to differ. Thus, neural differences between the congruent and incongruent conditions reflects sensitivity to the object-level differences between the combination of shape and sound. However, we agree that there are multiple interpretations regarding the nature of how the integrative code is structured in the temporal pole and perirhinal cortex. We have removed the interpretation highlighted by the reviewer from the results. Instead, we now provide our preferred interpretation in the discussion, while acknowledging the other possibilities that the reviewer mentions.

As one possibility, these results in temporal pole may reflect “conceptual combination”. “hummingbird” – a congruent pairing – may require less neural resources than an incongruent pairing such as “bark-frog”.

“Furthermore, these distinct anterior temporal lobe structures may be involved with integrative coding in different ways. For example, the crossmodal object representations measured after learning were found to be related to the component unimodal feature representations measured before learning in the temporal pole but not the perirhinal cortex (Figure 5, 6, Supplemental Figure S5). Moreover, pattern similarity for congruent shape-sound pairs were lower than the pattern similarity for incongruent shape-sound pairs after crossmodal learning in the temporal pole but not the perirhinal cortex (Figure 4b, Supplemental Figure S3a). As one interpretation of this pattern of results, the temporal pole may represent new crossmodal objects by combining previously learned knowledge. 8,9,10,11,13,14,15,33 Specifically, research into conceptual combination has linked the anterior temporal lobes to compound object concepts such as “hummingbird”.34,35,36 For example, participants during our task may have represented the sound-based “humming” concept and visually-based “bird” concept on Day 1, forming the crossmodal “hummingbird” concept on Day 3; Figure 1, 2, which may recruit less activity in temporal pole than an incongruent pairing such as “barking-frog”. For these reasons, the temporal pole may form a crossmodal object code based on pre-existing knowledge, resulting in reduced neural activity (Figure 3d) and pattern similarity towards features associated with learned objects (Figure 4b).”– pg. 18

(3) The authors ran a neural pattern similarity analysis on the unimodal features before and after multimodal object learning. They found that the similarity between visual and auditory features that composed congruent objects decreased in the temporal pole after multimodal object learning. This was interpreted to reflect an explicit integrative code for multimodal objects, though it is not clear why. First, behavioral data show that participants reported increased similarity between the visual and auditory unimodal features within congruent objects after learning, the opposite of what was found in the temporal pole. Second, it is unclear why an analysis of the unimodal features would be interpreted to reflect the nature of the multimodal object representations. Since the same features corresponded with both congruent and incongruent objects, the nature of the feature representations cannot be interpreted to reflect the nature of the object representations per se. Third, using unimodal feature representations to make claims about object representations seems to contradict the theoretical claim that explicit, integrative object representations are distinct from unimodal features. If the learned multimodal object representation exists separately from the unimodal feature representations, there is no reason why the unimodal features themselves would be influenced by the formation of the object representation. Instead, these results seem to more strongly support the theory that multimodal object learning results in a transformation or warping of feature space.

We apologize for the lack of clarity. We have now overhauled this aspect of our manuscript in an attempt to better highlight key aspects of our experimental design. In particular, because the unimodal features composing the congruent and incongruent objects were equated, neural differences between these conditions would provide evidence for an experience-dependent crossmodal integrative code that is different from its component unimodal features.

Related to the second and third points, we were looking at the extent to which the original unimodal representations change with crossmodal learning. Before crossmodal learning, we found that the perirhinal cortex tracked the similarity between the individual visual shape features and the crossmodal objects that were composed of those visual shapes – however, there was no evidence that perirhinal cortex was tracking the unimodal sound features on those crossmodal objects. After crossmodal learning, we see that this visual shape bias in perirhinal cortex was no longer present – that is, the representation in perirhinal cortex started to look less like the visual features that comprise the objects. Thus, crossmodal learning transformed the perirhinal representations so that they were no longer predominantly grounded in a single visual modality, which may be a mechanism by which object concepts gain their abstraction. We have now tried to be clearer about this interpretation throughout the paper.

Notably, we suggest that experience may change both the crossmodal object representations, as well as the unimodal feature representations. For example, we have previously shown that unimodal visual features are influenced by experience in parallel with the representation of the conjunction (e.g., Liang et al., 2020; Cerebral Cortex). Nevertheless, we remain open to the myriad possible structures of the integrative code that might emerge with experience.

We now clarify these points throughout the manuscript. For example:

“We then examined whether the original representations would change after participants learned how the features were paired together to make specific crossmodal objects, conducting the same analysis described above after crossmodal learning had taken place (Figure 5b). With this analysis, we sought to measure the relationship between the representation for the learned crossmodal object and the original baseline representation for the unimodal features. More specifically, the voxel-wise activity for unimodal feature runs before crossmodal learning was correlated to the voxel-wise activity for crossmodal object runs after crossmodal learning (Figure 5b). Another linear mixed model which included modality as a fixed factor within each ROI revealed that the perirhinal cortex was no longer biased towards visual shape after crossmodal learning (F1,32 = 0.12, p = 0.73), whereas the temporal pole, LOC, V1, and A1 remained biased towards either visual shape or sound (F1,30-32 between 16.20 and 73.42, all p < 0.001, η2 between 0.35 and 0.70).” – pg. 14

“To investigate this effect in perirhinal cortex more specifically, we conducted a linear mixed model to directly compare the change in the visual bias of perirhinal representations from before crossmodal learning to after crossmodal learning (green regions in Figure 5a vs. 5b). Specifically, the linear mixed model included learning day (before vs. after crossmodal learning) and modality (visual feature match to crossmodal object vs. sound feature match to crossmodal object). Results revealed a significant interaction between learning day and modality in the perirhinal cortex (F1,775 = 5.56, p = 0.019, η2 = 0.071), meaning that the baseline visual shape bias observed in perirhinal cortex (green region of Figure 5a) was significantly attenuated with experience (green region of Figure 5b). After crossmodal learning, a given shape no longer invoked significant pattern similarity between objects that had the same shape but differed in terms of what they sounded like. Taken together, these results suggest that prior to learning the crossmodal objects, the perirhinal cortex had a default bias toward representing the visual shape information and was not representing sound information of the crossmodal objects. After crossmodal learning, however, the visual shape bias in perirhinal cortex was no longer present. That is, with crossmodal learning, the representations within perirhinal cortex started to look less like the visual features that comprised the crossmodal objects, providing evidence that the perirhinal representations were no longer predominantly grounded in the visual modality.” – pg. 13

“Importantly, the initial visual shape bias observed in the perirhinal cortex was attenuated by experience (Figure 5, Supplemental Figure S5), suggesting that the perirhinal representations had become abstracted and were no longer predominantly grounded in a single modality after crossmodal learning. One possibility may be that the perirhinal cortex is by default visually driven as an extension to the ventral visual stream,10,11,12 but can act as a polymodal “hub” region for additional crossmodal input following learning.” – pg. 19

(4) The most compelling evidence the authors provide for their theoretical claims is the finding that, in the perirhinal cortex, the unimodal feature representations on Day 2 do not correlate with the multimodal objects they comprise on Day 4. This suggests that the learned multimodal object representations are not combinations of their unimodal features. If unimodal features are not decodable within the congruent object representations, this would support the authors' explicit integrative hypothesis. However, the analyses provided do not go all the way in convincing the reader of this claim. First, the analyses reported do not differentiate between congruent and incongruent objects. If this result in the perirhinal cortex reflects the formation of new multimodal object representations, it should only be true for congruent objects but not incongruent objects. Since the analyses combine congruent and incongruent objects it is not possible to know whether this was the case. Second, just because feature representations on Day 2 do not correlate with multimodal object patterns on Day 4 does not mean that the object representations on Day 4 do not contain featural information. This could be directly tested by correlating feature representations on Day 4 with congruent vs. incongruent object representations on Day 4. It could be that representations in the perirhinal cortex are not stable over time and all representations-including unimodal feature representations-shift between sessions, which could explain these results yet not entail the existence of abstracted object representations.

We thank the reviewer for this suggestion and have conducted the two additional analyses. Specifically, we split the congruent and incongruent conditions and also investigated correlations between unimodal representations on Day 4 with crossmodal object representations on Day 4. There was no significant interaction between modality and congruency in any ROI across or within learning days. One possible explanation for these findings is that both congruent and incongruent crossmodal objects are represented differently from their underlying unimodal features, and all of these representations can transform with experience.

However, the new analyses also revealed that perirhinal cortex was the only region without a modality-specific bias after crossmodal learning (e.g., Day 4 Unimodal Feature runs x Day 4 Crossmodal Object runs; now shown in Supplemental Figure S5). Overall, these results are consistent with the notion of a crossmodal integrative code in perirhinal cortex that has changed with experience and is different from the component unimodal features. Nevertheless, we explore alternative interpretations for how the crossmodal code emerges with experience in the discussion.

“To examine whether these results differed by congruency (i.e., whether any modality-specific biases differed as a function of whether the object was congruent or incongruent), we conducted exploratory linear mixed models for each of the five a priori ROIs across learning days. More specifically, we correlated: 1) the voxel-wise activity for Unimodal Feature Runs before crossmodal learning to the voxel-wise activity for Crossmodal Object Runs before crossmodal learning (Day 2 vs. Day 2), 2) the voxel-wise activity for Unimodal Feature Runs before crossmodal learning to the voxel-wise activity for Crossmodal Object Runs after crossmodal learning (Day 2 vs Day 4), and 3) the voxel-wise activity for Unimodal Feature Runs after crossmodal learning to the voxel-wise activity for Crossmodal Object Runs after crossmodal learning (Day 4 vs Day 4). For each of the three analyses described, we then conducted separate linear mixed models which included modality (visual feature match to crossmodal object vs. sound feature match to crossmodal object) and congruency (congruent vs. incongruent)….There was no significant relationship between modality and congruency in any ROI between Day 2 and Day 2 (F1,346-368 between 0.00 and 1.06, p between 0.30 and 0.99), between Day 2 and Day 4 (F1,346-368 between 0.021 and 0.91, p between 0.34 and 0.89), or between Day 4 and Day 4 (F1,346-368 between 0.01 and 3.05, p between 0.082 and 0.93). However, exploratory analyses revealed that perirhinal cortex was the only region without a modality-specific bias and where the unimodal feature runs were not significantly correlated to the crossmodal object runs after crossmodal learning (Supplemental Figure S5).” – pg. 14

“Taken together, the overall pattern of results suggests that representations of the crossmodal objects in perirhinal cortex were heavily influenced by their consistent visual features before crossmodal learning. However, the crossmodal object representations were no longer influenced by the component visual features after crossmodal learning (Figure 5, Supplemental Figure S5). Additional exploratory analyses did not find evidence of experience-dependent changes in the hippocampus or inferior parietal lobes (Supplemental Figure S4c-e).” – pg. 14

“The voxel-wise matrix for Unimodal Feature runs on Day 4 were correlated to the voxel-wise matrix for Crossmodal Object runs on Day 4 (see Figure 5 in the main text for an example). We compared the average pattern similarity (z-transformed Pearson correlation) between shape (blue) and sound (orange) features specifically after crossmodal learning. Consistent with Figure 5b, perirhinal cortex was the only region without a modality-specific bias. Furthermore, perirhinal cortex was the only region where the representations of both the visual and sound features were not significantly correlated to the crossmodal objects. By contrast, every other region maintained a modality-specific bias for either the visual or sound features. These results suggest that perirhinal cortex representations were transformed with experience, such that the initial visual shape representations (Figure 5a) were no longer grounded in a single modality after crossmodal learning. Furthermore, these results suggest that crossmodal learning formed an integrative code different from the unimodal features in perirhinal cortex, as the visual and sound features were not significantly correlated with the crossmodal objects. * p < 0.05, ** p < 0.01, *** p < 0.001. Horizontal lines within brain regions indicate a significant main effect of modality. Vertical asterisks denote pattern similarity comparisons relative to 0.” – Supplemental Figure S5

“We found that the temporal pole and perirhinal cortex – two anterior temporal lobe structures – came to represent new crossmodal object concepts with learning, such that the acquired crossmodal object representations were different from the representation of the constituent unimodal features (Figure 5, 6). Intriguingly, the perirhinal cortex was by default biased towards visual shape, but that this initial visual bias was attenuated with experience (Figure 3c, 5, Supplemental Figure S5). Within the perirhinal cortex, the acquired crossmodal object concepts (measured after crossmodal learning) became less similar to their original component unimodal features (measured at baseline before crossmodal learning); Figure 5, 6, Supplemental Figure S5. This is consistent with the idea that object representations in perirhinal cortex integrate the component sensory features into a whole that is different from the sum of the component parts, which might be a mechanism by which object concepts obtain their abstraction…. As one solution to the crossmodal binding problem, we suggest that the temporal pole and perirhinal cortex form unique crossmodal object representations that are different from the distributed features in sensory cortex (Figure 4, 5, 6, Supplemental Figure S5). However, the nature by which the integrative code is structured and formed in the temporal pole and perirhinal cortex following crossmodal experience – such as through transformations, warping, or other factors – is an open question and an important area for future investigation.” – pg. 18

In sum, the authors have collected a fantastic dataset that has the potential to answer questions about the formation of multimodal object representations in the brain. A more precise delineation of different theoretical accounts and additional analyses are needed to provide convincing support for the theory that “explicit integrative” multimodal object representations are formed during learning.

We thank the reviewer for the positive comments and helpful feedback. We hope that our changes to our wording and clarifications to our methodology now more clearly supports the central goal of our study: to find evidence of crossmodal integrative coding different from the original unimodal feature parts in anterior temporal lobe structures. We furthermore agree that future research is needed to delineate the structure of the integrative code that emerges with experience in the anterior temporal lobes.

Reviewer #3 (Public Review):

This paper uses behavior and functional brain imaging to understand how neural and cognitive representations of visual and auditory stimuli change as participants learn associations among them. Prior work suggests that areas in the anterior temporal (ATL) and perirhinal cortex play an important role in learning/representing cross-modal associations, but the hypothesis has not been directly tested by evaluating behavior and functional imaging before and after learning cross- modal associations. The results show that such learning changes both the perceived similarities amongst stimuli and the neural responses generated within ATL and perirhinal regions, providing novel support for the view that cross-modal learning leads to a representational change in these regions.

This work has several strengths. It tackles an important question for current theories of object representation in the mind and brain in a novel and quite direct fashion, by studying how these representations change with cross-modal learning. As the authors note, little work has directly assessed representational change in ATL following such learning, despite the widespread view that ATL is critical for such representation. Indeed, such direct assessment poses several methodological challenges, which the authors have met with an ingenious experimental design. The experiment allows the authors to maintain tight control over both the familiarity and the perceived similarities amongst the shapes and sounds that comprise their stimuli so that the observed changes across sessions must reflect learned cross-modal associations among these. I especially appreciated the creation of physical objects that participants can explore and the approach to learning in which shapes and sounds are initially experienced independently and later in an associated fashion. In using multi-echo MRI to resolve signals in ventral ATL, the authors have minimized a key challenge facing much work in this area (namely the poor SNR yielded by standard acquisition sequences in ventral ATL). The use of both univariate and multivariate techniques was well-motivated and helpful in testing the central questions. The manuscript is, for the most part, clearly written, and nicely connects the current work to important questions in two literatures, specifically (1) the hypothesized role of the perirhinal cortex in representing/learning complex conjunctions of features and (2) the tension between purely embodied approaches to semantic representation vs the view that ATL regions encode important amodal/crossmodal structure.

There are some places in the manuscript that would benefit from further explanation and methodological detail. I also had some questions about the results themselves and what they signify about the roles of ATL and the perirhinal cortex in object representation.

We thank the reviewer for their positive feedback and address the comments in the below point-by-point responses.

(A) I found the terms "features" and "objects" to be confusing as used throughout the manuscript, and sometimes inconsistent. I think by "features" the authors mean the shape and sound stimuli in their experiment. I think by "object" the authors usually mean the conjunction of a shape with a sound---for instance, when a shape and sound are simultaneously experienced in the scanner, or when the participant presses a button on the shape and hears the sound. The confusion comes partly because shapes are often described as being composed of features, not features in and of themselves. (The same is sometimes true of sounds). So when reading "features" I kept thinking the paper referred to the elements that went together to comprise a shape. It also comes from ambiguous use of the word object, which might refer to (a) the 3D- printed item that people play with, which is an object, or (b) a visually-presented shape (for instance, the localizer involved comparing an "object" to a "phase-scrambled" stimulus---here I assume "object" refers to an intact visual stimulus and not the joint presentation of visual and auditory items). I think the design, stimuli, and results would be easier for a naive reader to follow if the authors used the terms "unimodal representation" to refer to cases where only visual or auditory input is presented, and "cross-modal" or "conjoint" representation when both are present.

We thank the reviewer for this suggestion and agree. We have replaced the terms “features” and “objects” with “unimodal” and “crossmodal” in the title, text, and figures throughout the manuscript for consistency (i.e., “crossmodal binding problem”). To simplify the terminology, we have also removed the localizer results.

(B) There are a few places where I wasn't sure what exactly was done, and where the methods lacked sufficient detail for another scientist to replicate what was done. Specifically:

(1) The behavioral study assessing perceptual similarity between visual and auditory stimuli was unclear. The procedure, stimuli, number of trials, etc, should be explained in sufficient detail in methods to allow replication. The results of the study should also minimally be reported in the supplementary information. Without an understanding of how these studies were carried out, it was very difficult to understand the observed pattern of behavioral change. For instance, I initially thought separate behavioral blocks were carried out for visual versus auditory stimuli, each presented in isolation; however, the effects contrast congruent and incongruent stimuli, which suggests these decisions must have been made for the conjoint presentation of both modalities. I'm still not sure how this worked. Additionally, the manuscript makes a brief mention that similarity judgments were made in the context of "all stimuli," but I didn't understand what that meant. Similarity ratings are hugely sensitive to the contrast set with which items appear, so clarity on these points is pretty important. A strength of the design is the contention that shape and sound stimuli were psychophysically matched, so it is important to show the reader how this was done and what the results were.

We agree and apologize for the lack of sufficient detail in the original manuscript. We now include much more detail about the similarity rating task. The methodology and results of the behavioral rating experiments are now shown in Supplemental Figure S1. In Figure S1a, the similarity ratings are visualized on a multidimensional scaling plot. The triangular geometry for shape (blue) and sound (red) indicate that the subjective similarity was equated within each unimodal feature across individual participants. Quantitatively, there was no difference in similarity between the congruent and incongruent pairings in Figure S1b and Figure S1c prior to crossmodal learning. In addition to providing more information on these methods in the Supplemental Information, we also now provide a more detailed description of the task in the manuscript itself. For convenience, we reproduce these sections below.

“Pairwise Similarity Task. Using the same task as the stimulus validation procedure (Supplemental Figure S1a), participants provided similarity ratings for all combinations of the 3 validated shapes and 3 validated sounds (each of the six features were rated in the context of every other feature in the set, with 4 repeats of the same feature, for a total of 72 trials). More specifically, three stimuli were displayed on each trial, with one at the top and two at the bottom of the screen in the same procedure as we have used previously27. The 3D shapes were visually displayed as a photo, whereas sounds were displayed on screen in a box that could be played over headphones when clicked with the mouse. The participant made an initial judgment by selecting the more similar stimulus on the bottom relative to the stimulus on the top. Afterwards, the participant made a similarity rating between each bottom stimulus with the top stimulus from 0 being no similarity to 5 being identical. This procedure ensured that ratings were made relative to all other stimuli in the set.”– pg. 28

“Pairwise similarity task and results. In the initial stimulus validation experiment, participants provided pairwise ratings for 5 sounds and 3 shapes. The shapes were equated in their subjective similarity that had been selected from a well-characterized perceptually uniform stimulus space27 and the pairwise ratings followed the same procedure as described in ref 27. Based on this initial experiment, we then selected the 3 sounds from the that were most closely equated in their subjective similarity. (a) 3D-printed shapes were displayed as images, whereas sounds were displayed in a box that could be played when clicked by the participant. Ratings were averaged to produce a similarity matrix for each participant, and then averaged to produce a group-level similarity matrix. Shown as triangular representational geometries recovered from multidimensional scaling in the above, shapes (blue) and sounds (orange) were approximately equated in their subjective similarity. These features were then used in the four-day crossmodal learning task. (b) Behavioral results from the four-day crossmodal learning task paired with multi-echo fMRI described in the main text. Before crossmodal learning, there was no difference in similarity between shape and sound features associated with congruent objects compared to incongruent objects – indicating that similarity was controlled at the unimodal feature-level. After crossmodal learning, we observed a robust shift in the magnitude of similarity. The shape and sound features associated with congruent objects were now significantly more similar than the same shape and sound features associated with incongruent objects (p < 0.001), evidence that crossmodal learning changed how participants experienced the unimodal features (observed in 17/18 participants). (c) We replicated this learning-related shift in pattern similarity with a larger sample size (n = 44; observed in 38/44 participants). *** denotes p < 0.001. Horizontal lines denote the comparison of congruent vs. incongruent conditions. – Supplemental Figure S1

(2) The experiences through which participants learned/experienced the shapes and sounds were unclear. The methods mention that they had one minute to explore/palpate each shape and that these experiences were interleaved with other tasks, but it is not clear what the other tasks were, how many such exploration experiences occurred, or how long the total learning time was. The manuscript also mentions that participants learn the shape-sound associations with 100% accuracy but it isn't clear how that was assessed. These details are important partly b/c it seems like very minimal experience to change neural representations in the cortex.

We apologize for the lack of detail and agree with the reviewer’s suggestions – we now include much more information in the methods section. Each behavioral day required about 1 hour of total time to complete, and indeed, participants rapidly learned their associations with minimal experience. For example:

“Behavioral Tasks. On each behavioral day (Day 1 and Day 3; Figure 2), participants completed the following tasks, in this order: Exploration Phase, one Unimodal Feature 1-back run (26 trials), Exploration Phase, one Crossmodal 1-back run (26 trials), Exploration Phase, Pairwise Similarity Task (24 trials), Exploration Phase, Pairwise Similarity Task (24 trials), Exploration Phase, Pairwise Similarity Task (24 trials), and finally, Exploration Phase. To verify learning on Day 3, participants also additionally completed a Learning Verification Task at the end of the session. – pg. 27

“The overall procedure ensured that participants extensively explored the unimodal features on Day 1 and the crossmodal objects on Day 3. The Unimodal Feature and the Crossmodal Object 1-back runs administered on Day 1 and Day 3 served as practice for the neuroimaging sessions on Day 2 and Day 4, during which these 1-back tasks were completed. Each behavioral session required less than 1 hour of total time to complete.” – pg. 27

“Learning Verification Task (Day 3 only). As the final task on Day 3, participants completed a task to ensure that participants successfully formed their crossmodal pairing. All three shapes and sounds were randomly displayed in 6 boxes on a display. Photos of the 3D shapes were shown, and sounds were played by clicking the box with the mouse cursor. The participant was cued with either a shape or sound, and then selected the corresponding paired feature. At the end of Day 3, we found that all participants reached 100% accuracy on this task (10 trials).” – pg. 29

(3) I didn't understand the similarity metric used in the multivariate imaging analyses. The manuscript mentions Z-scored Pearson's r, but I didn't know if this meant (a) many Pearson coefficients were computed and these were then Z-scored, so that 0 indicates a value equal to the mean Pearson correlation and 1 is equal to the standard deviation of the correlations, or (b) whether a Fisher Z transform was applied to each r (so that 0 means r was also around 0). From the interpretation of some results, I think the latter is the approach taken, but in general, it would be helpful to see, in Methods or Supplementary information, exactly how similarity scores were computed, and why that approach was adopted. This is particularly important since it is hard to understand the direction of some key effects.

The reviewer is correct that the Fisher Z transform was applied to each individual r before averaging the correlations. This approach is generally recommended when averaging correlations (see Corey, Dunlap, & Burke, 1998). We are now clearer on this point in the manuscript:

“The z-transformed Pearson’s correlation coefficient was used as the distance metric for all pattern similarity analyses. More specifically, each individual Pearson correlation was Fisher z-transformed and then averaged (see 61).” – pg. 32

(C) From Figure 3D, the temporal pole mask appears to exclude the anterior fusiform cortex (or the ventral surface of the ATL generally). If so, this is a shame, since that appears to be the locus most important to cross-modal integration in the "hub and spokes" model of semantic representation in the brain. The observation in the paper that the perirhinal cortex seems initially biased toward visual structure while more superior ATL is biased toward auditory structure appears generally consistent with the "graded hub" view expressed, for instance, in our group's 2017 review paper (Lambon Ralph et al., Nature Reviews Neuroscience). The balance of visual- versus auditory-sensitivity in that work appears balanced in the anterior fusiform, just a little lateral to the anterior perirhinal cortex. It would be helpful to know if the same pattern is observed for this area specifically in the current dataset.

We thank the reviewer for this suggestion. After close inspection of Lambon Ralph et al. (2017), we believe that our perirhinal cortex mask appears to be overlapping with the ventral ATL/anterior fusiform region that the reviewer mentions. See Author response image 1 for a visual comparison:

Author response image 1.

The top four figures are sampled from Lambon Ralph et al (2017), whereas the bottom two figures visualize our perirhinal cortex mask (white) and temporal pole mask (dark green) relative to the fusiform cortex. The ROIs visualized were defined from the Harvard-Oxford atlas.

We now mention this area of overlap in our manuscript and link it to the hub and spokes model:

“Notably, our perirhinal cortex mask overlaps with a key region of the ventral anterior temporal lobe thought to be the central locus of crossmodal integration in the “hub and spokes” model of semantic representations.9,50 – pg. 20

(D) While most effects seem robust from the information presented, I'm not so sure about the analysis of the perirhinal cortex shown in Figure 5. This compares (I think) the neural similarity evoked by a unimodal stimulus ("feature") to that evoked by the same stimulus when paired with its congruent stimulus in the other modality ("object"). These similarities show an interaction with modality prior to cross-modal association, but no interaction afterward, leading the authors to suggest that the perirhinal cortex has become less biased toward visual structure following learning. But the plots in Figures 4a and b are shown against different scales on the y-axes, obscuring the fact that all of the similarities are smaller in the after-learning comparison. Since the perirhinal interaction was already the smallest effect in the pre-learning analysis, it isn't really surprising that it drops below significance when all the effects diminish in the second comparison. A more rigorous test would assess the reliability of the interaction of comparison (pre- or post-learning) with modality. The possibility that perirhinal representations become less "visual" following cross-modal learning is potentially important so a post hoc contrast of that kind would be helpful.

We apologize for the lack of clarity. We conducted a linear mixed model to assess the interaction between modality and crossmodal learning day (before and after crossmodal learning) in the perirhinal cortex as described by the reviewer. The critical interaction was significant, which is now clarified in the text as well as in the rescaled figure plots.

“To investigate this effect in perirhinal cortex more specifically, we conducted a linear mixed model to directly compare the change in the visual bias of perirhinal representations from before crossmodal learning to after crossmodal learning (green regions in Figure 5a vs. 5b). Specifically, the linear mixed model included learning day (before vs. after crossmodal learning) and modality (visual feature match to crossmodal object vs. sound feature match to crossmodal object). Results revealed a significant interaction between learning day and modality in the perirhinal cortex (F1,775 = 5.56, p = 0.019, η2 = 0.071), meaning that the baseline visual shape bias observed in perirhinal cortex (green region of Figure 5a) was significantly attenuated with experience (green region of Figure 5b). After crossmodal learning, a given shape no longer invoked significant pattern similarity between objects that had the same shape but differed in terms of what they sounded like. Taken together, these results suggest that prior to learning the crossmodal objects, the perirhinal cortex had a default bias toward representing the visual shape information and was not representing sound information of the crossmodal objects. After crossmodal learning, however, the visual shape bias in perirhinal cortex was no longer present. That is, with crossmodal learning, the representations within perirhinal cortex started to look less like the visual features that comprised the crossmodal objects, providing evidence that the perirhinal representations were no longer predominantly grounded in the visual modality.” – pg. 13

We note that not all effects drop in Figure 5b (even in regions with a similar numerical pattern similarity to PRC, like the hippocampus – also see Supplemental Figure S5 for a comparison for patterns only on Day 4), suggesting that the change in visual bias in PRC is not simply due to noise.

“Importantly, the change in pattern similarity in the perirhinal cortex across learning days (Figure 5) is unlikely to be driven by noise, poor alignment of patterns across sessions, or generally reduced responses. Other regions with numerically similar pattern similarity to perirhinal cortex did not change across learning days (e.g., visual features x crossmodal objects in A1 in Figure 5; the exploratory ROI hippocampus with numerically similar pattern similarity to perirhinal cortex also did not change in Supplemental Figure S4c-d).” – pg. 14

(E) Is there a reason the authors did not look at representation and change in the hippocampus? As a rapid-learning, widely-connected feature-binding mechanism, and given the fairly minimal amount of learning experience, it seems like the hippocampus would be a key area of potential import for the cross-modal association. It also looks as though the hippocampus is implicated in the localizer scan (Figure 3c).

We thank the reviewer for this suggestion and now include additional analyses for the hippocampus. We found no evidence of crossmodal integrative coding different from the unimodal features. Rather, the hippocampus seems to represent the convergence of unimodal features, as evidenced by …[can you give some pithy description for what is meant by “convergence” vs “integration”?]. We provide these results in the Supplemental Information and describe them in the main text:

“Analyses for the hippocampus (HPC) and inferior parietal lobe (IPL). (a) In the visual vs. auditory univariate analysis, there was no visual or sound bias in HPC, but there was a bias towards sounds that increased numerically after crossmodal learning in the IPL. (b) Pattern similarity analyses between unimodal features associated with congruent objects and incongruent objects. Similar to Supplemental Figure S3, there was no main effect of congruency in either region. (c) When we looked at the pattern similarity between Unimodal Feature runs on Day 2 to Crossmodal Object runs on Day 2, we found that there was significant pattern similarity when there was a match between the unimodal feature and the crossmodal object (e.g., pattern similarity > 0). This pattern of results held when (d) correlating the Unimodal Feature runs on Day 2 to Crossmodal Object runs on Day 4, and (e) correlating the Unimodal Feature runs on Day 4 to Crossmodal Object runs on Day 4. Finally, (f) there was no significant pattern similarity between Crossmodal Object runs before learning correlated to Crossmodal Object after learning in HPC, but there was significant pattern similarity in IPL (p < 0.001). Taken together, these results suggest that both HPC and IPL are sensitive to visual and sound content, as the (c, d, e) unimodal feature-level representations were correlated to the crossmodal object representations irrespective of learning day. However, there was no difference between congruent and incongruent pairings in any analysis, suggesting that HPC and IPL did not represent crossmodal objects differently from the component unimodal features. For these reasons, HPC and IPL may represent the convergence of unimodal feature representations (i.e., because HPC and IPL were sensitive to both visual and sound features), but our results do not seem to support these regions in forming crossmodal integrative coding distinct from the unimodal features (i.e., because representations in HPC and IPL did not differentiate the congruent and incongruent conditions and did not change with experience). * p < 0.05, ** p < 0.01, *** p < 0.001. Asterisks above or below bars indicate a significant difference from zero. Horizontal lines within brain regions in (a) reflect an interaction between modality and learning day, whereas horizontal lines within brain regions in reflect main effects of (b) learning day, (c-e) modality, or (f) congruency.” – Supplemental Figure S4.

“Notably, our perirhinal cortex mask overlaps with a key region of the ventral anterior temporal lobe thought to be the central locus of crossmodal integration in the “hub and spokes” model of semantic representations.9,50 However, additional work has also linked other brain regions to the convergence of unimodal representations, such as the hippocampus51,52,53 and inferior parietal lobes.54,55 This past work on the hippocampus and inferior parietal lobe does not necessarily address the crossmodal binding problem that was the main focus of our present study, as previous findings often do not differentiate between crossmodal integrative coding and the convergence of unimodal feature representations per se. Furthermore, previous studies in the literature typically do not control for stimulus-based factors such as experience with unimodal features, subjective similarity, or feature identity that may complicate the interpretation of results when determining regions important for crossmodal integration. Indeed, we found evidence consistent with the convergence of unimodal feature-based representations in both the hippocampus and inferior parietal lobes (Supplemental Figure S4), but no evidence of crossmodal integrative coding different from the unimodal features. The hippocampus and inferior parietal lobes were both sensitive to visual and sound features before and after crossmodal learning (see Supplemental Figure S4c-e). Yet the hippocampus and inferior parietal lobes did not differentiate between the congruent and incongruent conditions or change with experience (see Supplemental Figure S4).” – pg. 20

(F) The direction of the neural effects was difficult to track and understand. I think the key observation is that TP and PRh both show changes related to cross-modal congruency - but still it would be helpful if the authors could articulate, perhaps via a schematic illustration, how they think representations in each key area are changing with the cross-modal association. Why does the temporal pole come to activate less for congruent than incongruent stimuli (Figure 3)? And why do TP responses grow less similar to one another for congruent relative to incongruent stimuli after learning (Figure 4)? Why are incongruent stimulus similarities anticorrelated in their perirhinal responses following cross-modal learning (Figure 6)?

We thank the author for identifying this issue, which was also raised by the other reviewers. The reviewer is correct that the key observation is that the TP and PRC both show changes related to crossmodal congruency (given that the unimodal features were equated in the methodological design). However, the structure of the integrative code is less clear, which we now emphasize in the main text. Our findings provide evidence of a crossmodal integrative code that is different from the unimodal features, and future studies are needed to better understand the structure of how such a code might emerge. We now more clearly highlight this distinction throughout the paper:

“By contrast, perirhinal cortex may be involved in pattern separation following crossmodal experience. In our task, participants had to differentiate congruent and incongruent objects constructed from the same three shape and sound features (Figure 2). An efficient way to solve this task would be to form distinct object-level outputs from the overlapping unimodal feature-level inputs such that congruent objects are made to be orthogonal from the representations before learning (i.e., measured as pattern similarity equal to 0 in the perirhinal cortex; Figure 5b, 6, Supplemental Figure S5), whereas non-learned incongruent objects could be made to be dissimilar from the representations before learning (i.e., anticorrelation, measured as patten similarity less than 0 in the perirhinal cortex; Figure 6). Because our paradigm could decouple neural responses to the learned object representations (on Day 4) from the original component unimodal features at baseline (on Day 2), these results could be taken as evidence of pattern separation in the human perirhinal cortex.11,12 However, our pattern of results could also be explained by other types of crossmodal integrative coding. For example, incongruent object representations may be less stable than congruent object representations, such that incongruent objects representation are warped to a greater extent than congruent objects (Figure 6).” – pg. 18

“As one solution to the crossmodal binding problem, we suggest that the temporal pole and perirhinal cortex form unique crossmodal object representations that are different from the distributed features in sensory cortex (Figure 4, 5, 6, Supplemental Figure S5). However, the nature by which the integrative code is structured and formed in the temporal pole and perirhinal cortex following crossmodal experience – such as through transformations, warping, or other factors – is an open question and an important area for future investigation. Furthermore, these anterior temporal lobe structures may be involved with integrative coding in different ways. For example, the crossmodal object representations measured after learning were found to be related to the component unimodal feature representations measured before learning in the temporal pole but not the perirhinal cortex (Figure 5, 6, Supplemental Figure S5). Moreover, pattern similarity for congruent shape-sound pairs were lower than the pattern similarity for incongruent shape-sound pairs after crossmodal learning in the temporal pole but not the perirhinal cortex (Figure 4b, Supplemental Figure S3a). As one interpretation of this pattern of results, the temporal pole may represent new crossmodal objects by combining previously learned knowledge. 8,9,10,11,13,14,15,33 Specifically, research into conceptual combination has linked the anterior temporal lobes to compound object concepts such as “hummingbird”.34,35,36 For example, participants during our task may have represented the sound-based “humming” concept and visually-based “bird” concept on Day 1, forming the crossmodal “hummingbird” concept on Day 3; Figure 1, 2, which may recruit less activity in temporal pole than an incongruent pairing such as “barking-frog”. For these reasons, the temporal pole may form a crossmodal object code based on pre-existing knowledge, resulting in reduced neural activity (Figure 3d) and pattern similarity towards features associated with learned objects (Figure 4b).” – pg. 18

This work represents a key step in our advancing understanding of object representations in the brain. The experimental design provides a useful template for studying neural change related to the cross-modal association that may prove useful to others in the field. Given the broad variety of open questions and potential alternative analyses, an open dataset from this study would also likely be a considerable contribution to the field.

Author Response

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

Reviewer 1

Comment 1.1: “Did the UKB or HCHS datasets have information on accurate markers of insulin resistance, such as HbA1c or HOMA-IR (if fasting glucose was not available)? Looking at that data would allow us to determine the contribution of insulin resistance to the observed cortical phenotype.”

Reply 1.1: We appreciate the insightful suggestion from the reviewer. In response, we incorporated the HbA1c into our analysis, enhancing its sensitivity to potential effects of insulin resistance. Subsequently, our analysis was reperformed, integrating HbA1c alongside non-fasting blood glucose in the PLS. This addition did not alter our main results, i.e., that of the PLS, virtual histology, and network contextualization analysis. Notably, as a result of the inclusion of HbA1c, the second latent variable now accounted for a greater shared variance (22.13%), with HbA1c showing the highest loading among MetS component variables. The manuscript has been thoroughly revised to incorporate these results.

Comments 1.2: “(Results, p.13, 291-292) "A correlation matrix relating all considered MetS component measures is displayed in supplementary figure S12. Please clarify in this figure labels whether this was non-fasting glucose. If this is non-fasting glucose, it is not a MetS-related risk factor. The reader might be misled into thinking that fasting-glucose has a weak correlation, while its contribution (and the effect of insulin resistance) was not studied here.”

“Table S8 and Table S9: Is the glucose metric here measured following fasting? If not, this should not be listed as a metabolic syndrome criterion. Or it should be specified that it isn't fasted glucose, otherwise, it sounds misleading.”

Reply 1.2: We thank the reviewer for bringing this ambiguity to our attention. The initial analysis included only non-fasting plasma glucose in the PLS, as fasting plasma glucose data was unavailable for UKB and HCHS participants. Following your suggestion in reply 1.1, we have now incorporated HbA1c, a more indicative marker of insulin resistance. We retained non-fasting blood glucose in our analysis, recognizing its relevance as a diagnostic variable for type 2 diabetes mellitus, although it is less informative than fasting plasma glucose, HbA1c, or HOMA-IR. This decision is substantiated by the significant correlation found between non-fasting plasma glucose and HbA1c in our sample (r=.49).

To enhance clarity, we have revised the methods section to explicitly mention that the study investigates non-fasting blood glucose. The revised sentence reads: “Here, we related regional cortical thickness and subcortical volumes to clinical measurements of MetS components, i.e., obesity (waist circumference, hip circumference, waist-hip ratio, body mass index), arterial hypertension (systolic blood pressure, diastolic blood pressure), dyslipidemia (high density lipoprotein, low density lipoprotein, total cholesterol, triglycerides) and insulin resistance (HbA1c, non-fasting blood glucose).”

Additionally, we have updated the caption of supplementary figure S13 (formerly supplementary figure S12) to clearly indicate the investigation of non-fasting plasma glucose. The table detailing diagnostic MetS criteria (supplementary table S2) has also been amended to clarify the absence of fasting plasma glucose data in our study and to indicate that only data on antidiabetic therapy and diagnosis of type 2 diabetes mellitus were used as criteria for insulin resistance in the case-control analysis.

Comment 1.3: “I do not understand how the authors can claim there is a deterministic relationship there if all the results are only correlational or comparative. Can the differences in functional connectivity and white matter fiber tracts observed not be caused by the changes in cortices they relate to? How can the authors be sure the network organisation is shaping the cortical effects and not the opposite (the cortical changes influence the network organisation)? This should be further discussed or explained.”

Reply 1.3: We agree with the reviewer's comment on the non-causative nature of our data and have accordingly revised the discussion section to reflect a more cautious interpretation of our findings. We have carefully reframed our language to avoid any implications of causality, ensuring the narrative aligns with the correlational nature of our data. Nevertheless, we believe that exploring causal interpretations can offer valuable clinical insights. Therefore, while moderating our language, we have maintained certain speculative discussions regarding potential causative pathomechanistic pathways.

Comment 1.4: “The hippocampus is also an area where changes have consistently been observed. Why did the authors limit their analysis to the cortex.”

Reply 1.4: We appreciate this reviewer comment. In response, we have added volumes of Melbourne Subcortical Atlas parcels (including the hippocampus) to the analysis. Corresponding results are now shown in figure 2. The subcortical bootstrap ratios indicated that higher MetS severity was related to lower volumes across all investigated subcortical structures.

Comment 1.5: “Which field ID of the UK biobank are the measures referring to? If possible, please specify the Field ID for each of the UKB metrics used in the study.”

Reply 1.5: We thank the reviewer for the recommendation. The Field IDs used in our study are now listed in supplementary figure S1.

Comment 1.6: “Several Figures were wrongly annotated, making it hard to follow the text.”

Reply 1.6: Thank you for bringing the annotation issues to our awareness. We have thoroughly edited all annotations which should now correctly reference the figure content.

Reviewer 2

Comment 2.1: “Do the authors have the chance to see how the pattern relates to changes in cognitive function in the UKBB and possibly HCHS? This could help to provide some evidence about the directionality of the effect.” Reply 2.1: Thank you for your suggestion. We acknowledge the potential value of investigating gray matter morphometric data alongside longitudinal information on cognitive function. Although we concur with the significance of this approach, we are constrained by the ongoing processing of the UKB's imaging follow-up data and the pending release of the HCHS follow-up data. Consequently, our current analysis cannot incorporate this aspect for now. We plan to explore the relationship between MetS, cognition and brain morphology using longitudinal data as soon as it becomes available.

Comment 2.2: “Also, you could project new data onto the component and establish a link with cognition in a third sample which would be even more convincing. I can offer LIFE-Adult study for this aim.”

Reply 2.2: We are grateful for your recommendation to enhance our study's robustness by including a third sample to establish a cognitive link. While we recognize the merit of such a sensitivity analysis, we believe that our current dataset, derived from two large, independent cohorts, is sufficiently comprehensive for the scope of our current analysis. However, we are open to considering this approach in future studies and appreciate your offer of the LIFE-Adult study. We would welcome further conversation with you regarding future joint projects.

Comment 2.3: “The sentences (p.17, ll.435 ff) seem to repeat: "Interestingly, we also observed a positive relationship between cortical thickness and MetS in the superior frontal, parietal and occipital lobe. Interpretation of this result is, however, less intuitive. We also noted a positive MetS-cortical thickness association in superior frontal, parietal and occipital lobes, a less intuitive finding that has been previously reported [60,61].”

Reply 2.3: Thank you for making us aware of this duplication. We have deleted the first part of the section. It now reads “We also noted a positive MetS-cortical thickness association in superior frontal, parietal and occipital lobes, a less intuitive finding that has been previously reported.”

Comment 2.4: “I would highly appreciate empirical evidence for the claim in ll. 442 "In support of this hypothesis, the determined cortical thickness abnormality pattern is consistent with the atrophy pattern found in vascular mild cognitive impairment and vascular dementia" Considering the previous reports about the co-localization of obesity-associated atrophy and AD neurodegeneration (Morys et al. 2023, DOI: 10.3233/JAD-220535), that most dementias are mixed and that MetS probably increases dementia risk through both AD and vascular mechanisms, I feel such "binary" claims on VaD/AD-related atrophy patterns should be backed up empirically.”

Reply 2.4: Thank you for highlighting the need for clarity in differentiating between vascular and Alzheimer's dementia. We recognize the intricate overlap in dementia pathologies. Acknowledging the prevalence of mixed dementia and the influence of MetS on both AD and vascular mechanisms, we realize our original statement might have implied a specificity to vascular dementia, which was not intended.

To address your concern, we have revised our statement to avoid an exclusive focus on vascular pathology, ensuring a more balanced representation of dementia types. Additionally, we have included Morys et al. 2023 as a reference. The section now reads: “In support of this hypothesis, the determined brain morphological abnormality pattern is consistent with the atrophy pattern found in vascular mild cognitive impairment, vascular dementia and Alzheimer’s dementia.”

Comment 2.5: “I wonder how specific the cell-type results are to this covariance pattern. Maybe patterns of CT (independent of MetS) show similar associations with one or more of the reported celltypes? Would it be possible to additionally show the association of the first three components of general cortical thickness variation with the cell type densities?”

Reply 2.5: Thank you for your query regarding the specificity of the cell-type results to the observed covariance pattern. To address this, we have conducted a virtual histology analysis of the first three latent variables of the main analysis PLS. The findings of this extended analysis have been detailed in the supplementary Figure S21. The imaging covariance profile of latent variable 2 was significantly associated with the density of excitatory neurons of subtype 3. The imaging covariance profile linked to latent variable 3 showed no significant association of cell type densities. Possibly, latent variable 3 represents only a noise component as it explained only 2.12% of shared variance. We hope this addition provides a clearer understanding of the specificity of our main results.

Comment 2.6: “I agree that this multivariate approach can contribute to a more holistic understanding, yet I would like to see the discussion expanded on how to move on from here. Should we target the MetS more comprehensively or would it be best to focus on obesity (being the strongest contributor and risk factor for other "downstream" conditions such as T2DM)? A holistic approach is somewhat at odds with the in-depth investigation of specific mechanisms.”

Reply 2.6: We value your suggestion to elaborate on the implications of our findings. Our study indicates that obesity may have the most pronounced impact on brain morphology among MetS components, suggesting it as a key contributor to the clinical-anatomical covariance pattern observed in our analysis. This highlights obesity as a primary target for future research and preventive strategies. However, we believe that our results warrant further validation, ideally through longitudinal studies, before drawing definitive clinical conclusions.

Additionally, our study endorses a comprehensive approach to MetS, highlighting the importance of considering the syndrome as a whole to gain broader insights. We want to clarify, however, that such an approach is meant to complement, rather than replace, the study of individual cardiometabolic risk factors. The broad perspective our study adopts is facilitated by its epidemiological nature, which may not be as applicable in experimental settings that are vital for deriving mechanistic disease insights.

To reflect these points, we have expanded the discussion in our manuscript to include a more detailed consideration of these implications and future research directions.

Comment 2.7: “Please report the number of missing variables.”

Reply 2.7: Thank you for your request to report the number of missing variables. We would like to direct your attention to table 1, where we have listed the number of available values for each variable in parentheses. To determine the number of missing variables, one can subtract these numbers from the total sample size.

Comment 2.8: “Was the pattern similar in pre-clinical (pre-diabetes, pre-hypertension) vs. clinical conditions?“

Reply 2.8: Thank you for your interest in the applicability of our findings across different MetS severity levels. Our analysis employs a continuous framework to encompass the entire range of vascular and cardiometabolic risks, including those only mildly affected by MetS. The linear relationship we observed between MetS severity and gray matter morphology patterns, as illustrated in Figure 2d, supports the interpretation that our findings apply to the entire spectrum of MetS severities.

Comment 2.9: “How did you deal with medication (anti-hypertensive, anti-diabetic, statins..)?”

Reply 2.9: Information on medication was considered for defining MetS for the case-control sensitivity analysis but was not included in the PLS. Detailed information can be found in table 1.

Comment 2.10: “It would be really interesting to determine the genetic variations associated with the latent component. Have you considered doing a GWAS on this, potentially in the CHARGE consortium or with UKBB as discovery and HCHS as replication sample?”

Reply 2.10: Thank you for your valuable suggestion regarding the implementation of a GWAS. We agree that incorporating a GWAS would provide significant insights, but we also recognize that it extends beyond the scope of our current analysis. However, we are actively planning a follow-up analysis. This subsequent analysis will encompass a comprehensive examination of both genetic variation and imaging findings in the context of MetS.

Comment 2.11: “Please provide more information on which data fields from UKBB were used exactly (e.g. in github repository).”

Reply 2.11: We appreciate your recommendation. The details regarding the Field IDs used in our study have been included as supplementary table S1.

Reviewer 3

Comments 3.1: “After a thorough review of the methods and results sections, I found no direct or strong evidence supporting the authors' claim that the identified latent variables were related to more severe MetS to worse cognitive performance. While a sub-group comparison was conducted, it did not adequately account for confounding factors such as educational level.”

“Page 18-19 lines 431-446: the fifth paragraph in the discussion section. - As previously mentioned in the "Weaknesses" section, this study did not conduct a direct association analysis between MetS and cognitive levels without considering subgroup comparisons. Hence, I recommend the content of this paragraph warrants careful reconsideration.”

Reply 3.1: We acknowledge the reviewer's constructive feedback regarding our analysis of cognitive data. We have performed a mediation analysis relating the subject-specific clinical PLS score of latent variable 1 representing MetS severity and cognitive test performances and testing for mediating effects of the imaging PLS score capturing the MetS-related brain morphological abnormalities. The imaging score was found to statistically mediate the relationship between the clinical PLS score and executive function and processing speed, memory, and reasoning test performance. These findings highlight brain structural differences as a relevant pathomechanistic correlate in the relationship of MetS and cognition. Corresponding information can now be found in figure 3, methods section 2.6.2, result section 3.3 and discussion section 4.2.

Moreover, we would like to apologize for any confusion caused by previous unclear presentation. Our study further incorporates association analyses between MetS, brain structure, and cognition using MetS components, regional brain morphological measures, and cognitive performance data in a PLS to investigate whether cognitive measures contribute to the latent variable. These analyses were separately performed on the UK Biobank and HCHS datasets, due to their distinct cognitive assessments. We adjusted for age, sex, and education in the subgroup analyses by removing their effects from the input variables. These relationships are detailed in supplementary figures S16b and S17b, with loadings close to zero for age, sex, and education, confirming effective deconfounding.

In sum, we greatly appreciate the suggestion to conduct a mediation analysis, which has substantially enhanced the strength and relevance of our analysis.

Comment 3.2: “I would suggest the authors provide a more comprehensive description of the metrics used to assess each MetS component, such as obesity (incorporating parameters like waist circumference, hip circumference, waist-hip ratio, and body mass index) and arterial hypertension (detailing metrics like systolic and diastolic blood pressure), etc.”

Reply 3.2: Thank you for your suggestion regarding a more detailed description of the metrics for assessing each component of MetS. We would like to point out that the specific metrics used, including those for obesity (such as waist circumference, hip circumference, waist-hip ratio, and body mass index) and arterial hypertension (including systolic and diastolic blood pressure), are comprehensively detailed in table 1 of our manuscript. We hope this table provides the clarity and specificity you are seeking regarding the MetS assessment metrics in our study.

Comment 3.3: “I recommend the inclusion of an additional, detailed flowchart to further illustrate the procedure of virtual histology analysis. This would enhance the clarity of the methodological approach and assist readers in better comprehending the analysis method.”

Reply 3.3: Thank you for your suggestion. Recognizing the challenges in visually representing many of our analysis steps, we have instead supplemented our manuscript with additional references. These references provide a clearer understanding of our virtual histology approach, particularly focusing on the processing of regional microarray expression data.

The corresponding sentence reads: “Further details on the processing steps covered by ABAnnotate can be found elsewhere (https://osf.io/gcxun) [42]”

Comment 3.4: “Why were both brain hemispheres used instead of solely utilizing the left hemisphere as the atlas, especially considering that the Allen Human Brain Atlas (AHBA) only includes gene data for the right hemisphere for two subjects?”

Reply 3.4: Thank you for your query regarding our decision to use both brain hemispheres instead of solely the left hemisphere, especially considering the Allen Human Brain Atlas (AHBA) predominantly featuring gene data from the left hemisphere. Given the AHBA's limited spatial coverage of expression data in the right hemisphere, our approach involved mirroring the existing tissue samples across the left-right hemisphere boundary using the abagen toolbox,1 a practice supported by findings that suggest minimal lateralization of microarray expression.2,3 Further details are provided in previous work employing ABAnnotate.4 These studies are now referenced in our methods section.

Comment 3.5: “The second latent variable was not further discussed. If this result is deemed significant, it warrants a more detailed discussion. "

Reply 3.5: Thank you for the suggestion. We have added a paragraph to the discussion that discusses the second latent variable in greater detail. It reads: “The second latent variable accounted for 22.33% of shared variance and linked higher insulin resistance and lower dyslipidemia to lower thickness and volume in lateral frontal, posterior temporal, parietal and occipital regions. The distinct covariance profile of this latent variable, compared to the first, likely indicates a separate pathomechanistic connection between MetS components and brain morphology. Given that HbA1c and blood glucose were the most significant contributors to this variable, insulin resistance might drive the observed clinicalanatomical relationship.”

Comment 3.6: “I suggest appending positive MetS effects after "..., insular, cingulate and temporal cortices;" for two reasons: a). The "positive MetS effects" might represent crucial findings that should not be omitted. b). Including both negative and positive effects ensures that subsequent references to "this pattern" are more precise.”

Reply 3.6: We concur with the notion that the positive MetS effects should be highlighted as well. We modified the first discussion paragraph now mentioning them.

Comment 3.7: “I would appreciate further clarification on this sentence and the use of the term "uniform" in this context. Does this suggest that despite the heterogeneity in the physiological and pathological characteristics of the various MetS components (e.g., obesity, hypertension), their impacts on cortical thickness manifest similarly? How is it that these diverse components lead to "uniform" effects on cortical thickness? Does this observation align with or deviate from previous findings in the literature?”

Reply 3.7: Thank you for highlighting the ambiguity in our previous explanation. We agree that the complexity of the relationship between MetS components and brain morphology requires clearer articulation. To address this, we have revised the relevant sentence for better clarity. It now reads: „This finding indicates a relatively uniform connection between MetS and brain morphology, implying that the associative effects of various MetS components on brain structure are comparatively similar, despite the distinct pathomechanisms each component entails.“

Comment 3.8: “Figure 1 does not have the labels "c)" and "d)". ”

Reply 3.8: Thank you. We have modified figure 1 and made sure that the caption correctly references its content.

Comment 3.10: “Incorrect figure/table citation:

• Page 18 line 418: "(figure 2b and 1c)" à (figure 2b and 2c).

• Page 18 line 419: "(supplementary figures S8 and S12-13)" à (supplementary figures S11 and S1516).

• In the supplementary material, "Text S5 - Case-control analysis" section contains several figure or table citation errors. Please take a moment to review and correct them.”

Reply 3.10: Thank you for bringing this to our attention. We have corrected the figure and table citation errors.

Comment 3.11: “Page 8 line 184: The more commonly used term is "insulin resistance" rather than "insuline resistance.”

Reply 3.11: We now use “insulin resistance” throughout the manuscript.

Comment 3.12: “Nevertheless, variations in gene sets may introduce a degree of heterogeneity in the results (Seidlitz, et al., 2020; Martins et al., 2021). Consequently, further validation or exploratory analyses utilizing different gene sets can yield more compelling results and conclusions.”

Reply 3.12: Thank you for your insightful comment regarding the potential heterogeneity introduced by variations in gene sets. We agree that exploring different gene sets could indeed enhance the robustness and generalizability of our findings. However, we think conducting a comprehensive methodological analysis of the available cell-type specific gene sets is a substantial effort and warrants its own investigation to thoroughly implement it and assess its implications. We also like to highlight that we are adhering to previous practices in our analysis setup.4,5

References

(1) Markello RD, Arnatkeviciute A, Poline JB, Fulcher BD, Fornito A, Misic B. Standardizing workflows in imaging transcriptomics with the abagen toolbox. Jbabdi S, Makin TR, Jbabdi S, Burt J, Hawrylycz MJ, eds. eLife. 2021;10:e72129. doi:10.7554/eLife.72129

(2) Hawrylycz MJ, Lein ES, Guillozet-Bongaarts AL, et al. An anatomically comprehensive atlas of the adult human brain transcriptome. Nature. 2012;489(7416):391-399. doi:10.1038/nature11405

(3) Hawrylycz M, Miller JA, Menon V, et al. Canonical genetic signatures of the adult human brain. Nat Neurosci. 2015;18(12):1832-1844. doi:10.1038/nn.4171

(4) Lotter LD, Saberi A, Hansen JY, et al. Human cortex development is shaped by molecular and cellular brain systems. Published online May 5, 2023:2023.05.05.539537. doi:10.1101/2023.05.05.539537

(5) Lotter LD, Kohl SH, Gerloff C, et al. Revealing the neurobiology underlying interpersonal neural synchronization with multimodal data fusion. Neuroscience & Biobehavioral Reviews. 2023;146:105042. doi:10.1016/j.neubiorev.2023.105042

Author Response

Reviewer #1 (Public Review):

(1.1) The work by Porciello and colleagues provides scientific evidence that the acidic content of the stomach covaries with the experienced level of disgust and fear evoked by disgusting videos. The working of the inside of the gut during cognitive or emotional processes have remained elusive due to the invasiveness of the methods to study it. The major strength of the paper is the use of the non-invasive smart pill technology, which senses changes in Ph, pressure and temperature as it travels through the gut, allowing authors to investigate how different emotions induced with validated video clips modulate the state of the gut. The experimental paradigm used to evoke distinct emotions was also successful, as participants reported the expected emotions after each emotion block. While the reported evidence is correlational in nature, I believe these results open up new avenues for studying brain-body interactions during emotions in cognitive neuroscience, and future causal manipulations will shed more insight on this phenomena. Indeed, this is the first study to provide evidence for a link between gastric acidity and emotional experience beyond single patient studies, and it has major implications for the advancement of our understanding of disorders with psycho-somatic influences, such as stress and it's influence of gastritis.

1.1 First of all, we want to thank Reviewer#1 for his cogent comments and for highlighting that our findings may inspire future research on brain-body interactions. We took into the highest consideration all the remarks and changed the manuscripts accordingly.

(1.2) As for the limitations, little insight is provided on the mechanisms, time scales, and inter-individual variability of the link between gastric Ph and emotional induction. Since this is a novel phenomena, it would be important to further validate and characterize this finding. On this line, one of the most well known influences of disgust on the gut is tachygastria, the acceleration of the gastric rhythm. It would be important to understand how acid secretion by disgusting film is related to tachygastria, but authors only examine the influence of disgusting film on the normogastric frequency range.

1.2 We are aware that at the moment our data are mainly descriptive and do not provide a clear picture of the causal mechanisms. However, to deal with this outstanding issue we added a new series of analysis.

Most of the data on gastric activity come from analysis of the normogastric band. However, information about the EGG tachygastric rhythm in humans is of potential great importance. To deal with the reviewer’s comment and considering the previously published literature, we re-examined the EGG data focusing on the tachygastric rhythm. The methodology remained consistent with the process described for normogastric peak extraction but this time, we extracted the peak in the tachygastric band, specifically 0.067 to 0.167 Hz (i.e., 4–10 cpm). The ANOVA performed over the tachygastric cycle revealed a significant main effect of the type of video clip (F(4, 112) = 2.907, p = 0.025, Eta2 (partial) = 0.09). However, the Bonferroni corrected post hoc tests did not show any significant difference between the different type of emotional video clips and the neutral condition. The sole significant comparison was observed between participants viewing happy and fearful video clips, indicating that participants’ tachygastric cycles were faster when exposed to happy rather than fearful video clips (p = 0.038). For a visual representation of the outcomes, please see Fig S6.

We revised the main text (Page 17, lines: 472-482) to include this analysis. The revised text now reads as follows:

“Finally, we explored whether normogastric and/or tachygastric cycle changed in response to specific emotional experience. After checking that normogastric and tachygastric peak frequencies were normally distributed (all ps > 0.05), we ran two separate ANOVAs on the individual peak frequencies in the normogastric and tachygastric range. Each analysis had the type of video clip as within-subjects factor. The ANOVA performed on the normogastric rhythm was not significant (F(4, 44) = 1.037, p = 0.399) suggesting that the gastric rhythm did not change while participants observed the different emotional video clips. In contrast, the ANOVA performed on the tachygastric rhythm did show a significant main effect (F(4, 112) = 2.907, p = 0.025, Eta2 (partial) = 0.09). However, the only comparison that survived the Bonferroni correction was the one between happy and fearful video clips, namely participants’ tachygastric cycle was faster when they observed happy vs fearful video clips (p = 0.038) see Fig. S6 for a graphical representation of the results.”

To deal with the Reviewer’s comment, we also correlated the average pH value with the corresponding frequency of the tachygastric cycle recorded in the disgusting, happy and the fearful video clips, namely the emotions associated to changes in pH. The only significant correlation was the one found during the disgusting video clips (r= 0.435; p= 0.023, all the other rs ≤ 0.351, all the other ps ≥ 0.073). Differently from what we expected, we found a positive correlation suggesting that when participants were exposed to disgusting video clips the less acidic was the pH the higher was the frequency of the tachygastric cycle. Instead, we know from our pill data that disgusting video clips are associated to more acid values, and from literature (not replicated by us) to a faster gastric rhythm. Since we did not find strong support in the EGG analysis suggesting a relationship between the gastric rhythm and the emotional experience, we believe that additional evidence will help to clarify the relationship between pH and gastric rhythm.

(1.3) Additionally, only one channel of the electrogastrogram (EGG) was used to measure the gastric rhythm, and no information is provided on the quality of the recordings. With only one channel of EGG, it is often impossible to identify the gastric rhythm as the position of the stomach varies from person to person, yielding inaccurate estimates of the frequency of the gastric rhythm.

1.3 We agree with Reviewer 1 on this point. We acknowledge the potential limitation associated with one-channel EGG recording in our study. To deal with this remark, in a separate (ongoing) study (N# participants= 25) we recorded the electrogastrogram following the methodology outlined by Wolpert et al., 2020 published on Psychophysiology. Thus, in order to study the EGG in association to the emotional experience, we used a bipolar 4-channels montage while participants observed the same emotional video clips used in our current study (see picture below for the montage set-up).

Author response image 1 shows the 4-channels EGG bipolar recording montage reproducing the one proposed by Wolpert et al., 2020.

Author response image 1.

Then, we extracted the gastric cycle in both the normogastric and the tachygastric bands.

After checking that data were normally distributed (Kolmogorov-Smirnov ds > 0.10; ps> .20), in the case of the gastric cycle extracted in the normogastric band, we ran a repeated measures ANOVA with the type of video clip as the only within-subjects factor measured on the 5 levels (i.e. the five types of video clip: Disgusting, Fearful, Happy, Neutral, and Sad). The ANOVA shows that the gastric cycle recorded during the different video clips did not differ (F (4,96) = 0.39; p= 0.81), see the plot on Author response image 2.

Author response image 2.

Gastric cycle (normogastric band) recorded via multiple-channels electrogastrogram (EGG) during the emotional experience. The plot shows the gastric cycle extracted in the normogastric band while participants were observing the five categories of the video clips (i.e. those inducing disgust, fear, happiness, sadness and, as control, a neutral state).

We also extracted the gastric cycle in the tachygastric band, the distribution of the data was not normal in one condition (Kolmogorov-Smirnov ds > 0.27; p < 0.05), therefore we ran a Friedman ANOVA to compare the gastric cycle during the different emotional experiences. The Friedman ANOVA was not statistically significant (χ2 (4) = 2.88; p = 0.58), suggesting that, similarly to the gastric cycle extracted in the normogastric band, also the one extracted in the tachygastric band was not clearly associated to the investigated emotional states, see Author response image 3.

Author response image 3.

Gastric cycle (tachygastric band) recorded via multiple-channels electrogastrogram (EGG) during the emotional experience. The plot above shows the gastric cycle extracted in the tachygastric band while participants were observing the five categories of the video clips (i.e. those inducing disgust, fear, happiness, sadness and as control a neutral state).

Results from this control study seem to suggest that the non-significant effect of the gastric cycle was probably not due to the fact that we use a one-channel egg montage, at least for what concerns the gastric cycle extracted from the normogastric band.

For what concerns the tachygastric frequency associated to the emotional experience these results from a multi-channel EGG recording seem to go in the same direction of the normogastric one, namely no frequency of the gastric cycles recorded during the emotional video clips was different from the control condition.

The only significant difference that we found in our 1-channel EGG study was the one between the happy and the fearful video clips (see Fig. S6 contained in the supplementary materials and above). Specifically, we found that happy video clips were associated to higher gastric frequency compared to the fearful ones. However, we did not replicate these findings in our multi-channels EGG study.

Although suggestive, this evidence is not conclusive. Indeed, we are aware that a final word on the results of our multi-channel study can be said only when a larger sample is obtained.

(1.4) Finally, I believe that the results do not show evidence in favor of the discrete nature of emotions theory as they claim in the discussion. Authors chose to use stimuli inducing discrete emotions, and only asked subjective reports of these same discrete emotions, so these results shed no light on whether emotions are represented discretely vs continuously in the brain.

We revised the discussion in order to better describe our results and toned down the interpretation that the present findings directly support the discrete nature of emotions, as suggested by this Reviewer.

Now page 21&22 lines 622-631 reads as follow:

“Overall, and in line with theoretical and empirical evidence (Damasio, 1999; Harrison et al., 2010; James, 1994, Lettieri et al., 2019; Stephens et al., 2010), our findings may suggest that specific patterns of subjective, behavioural, and physiological measures are linked to unique emotional states...We acknowledge that our results, although novel, are restricted to a sample of male participants, and more importantly they need to be replicated. We also acknowledge that future studies should better investigate the mechanisms underlying the role of the pH in the emergence of specific emotion. For instance, pharmacologically manipulating stomach pH during emotional induction, not only for basic emotions but also for exploring complex emotions such as moral disgust (Rozin et al., 2009), would enable researchers to generalize these findings and examine the directionality of this relationship.”

Reviewer #2 (Public Review):

To measure the role of gastric state in emotion, the authors used an ingestible smart pill to measure pH, pressure, and temperature in the gastrointestinal tract (stomach, small bowel, large bowel) while participants watched videos that induced disgust, fear, happiness, sadness, or a control (neutral). The study has a number of strengths, including the novelty of the measurement (very few studies have ever measured these gut properties during emotion processing) and the apparent robustness of their main finding (that during disgusting video clips, participants who experienced more feelings of disgust (and to a lesser degree which might not survive more stringent multiple comparison correction, fear) had more acidic stomach measurements, while participants who experienced more happiness during the disgusting video clips had a less acidic (more basic) stomach pH. Although the study is correlational (which all discussion should carefully reflect) and is restricted to a moderately-sized, homogenous sample, the results support their general conclusion that stomach pH is related to emotion experience during disgust induction. There may be additional analyses to conduct in order for the authors to claim this effect is specific to the stomach. Nevertheless, this work is likely to have a large impact on the field, which currently tends to rely on noninvasive measures of gastric activity such as electrogastrography (which the authors also collect for comparison); the authors' minimally-invasive approach yields new and useful measurements of gastric state. These new measures could have relevance beyond emotion processing in understanding the role of gut pH (and perhaps temperature and pressure) in cognitive processes (e.g. interoception) as well as mental and physical health.

We are very grateful to Reviewer#2 for skilfully managing the paper and highlighting its strengths, particularly the innovative measurement approach and the potential implications these findings might offer for future research into the impact of gastric signals on emotional experiences and potentially on many other higher-order cognitive functions. Additionally, we would like to thank her for the highly valuable feedback. We have incorporated all the comments into the revised manuscript, aiming to enhance its quality.

Reviewer #3 (Public Review):

This study used novel ingestible pills to measure pH and other gastric signals, and related these measures to self-report ratings of emotions induced by video clips. The main finding was that when participants viewed videos of disgust, there was an association between gastric pH and feelings of disgust and fear, and (in the opposite direction) happiness. These findings may be the first to relate objective measures of gastric physiology to emotional experience. The methods open up many new questions that can be addressed by future studies and are thus likely to have an impact on the field.

We thank very much also Reviewer#3 for the accurate reading of our manuscript; for highlighting the strengths of our study; and for providing valuable feedback. Below, a point-by-point response to all the comments raised by this Reviewer. We have incorporated their comments, and we hope they are satisfied by the new version of the manuscript.

(3.1) My main concern is with the reliability of the results. The study associates many measures (pH, temperature, pressure, EGG) in stomach, small bowel, and large bowel with multiple emotion ratings. This amounts to many statistical tests. Only one of these measures (pH in the stomach) shows a significant effect. Furthermore, the key findings, as displayed in Figure 4 do not look particularly convincing. Perhaps this is a display issue, but the relations between stomach pH and Vas ratings of disgust, fear, and happiness were not apparent from the scatter plot and may be influenced by outliers (e.g., happiness).

3.1 We thank Reviewer#3 for raising this issue which was also raised by Reviewer#1 and #2, se replies above. As reported above we worked on the data analysis in order to provide more evidence supporting our claim, i.e. that pH plays a role in the emotional experience of disgust, happiness and fear. We modified Figure 4 (now 5) as also requested by Reviewer 1 and 2, and we now hope that it is clearer. We included a new analysis, in which we used all the datapoints recorded from the ingestible device and we performed a mixed models analysis with pH as dependent variable, type of video clips and number of datapoints (‘Time’) as fixed factors, and the by-subject intercepts as random effects. This analysis not only supported the results of the original one but provided evidence for a causal role of the emotional induction on the pH of the stomach. Results of this analysis are described in point 1.7 in the response to Reviewer#1 and results of the new analysis and the revised version of the main figure can be found in track change in the manuscript (Page 15&16, lines: 408-439) in the main text and copied and pasted below.

“To explore how the emotional induction could modulate the pH of the stomach and how the length of the exposure to that specific emotional induction could also play a role in modulating pH variations, we ran an additional model, Model 2. This model included all the pH datapoints registered using the Smartpill as dependent variable, the type of video clip and the number of the datapoints (“Time”) as fixed effects, and the by-subject intercepts as random effects (see Supplementary information for a detailed description of the model). Model 2 had a marginal R2 = 0.014 and a conditional R2 = 0.79. Visual inspection of the plots did reveal some small deviations from homoscedasticity, visual inspection of the residuals did not show important deviations from normality. As for collinearity (tested by means of vif function of car package), all independent variables had a GVIF^(1/(2*Df)))^2 < 10.

Type III analysis of variance of Model 2 showed a statistically significant main effect of the Time (F = 20.237, p < 0.001, Eta2 < 0.01) suggesting that independently from the type of video clip observed, the stomach pH significantly decreased as a function of the time of exposure to the induction. A significant main effect of the type of video clip was also found (F = 22.242, p < 0.001, Eta2 = 0.01) suggesting that pH of the stomach changes when participants experienced different types of emotions. In particular, post hoc analysis revealed that pH was more acidic when participants observed disgusting compared to fearful (t= -11.417; p < 0.001), happy (t= -15.510; p < 0.001) and neutral (t= -3.598; p = 0.003) video clips.

Also, pH was more acidic when participants observed fearful compared to happy (t= -4.064; p < 0.001), and less acidic compared to neutral (t= 7.835; p < 0.001) and sad scenarios (t= 9.743; p < 0.001). Finally, pH was less acidic when participants observed happy compared to neutral (t= 11.923; p < 0.001). and sad videoclips (t= 13.806; p < 0.001), see Fig.6, left panel. Interestingly, also the double interaction Time X Type of video clip was significant (F = 3.250, p = 0.0113, Eta2 < 0.01) suggesting that the time of the exposure to the induction differentially influenced the pH of the stomach depending on to the type of the observed video clip. Simple slope analysis showed that while pH did not change over time when observing disgusting (t= -1.2691; p = 0.2045) and happy (t= 0.4466; p = 0.6552) clips, it did significantly decrease over time when observing fearful (t= -4.4212; p < 0.001), sad (t= -2.0487; p = 0.0405) and neutral video clips (t= -2.7956; p = 0.0052), see Fig.6, right panel."

We believe that the new evidence reported provides support of our claims and we hope that the reviewer agrees with us. However, as we also mentioned in the paper, we are aware that replications are needed and we are already working on this.

Author Response

Reviewer #2 (Public Review):

This study aims to test the role of awake replay in short-term memory, a type of memory that operates on the timescale of seconds and minutes. Replay refers to a time-compressed burst of neuronal population activity during a particular oscillatory local field potential event in the hippocampus, called the sharp-wave ripple (SWR). SWRs are found during sleep and in the awake state and are always associated with the animal being quiescent. The paper compares results from three different behavioral tasks ranging in memory requirements and memory timescales. First, rats were trained on either a spatial match-to-sample task (MTS), a non-match-to-sample task (NMTS), or a task requiring the memorization of sequences (maze arms to be visited in a specific temporal order). In this initial training phase, the animals were allowed to learn the maze structure and the rules governing these tasks for all these behavioral paradigms. Then, awake sharp-SWRs were disrupted as the animal performed these tasks (both during instruction and test phases) via an online detection system combined with closed-loop electrical stimulation of the ventral hippocampal commissure. Notably, this manipulation appeared not to affect performance in all three tasks, as determined using various behavioral parameters. Trials with no stimulation or delayed stimulation serve as controls. Thus, the authors conclude that awake SWRs are not involved in these short-term memory-guided behaviors. I do have a few comments that the authors should discuss or address:

(1) This study adds to a large number of studies investigating the role of awake SWRs in spatial learning and memory tasks. The results of these previous studies are quite contradictory and range from awake SWRs are not crucial in guiding decisions at all to SWRs are only essential during task rule learning to SWRs do guide behavior. Could the authors comment on these seemingly contradictory results? Why are these experiments now the right ones?

The reviewer is correct that there is a large body of literature investigating awake SWRs. Most commonly, interpretations about the role of SWRs and associated replay are made based on correlations of their occurrence with behavior. These correlations do, however, not necessarily indicate that SWRs contribute to a particular cognitive process. That is why interventional studies like ours are important to clarify the contribution of SWRs.

The acquisition of a novel task involves a number of cognitive processes, including short- and long-term memory, building a map of the environment, exploration of the solution space and incorporating (non-)rewarding feedback. Based on available evidence, SWRs could contribute to many of these processes. Our experiments were designed to exclude the long-term memory aspect and focus on the memorization of locations on a short time-scale which as we now demonstrate is not dependent on SWRs. Since the use of short-term spatial memory is one of the possible explanations for the learning deficit seen by Jadhav et al. (2012) following SWR disruption in an alternation task, our results may also narrow down the exact contribution of SWR in these studies.

(2) None of the experiments presented here test the role of replay. I suggest making this distinction in the paper and the title clear. As the results are presented now, is it possible that the SWR content is not affected sufficiently to have a behavioral effect or that there is a bias towards detecting specific SWRs, e.g., longer SWRs?

The reviewer is right that our experiments do not say anything about replay directly. We adapted the text to make this distinction clear.

We address the possibility that SWR content may not be disrupted sufficiently to cause a behavioral effect in response to recommendation 1.

Reviewer #3 (Public Review):

In this manuscript, the authors seek to shed light on the role of awake hippocampal replay during memory tasks that are claimed to be short-term memory. For this, they make use of a real-time detection and disruption system of awake hippocampal ripples, which are used as a proxy for awake neuronal replay. The manuscript describes extensively the tasks as well as the disruption system and controls used during the experiments. The authors present numerous and solid analyses of the behavioral data acquired during the tasks. Nonetheless, the current version of the manuscript is lacking a more complete discussion in which the results are contrasted to previous similar findings, as well as mentioning the role of the awake ripple in the stabilization of hippocampal maps. Some extra analyses are also suggested below. The manuscript would also be enriched if the authors suggested alternative mechanisms for memory rehearsal. Finally, some claims of "we are first" seem inappropriate when compared to the previous literature.

Major comments:

How does one define short-term memory (STM) in rodents? The examples and papers cited in the first paragraphs refer mostly to human working memory tasks, from which it is known that a non- rehearsed STM lasts typically 20-30 seconds. Could the authors mention how this concept is translated to rodents? Could you clarify until what point memory is considered STM and what is the criteria to consider it has turned into long-term memory or when is it simply working memory or habit/skill?

We agree with the reviewer that the definition of short-term memory is fluid and may differ between researchers and model systems. To avoid confusion, we reframed our study in a different context and hope that this makes the timeframes we are talking about clearer.

Further, why should these tasks be classified as testing STM while Jadhav et al. tasks are working memory or as they now mention in this article rule learning?

Note that short-term memory and working memory are closely related, but not identical, concepts. Whereas short-term memory refers to the retaining of information for a short period of time, working memory is generally considered to also include some manipulation of that information. Unfortunately, in the rodent literature, (spatial) working memory and short-term memory are often used interchangeably.

Many (animal) spatial memory tasks do not test a single cognitive faculty, but likely involve a combination of short-term memory, working memory, and rule learning (among other abilities) to acquire or solve the task. As such, an unequivocal classification of behavioral tasks is not generally possible. For example, in the continuous version of the spatial alternation task used in Jadhav et al., animals may learn the rule “if I in the center arm and I came from the left goal arm, then I will next find reward in the right goal arm”. The execution of this rule would require maintaining in (short-term) memory the most recent visited goal arm. Alternatively, animals may learn the rule to turn left twice and right twice to successfully perform the task.

One of our goals in our study was to attempt to isolate rule learning components and short-term memory components in our tasks (to be clear: we are not claiming that our tasks are pure short- term memory tasks).

We have rewritten the introduction to reframe our study, which hopefully clarifies the points above.

In humans, the retention of memory after a certain time is achieved by retrieving a long-term memory. How do we know if the considerable training the rats received has not allowed the use of a long-term memory strategy which allows the rats to perform well even in the absence of rehearsal (replay)? These are conceptual explanations that would help understand the key concept of STM in greater detail.

Our experiments aimed to distinguish between the process of learning general task rules through training and the need to retain information specific to each trial or session. For example, in the NMTS task, the animals may have a long-term memory of the overall task design, but they cannot anticipate or recall in advance which specific arms will be baited in the instruction phase since they vary from one trial to another. Therefore, to complete a trial successfully, the animals must have formed some type of (short-term) memory of the instruction arms and/or of the arms that still need to be visited in the test phase. Although extended training may have resulted in a more optimized and less demanding strategy to memorize the necessary information, evidence in the literature indicates that even then (for this particular task), a functional hippocampus is required (Sasaki 2021). The question we address in our experiments is whether hippocampal SWRs (and by association, replay) are instrumental in the formation or maintenance of this memory, whether through rehearsal or other mechanisms. The rewritten introduction explains these concepts more clearly.

Further, claims of "first" should be adjusted, since I do not see a large difference between the w (m) maze of Jadhav and these tasks. The main difference between the two projects would rather be that Jadhav tests when animals are still newer to the task while here overtrained animals are used. In Jadhav, it's unlikely that just rule learning is affected since the inbound component is not affected by disruption, which also tests rule learning. Therefore, it is still likely that the effect seen in Jadhav et al is a deficit in working memory/short-term memory. And here it is more likely, that no effect was seen since with overtrained animals other strategies (cortical, striatal, etc) were used. The authors should compare in more detail how overtrained animals were in these different projects as well as in the articles they cite for replay analysis.

The training of the animals on the general task rules prior to SWR disruption manipulations is by design, as it better isolates the short-term memory demands required to solve the task in each trial/session. In our tasks, the rats are required to memorize a randomly chosen combination of goal arms on each day (MTS & SEQ task) or in every trial (NMTS task). Unlike the continuous alternation paradigm used by Jadhav et al. (2012), our tasks can not be solved using a stereotypical or habitual (striatal) strategy that is acquired through extended training. We can not exclude that the rats acquired an optimized and less cognitively demanding strategy that is mainly dependent on cortical structures outside the hippocampus, however evidence in the literature still indicates the requirement for a functional hippocampus (Sasaki, 2021; Okaichi and Oshima 1990; Blokland, Honig, and Raaijmakers, 1992).

The reviewer is correct that the inbound component of the continuous alternation task in Jadhav et al. (2012) can be considered rule learning and was not affected by SWR disruption. However, we do not believe that this should be generalized to all rule learning and it is very well conceivable that SWRs contribute to the learning of more complex rules that also feature ambiguity (such as the outbound component in the continuous alternation task). We elaborate on these points in the discussion (lines 425-455).

The main conclusion of the authors is that hippocampal replay is not the rehearsal mechanism expected in STM given that its disruption doesn't lead to behavioral changes. Could the authors hypothesize in their discussion what other neural mechanisms different from hippocampal replay may be involved in this rehearsal?

Thank you for this suggestion. We added an extra paragraph speculating on this aspect (lines 499- 518).

The discussion also lacks closure with respect to how the findings fit in the study of STM in human memory. This would make the article more interesting to a larger audience and highlight its translational aspect.

We agree with the reviewer and added our insight to the discussion.

The results describe deeply the behavioral performance of the rats and the validation of the ripple detection/disruption system. However, one important aspect missing is how the hippocampal activity and its encoding of space may be affected by the awake ripple disruption. The authors don't cite the work by Roux et al., Nature Neuroscience. 2017 where optogenetic stimulation of hippocampal neurons provided evidence that neuronal activity associated with awake hippocampal ripples during goal-directed behavior is required for both stabilizing and refining hippocampal place fields, while memory performance was not affected during ripple-locked stimulations compared to a ripple-delayed stimulation control (See supplementary Figure 7 of the mentioned article). I would like the authors to comment on their own findings and contrast them with those of Roux et al.

We agree that it is interesting to include the results of Roux et al. in our discussion (lines 470 and 463-466).

Line 64: Could the authors clarify what they mean by "indirect" causal evidence when discussing the contribution of papers by Jadhav, Igata, and Fernandez? Is it the fact that rodents' learning speed changed instead of showing a complete absence of learning? Or is it the fact that the disruption/prolongation is done on the hippocampal ripple and not strictly in the replay sequence?

We apologize for the confusion and rewrote large parts of the introduction to clarify the contributions of the papers by Jadhav, Igata, and Fernandez and the difference with what our manipulations contribute. In the process, we removed the phrase ‘indirect causal evidence’.

I would also highlight this latter difference, given that the above-mentioned authors describe their methodological approaches in terms of ripples and not in terms of replay content. For example, the use of "replay" instead of "ripple" in Line 61 results in methodological inaccurate terms such as replay disruption and replay prolongation.

Thank you for pointing this out. We adapted the manuscript to always use ‘ripple’ or ‘sharp-wave ripple’ (SWR) when describing our results.

Despite its apparent lack of statistical significance, the reported mean ripple detection rate during the trial and non-trial periods tend to be always higher in the disruption condition of all tasks by observing the median of the boxplots in Figure 1J, Figure 2H, and Figure 3J. It is worth investigating this further using the same linear regression method as Girardeau et al. Journal of Neuroscience, 2014 which may reduce the variability and allow comparing slopes of a cumulative number of ripples over time. This may reveal a compensatory homeostatic-like increase in the rate of ripples during the disrupted sessions, which may suggest a need for the ripple/replay occurrence in spite of it not having an effect on the rats' performance during the task.

The reviewer makes an interesting observation and we appreciate the suggestion for further investigation. However, note that a clear trend for higher ripple rates in disruption trials/sessions is not present when comparing to non-stimulated control trials/session. Part of the variability in the observed ripple rates is likely due to the variability in the animals’ behavioral state (e.g., moving, pausing but alert, grooming, consuming reward) and the corresponding varying propensity for SWRs to occur. The behavioral variability makes application of the linear regression approach of Girardeau et al. (2014) not straightforward (note that Girardeau et al. looked at SWRs during sleep). For these reasons, we have decided to not further look into the potential disruption-induced increase of the SWR rate.

In line 425, the authors report a median relative delay of 52.9 of their disruption system. Such a value would indicate that only around 47% of the ripple is being blocked. Is there any data from the authors or others that could reassure the reader that the 52.9% of the ripple that "leaks" is not enough for the replay phenomenon to occur? Considering the findings of Fernandez-Ruiz et al. 2019 on large-duration ripples, could the authors report the relative delay for both short and long ripples (>100 ms) separately?

The reviewer is correct that the initial part (~35 ms) of SWRs remains intact, which is inherent to the online detection and disruption approach. In relative terms, a larger fraction of long SWRs is disrupted. As requested, we have adapted figure 4c to separately show the distribution of relative detection delays for long (duration >100ms) and short SWRs.

As we and others have shown, the electrical stimulation temporarily suppresses spiking activity in CA1 and thus abruptly interferes with any ongoing replay, but any beginning of replay sequences before the stimulation will not be affected. Previous studies that use the same methodology to disrupt SWRs reported a behavioral performance deficit despite the detection delays (Michon et al. 2019; Girardeau et al. 2009; Jadhav et al. 2012). This suggests that the initial part of SWRs (and replay) is not sufficient to support the behavior. The delays in the current study are quantitatively similar to what we have reported before in Michon et al. (2019) and thus we are confident that we should have been able to observe a behavioral effect if present. We now elaborate on this topic in the Discussion (lines 489-498) .

Line 494: The authors define long ripples as (>120 ms) but this doesn't coincide with the 100ms threshold from Fernandez Ruiz et al. 2019.

Thank you for pointing this out, it is corrected in the text both in the Results (line 389) and Discussion (line 486).

The online ripple detector used filtered the traces in the 135-255 Hz range. This is a narrower frequency range compared to online detectors used by Jadhav et al. 2012 (100-400 Hz) and Fernandez-Ruiz et al. 2019 (80-300 Hz). What motivated the use of this narrow range? Would the omittance of ripples below 135 Hz have implications in the results? Could the authors add to the supplement a figure similar to Figure 4B (FDR vs TPR) using a wider frequency range similar to the authors above in the offline detection of ripples?

The frequency of hippocampal ripple oscillation in rat generally lies in the range of 160-225 Hz (Buzsaki, 1992). We have added a power spectrum in Figure 1d that confirms this frequency range in our experiments. Filters that include frequencies below this range (as in the studies referenced by the reviewer) likely also pass through high-frequency gamma oscillations, and filters that include frequencies above this range likely also pass through multi-unit spiking activity. The challenge for a real-time ripple detection system is to design a filter that has an acceptable trade-off between filtering in a specific (narrow) frequency range and introducing a long delay. In our study, we specifically designed a filter that is specific to the ripple frequency band and still has an acceptable low delay.

It is unclear what criterion was used to train the rats in the NMTS task. Line 216 specifies a learning criterion of 80% fully correct trials in one session for three days in a row, while the methods in line 852 mention an average performance below 50% for at least three days in a row.

Thank you for pointing this out. We corrected the learning criterium description in the results section (lines 108-110) to match the description in the Methods section.

In the methods section, it is not mentioned if there was a specific region in the cortex where the tetrode was placed (Line 908).

The detections in this tetrode were used to mark events as "false positives". The authors should be careful in line 933 when they make the statement "ripples are not present in the cortex". There have been recent publications that challenge this affirmation. See Khodagholy, Science. 2017, Nitzan, Nature Comm. 2020.

Thank you for pointing this out. We have added the cortical region in the methods (line 882) and clarified that, as far as we know, no ripples in that part of the cortex (parietal associate cortex) have been described that are synchronous with hippocampal ripples.

Author Response

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

eLife assessment

This study presents a useful characterization of the biochemical consequences of a disease-associated point mutation in a nonmuscle actin. The study uses solid and well-characterized in vitro assays to explore function. In some cases the statistical analyses are inadequate and several important in vitro assays are not employed.

Public Reviews:

Reviewer #1 (Public Review):

Strengths:

The authors first perform several important controls to show that the expressed mutant actin is properly folded, and then show that the Arp2/3 complex behaves similarly with WT and mutant actin via a TIRF microscopy assay as well as a bulk pyrene-actin assay. A TIRF assay showed a small but significant reduction in the rate of elongation of the mutant actin suggesting only a mild polymerization defect.

Based on in silico analysis of the close location of the actin point mutation and bound cofilin, cofilin was chosen for further investigation. Faster de novo nucleation by cofilin was observed with mutant actin. In contrast, the mutant actin was more slowly severed. Both effects favor the retention of filamentous mutant actin. In solution, the effect of cofilin concentration and pH was assessed for both WT and mutant actin filaments, with a more limited repertoire of conditions in a TIRF assay that directly showed slower severing of mutant actin.

Lastly, the mutated residue in actin is predicted to interact with the cardiomyopathy loop in myosin and thus a standard in vitro motility assay with immobilized motors was used to show that non-muscle myosin 2A moved mutant actin more slowly, explained in part by a reduced affinity for the filament deduced from transient kinetic assays. By the same motility assay, myosin 5A also showed impaired interaction with the mutant filaments.

The Discussion is interesting and concludes that the mutant actin will co-exist with WT actin in filaments, and will contribute to altered actin dynamics and poor interaction with relevant myosin motors in the cellular context. While not an exhaustive list of possible defects, this is a solid start to understanding how this mutation might trigger a disease phenotype.

We thank the reviewer for the positive evaluation of our work.

Weaknesses:

• Potential assembly defects of the mutant actin could be more thoroughly investigated if the same experiment shown in Fig. 2 was repeated as a function of actin concentration, which would allow the rate of disassembly and the critical concentration to also be determined.

The polymerization rate of individual filaments observed in TIRFM experiments showed only minor changes, as did the bulk-polymerization rate of 2 µM actin in pyrene-actin based experiments. Therefore, we decided not to perform additional pyrene-actin based experiments, in which we titrate the actin concentration, as we expect only very small changes to the critical concentration. Instead, we focused on the disturbed interaction with ABPs, as we assume these defects to be more relevant in an in vivo context. Using pyrene-based bulkexperiments, we did determine the rate of dilution-induced depolymerization of mutant filaments and compare them with the values determined for wt (Figure 5A, Table 1).

• The more direct TIRF assay for cofilin severing was only performed at high cofilin concentration (100 nM). Lower concentrations of cofilin would also be informative, as well as directly examining by the TIRF assay the effect of cofilin on filaments composed of a 50:50 mixture of WT:mutant actin, the more relevant case for the cell.

The TIRF assay for cofilin severing was performed initially over the cofilin concentration range from 20 to 250 nM. The results obtained in the presence of 100 nM cofilin allow a particularly informative depiction of the differences observed with mutant and WT actin. This applies to the image series showing the changes in filament length, cofilin clusters, and filament number as well as to the graphs showing time dependent changes in the number of filaments and total actin fluorescence. We have not included the results for a 50:50 mixture of WT:mutant actin because its attenuating effect is documented in several other experiments in the manuscript.

• The more appropriate assay to determine the effect of the actin point mutation on class 5 myosin would be the inverted assay where myosin walks along single actin filaments adhered to a coverslip. This would allow an evaluation of class 5 myosin processivity on WT versus mutant actin that more closely reflects how Myo5 acts in cells, instead of the ensemble assay used appropriately for myosin 2.

Our results with Myo5A show a less productive interaction with mutant actin filaments as indicated by a 1.7-fold reduction in the average sliding velocity and an increase in the optimal Myo5A-HMM surface density from 770 to 3100 molecules per µm2. These results indicate a reduction in binding affinity and coupling efficiency, with a likely impact on processivity. We expect only a small incremental gain in knowledge about the extent of changes by performing additional experiments with an inverted assay geometry, given that under physiological conditions the motor properties of Myo5A and other cytoskeletal myosins are modulated by other factors such as the presence of tropomyosin isoforms and other actin binding proteins.

Reviewer #2 (Public Review):

Greve et al. investigated the effects of a disease-associated gamma-actin mutation (E334Q) on actin filament polymerization, association of selected actin-binding proteins, and myosin activity. Recombinant wildtype and mutant proteins expressed in sf9 cells were found to be folded and stable, and the presence of the mutation altered a number of activities. Given the location of the mutation, it is not surprising that there are changes in polymerization and interactions with actin binding proteins. Nevertheless, it is important to quantify the effects of the mutation to better understand disease etiology.

We thank the reviewer for the positive evaluation of our work.

Some weaknesses were identified in the paper as discussed below.

• Throughout the paper, the authors report average values and the standard-error-of-the-mean (SEM) for groups of three experiments. Reporting the SEM is not appropriate or useful for so few points, as it does not reflect the distribution of the data points. When only three points are available, it would be better to just show the three different points. Otherwise, plot the average and the range of the three points.

We have gone through the manuscript carefully to correct any errors in the statistics, as explained below.

Figure 1B, 5B, 5C, 5D, 8D, 9B, and 8 – figure supplement 2 all show the mean ± SD, as also correctly reported for Figure 8E and 8F in the figure legend. The statement, that these figures show the mean ± SEM was inaccurate. We corrected this mistake for all the listed figures. Furthermore, we now give the exact N for every experiment in the figure legend.

Figure 2C, 2E, 2F, 4B, 5A, 6B-E showed the mean ± SEM. As suggested by the reviewer, we corrected the figures to show the mean ± SD.

We still refer to the mean ± SEM in Figure 2B, where elongation rates for more than 100 filaments were recorded, and in Figure 8B, where sliding velocities for several thousand actin filaments were measured.

• The description and characterization of the recombinant actin is incomplete. Please show gels of purified proteins. This is especially important with this preparation since the chymotrypsin step could result in internally cleaved proteins and altered properties, as shown by Ceron et al (2022). The authors should also comment on N-terminal acetylation of actin.

We added an additional figure showing the purification strategy for the recombinant cytoskeletal γ –actin WT and p.E334Q protein with exemplary SDS-gels from different stages of purification (Figure 1 – figure supplement 1).

In a previous paper, we reported the mass spectrometric analysis of the post-translational modifications of recombinant human β- and γ-cytoskeletal actin produced in Sf-9 cells. (Müller et al., 2013, Plos One). Recombinant actin showing complete N-terminal processing resulting in cleavage of the initial methionine and acetylation of the following aspartate (β-actin) or glutamate (γ-actin) is the predominant species in the analyzed preparations (> 95 %). While the recombinant actin in the 2013 study was produced tag-free and purified by affinity chromatography using the column-immobilized actin-binding domain of gelsolin (G4-G6), we have no reason to assume that the purification strategy using the actin-thymosin-β4 changes the efficiency of the N-terminal processing in Sf-9 cells. This is supported by our, yet unpublished, mass-spectrometric studies on recombinant human α-cardiac actin purified using the actin- thymosin-β4 fusion construct, which revealed actin species with an acetylated aspartate-3. This N-terminal modification of α-cardiac actin is catalyzed by the same actinspecific acetyltransferase (NAA80) as the acetylation of asparate-2 or glutamate-2 in cytoskeletal actin isoforms (Varland et al., 2019, Trends in Biochemical Sciences). Furthermore, additional studies that used the actin-thymosin-β4 fusion construct for the production of recombinant human cytoskeletal actin isoforms in Pichia pastoris reported robust N-terminal acetylation, when the actin was co-produced with NAA80 (In contrast to Sf-9 cells, NAA80 is not endogenously expressed in Pichia pastoris) (Hatano et al., 2020, Journal of Cell Science).

We therefore, added the following statement to the manuscript:

“Purification of the fusion protein by immobilized metal affinity chromatography, followed by chymotrypsin–mediated cleavage of C–terminal linker and tag sequences, results in homogeneous protein without non–native residues and native N-terminal processing, which includes cleavage of the initial methionine and acetylation of the following glutamate. “

• The authors do not use the best technique to assess actin polymerization parameters. Although the TIRF assay is excellent for some measurements, it is not as good as the standard pyrene-actin assays that provide critical concentration, nucleation, and polymerization parameters. The authors use pyrene-actin in other parts of the paper, so it is not clear why they don't do the assays that are the standard in the actin field.

The polymerization rate of individual filaments observed in TIRFM experiments showed only minor changes, as did the bulk-polymerization rate of 2 µM actin in pyrene-actin based experiments. Therefore, we decided not to perform additional pyrene-actin based experiments, in which we titrate the actin concentration, as we expect only very small changes to the critical concentration. Instead, we focused on the disturbed interaction with ABPs, as we assume these defects to be more relevant in an in vivo context. Using pyrene-based bulkexperiments, we did determine the rate of dilution-induced depolymerization of mutant filaments and compare them with the values determined for WT (Figure 5A, Table 1).

• The authors' data suggest that, while the binding of cofilin-1 to both the WT and mutant actins remains similar, the major defect of the E334Q actin is that it is not as readily severed/disassembled by cofilin. What is missing is a direct measurement of the severing rate (number of breaks per second) as measured in TIRF.

The severing rate as measured in TIRF is dependent on a number of parameters in a nonlinear manner. Therefore, we opted to show the combination of images directly showing the progress of the reaction and graphs summarizing the concomitant changes in cofilin clusters, actin filaments, actin-related fluorescence intensity and cofilin-related fluorescence intensity.

• Figure 4 shows that the E334Q mutation increases rather than decreases the number of filaments that spontaneously assemble in the TIRF assay, but it is unclear how reduced severing would lead to increased filament numbers, rather, the opposite would be expected. A more straightforward approach would be to perform experiments where severing leads to more nuclei and therefore enhances the net bulk assembly rate.

Figure 4 shows polymerization experiments that were started from ATP-G-actin in the presence of cofilin-1. These experiments show clearly that, especially at the higher cofilin-1 concentration (100 nM), the filament number is strongly increased in experiments performed with mutant actin. Inspection of the corresponding videos of these TIRFM experiments suggest that the increased number of filaments must result from an increased number of de novo nucleation events and not primarily from a mutation-induced change in severing susceptibility. The observation of a cofilin-stimulated increase in the de novo nucleation efficiency of actin was initially described by Andrianantoandro & Pollard (2006, Molecular Cell) using TIRFMbased experiments and is thought to arise from the stabilization of thermodynamically unfavorable actin dimers and trimers by cofilin. While the exact role of this cofilin-mediated effect in vivo is not completely clear, it is thought to contribute to cofilin-meditated actin dynamics synergistically with cofilin-mediated severing. It is therefore necessary, to clearly distinguish between the two effects of cofilin in vitro: stimulation of de novo nucleation and stimulation of filament disassembly. Our data indicated that the E334Q mutation affects these two effects differentially, as we state in the abstract and in the discussion.

Abstract: “E334Q differentially affects cofilin-mediated actin dynamics by increasing the rate of cofilin-mediated de novo nucleation of actin filaments and decreasing the efficiency of cofilin-mediated filament severing.”

Discussion: “Cofilin-mediated severing and nucleation were previously proposed to synergistically contribute to global actin turnover in cells (Andrianantoandro & Pollard, 2006; Du & Frieden, 1998). Our results show that the mutation affects these different cofilin functions in actin dynamics in opposite ways. Cofilin-mediated filament nucleation is more efficient for p.E334Q monomers, while cofilin-mediated severing of filaments containing p.E334Q is significantly reduced. The interaction of both actin monomers and actin filaments with ADF/cofilin proteins involves several distinct overlapping reactions. In the case of actin filaments, cofilin binding is followed by structural modification of the filament, severing and depolymerizing the filament (De La Cruz & Sept, 2010). Cofilin binding to monomeric actin is followed by the closure of the nucleotide cleft and the formation of stabilized “long-pitch” actin dimers, which stimulate nucleation (Andrianantoandro & Pollard, 2006)”.

We interpret the reviewer's suggestion to mean that additional pyrene-actin-based bulk polymerization experiments should be performed to investigate the bulk-polymerization rate of ATP-G-actin in the presence of cofilin-1. In our understanding, these experiment would not provide additional value as 1) An observed increase of the bulk-polymerization rate cannot be directly correlated to a change of the efficiency of de novo nucleation or severing and 2) the effect of the mutation on cofilin-mediated filament disassembly was extensively analyzed in other experiments starting from preformed actin filaments. Moreover, our results are consistent with in silico modelling and normal mode analysis of the WT and mutant actin-cofilin complex.

• Figure 5 A: in the pyrene disassembly assay, where actin is diluted below its critical concentration, cofilin enhances the rate of depolymerization by generating more free ends. The E334Q mutation leads to decreased cofilin-induced severing and therefore lower depolymerization. While these data seem convincing, it would be better to present them as an XY plot and fit the data to lines for comparison of the slopes.

We now present the data as suggested by the reviewer. Furthermore, we determined the apparent second-order rate constant for cofilin-induced F-actin depolymerization (kc) to quantify the observed differences between WT, mutant and heterofilaments, as suggested by the reviewer.

The paragraph describing these results was changed accordingly:

“The observed rate constant values are linearly dependent on the concentration of cofilin–1 in the range 0–40 nM, with the slope corresponding to the apparent second– order rate constant (kC) for the cofilin-1 induced depolymerization of F–actin. In experiments performed with p.E334Q filaments, the value obtained for kC was 4.2-fold lower (0.81 × 10-4 ± 0.08 × 10-4 nM-1 s-1) compared to experiments with WT filaments (3.42 × 10-4 ± 0.22 × 10-4 nM-1 s-1). When heterofilaments were used, the effect of the mutation was reduced to a 2.2-fold difference compared to WT filaments (1.54 × 10-4 ± 0.11 × 10-4 nM-1 s-1).”

• Figure 5 B and C: the cosedimentation data do not seem to help elucidate the underlying mechanism. While the authors report statistical significance, differences are small, especially for gel densitometry measurements where the error is high, which suggests that there may be little biological significance. Importantly, example gels from these experiments should be shown, if not the complete set included in the supplement. In B, the higher cofilin concentrations would be expected to stabilize the filaments and thus the curve should be Ushaped.

We do not completely agree with the reviewer on this point. We think the co-sedimentation experiments are useful, as they show that cofilin-1 efficiently binds to mutant filaments, but is less efficient in stimulating disassembly in these endpoint-experiments. This information is not provided by the analysis of the effect of cofilin-1 on the bulk-depolymerization rate and adds to our understanding of the defect of the actin-cofilin interaction for the mutant.

While we agree with the reviewer on the point that co-sedimentation experiments must be repeated several times to produce reliable data, we cannot fully grasp the reasoning behind the statement “While the authors report statistical significance, differences are small, especially for gel densitometry measurements where the error is high, which suggests that there may be little biological significance.”. We interpret this statement as advice to be cautious when extrapolating the observed perturbances of cofilin-mediated actin dynamics in vitro to the in vivo context. We think we are cautious about this throughout the manuscript.

The author expects a U-shape curve, as high cofilin concentrations are reported to stabilize actin filaments by completely decorating the filament before severing-prone boundaries between cofilin-decorated and undecorated regions are generated. We have also performed these experiment with cytoskeletal β-actin and human cofilin-1 and never observed this U shape. This indicates that significant filament disassembly also happens at high cofilin concentrations, most likely directly after mixing of F-actin and cofilin. We cannot rule out that the incubation time plays an important role and that the U-shape only appears after longer incubation times. We also want to direct the reviewer to the publication “A Mechanism for Actin Filament Severing by Malaria Parasite Actin Depolymerizing Factor 1 via a Low Affinity Binding Interface” (Wong et al. 2013, JBC) in which comparable co-sedimentation experiments were performed (Figure 5E-G) with rabbit skeletal α-actin and human cofilin-1 and also no Ushaped curves were observed, even at higher molar excess of cofilin-1 compared to our experiments and with longer incubation times (1 hour vs. 10 minutes).

We now included an exemplary gel showing co-sedimentation experiments performed with WT, mutant actin and different concentrations of cofilin at pH 7.8 in the manuscript (Figure 5 – figure supplement 2)

• Figure 5 D: these data show that the binding of cofilin to WT and E334Q actin is approximately the same, with the mutant binding slightly more weakly. It would be clearer if the two plots were normalized to their respective plateaus since the difference in arbitrary units distracts from the conclusion of the figure. If the difference in the plateaus is meaningful, please explain.

As suggested by the reviewer, we normalized the data for a better understanding of the message conveyed.

• Figure 6: It is assumed that the authors are trying to show in this figure that cofilin binds both actins approximately the same but does not sever as readily for E334Q actin. The numerous parameters measured do not directly address what the authors are actually trying to show, which presumably is that the rate of severing is lower for E334Q than WT. It is therefore puzzling why no measurement of severing events per second per micron of actin in TIRF is made, which would give a more precise account of the underlying mechanism.

The severing rate as measured in TIRF is dependent on a number of parameters in a nonlinear manner. Therefore, we opted to show the combination of images directly showing the progress of the reaction and graphs summarizing the concomitant changes in cofilin clusters, actin filaments, actin-related fluorescence intensity and cofilin-related fluorescence intensity.

• Actin-activated steady-state ATPase data of the NM2A with mutant and WT actin would have been extremely useful and informative. The authors show the ability to make these types of measurements in the paper (NADH assay), and it is surprising that they are not included for assessing the myosin activity. It may be because of limited actin quantities. If this is the case, it should be indicated.

Indeed, the measurement of the steady-state actin-activated ATPase with recombinant cytoskeletal actin is very material-intensive and therefore costly, as a complete titration of actin is required for the generation of meaningful data. Since the vast majority of our assays involving a myosin family member were performed with NM2A-HMM, we decided to perform a full actin titration of the steady-state actin-activated ATPase of NM2A-HMM with WT and mutant filaments. The results of these experiments are now shown in Figure 8C. The panel showing the results used for determining the dissociation rate constants (k-A) for the interaction of NM2C-2R with p.E334Q or WT γ –actin in the absence of nucleotide was moved to the supplement (Figure 8 – figure supplement 2).

We added the following paragraph to the Material and Methods section concerning the Steady-State ATPase assay:

“For measurements of the basal and actin–activated NM2A–HMM ATPase, 0.5 µM MLCKtreated HMM was used. Phalloidin–stabilized WT or mutant F-actin was added over the range of 0–25 µM. The change in absorbance at 340 nm due to oxidation of NADH was recorded in a Multiskan FC Microplate Photometer (Thermo Fisher Scientific, Waltham, MA, USA). The data were fitted to the Michaelis-Menten equation to obtain values for the actin concentration at half-maximal activation of ATP-turnover (Kapp) and for the maximum ATP-turnover at saturated actin concentration (kcat).”

Furthermore, we added a description of the results of the experiments to the Results section of the manuscript:

“Using a NADH-coupled enzymatic assay, we determined the ability of p.E334Q and WT filaments to activate the ATPase of NM2A-HMM over the range of 0-25 µM F-actin (Figure 8C). While we observed no significant difference in Kapp, indicated by the actin concentration at half-maximal activation, in experiments with p.E334Q filaments (2.89 ± 0.49 µM) and WT filaments (3.20 ± 0.74 µM), we observed a 28% slower maximal ATP turnover at saturating actin concentration (kcat) with p.E334Q filaments (0.076 ± 0.005 s-1 vs. 0.097 ± 0.002 s-1).”

• (line 310) The authors state that they "noticed increased rapid dissociation and association events for E334Q filaments" in the motility assay. This observation motivates the authors to assess actin affinities of NM2A-HMM. Although differences in rigor and AM.ADP affinities are found between mutant and WT actins, the actin attachment lifetimes (many minutes) are unlikely to be related to the rapid association and dissociation event seen in the motility assay. Rather, this jiggling is more likely to be related to a lower duty ratio of the myosins, which appears to be the conclusion reached for the myosin-V data. These points should be clarified in the text.

We changed the text in accordance with the reviewer’ suggestion. It reads now: Cytoskeletal –actin filaments move with an average sliding velocity of 195.3 ± 5.0 nm s–1 on lawns of surface immobilized NM2A–HMM molecules (Figure 8A, B). For NM2A-HMM densities below about 10,000 molecules per μm2, the average sliding speed for cytoskeletal actin filaments drops steeply (Hundt et al, 2016). Filaments formed by p.E334Q actin move 5fold slower, resulting in an observed average sliding velocity of 39.1 ± 3.2 nm/s. Filaments copolymerized from a 1:1 mixture of WT and p.E334Q actin move with an average sliding velocity of 131.2 ± 10 nm s–1 (Figure 8A, B). When equal densities of surface-attached WT and mutant filaments were used, we observed that the number of rapid dissociation and association events increased markedly for p.E334Q filaments (Figure 8 – video supplement 7– 9).

Using a NADH-coupled enzymatic assay, we determined the ability of p.E334Q and WT filaments to activate the ATPase of NM2A-HMM over the range of 0-25 µM F-actin (Figure 8C). While we observed no significant difference in Kapp, indicated by the actin concentration at halfmaximal activation, in experiments with p.E334Q filaments (2.89 ± 0.49 µM) and WT filaments (3.20 ± 0.74 µM), we observed a 28% slower maximal ATP turnover at saturating actin concentration (kcat) with p.E334Q filaments (0.076 ± 0.005 s-1 vs. 0.097 ± 0.002 s-1). To investigate the impact of the mutation on actomyosin–affinity using transient–kinetic approaches, we determined the dissociation rate constants using a single–headed NM2A–2R construct (Figure 8D). …..

• (line 327) The authors report that the 1/K1 value is unchanged. There are no descriptions of this experiment in the paper. I am assuming the authors measured the ATP-induced dissociation of actomyosin and determined ATP affinity (K1) from this experiment. If this is the case, they should describe the experiment and show the data, provide a second-order rate constate for ATP binding, and report the max rate of dissociation (k2). This is a kinetic experiment done frequently by this group, so the absence of these details is surprising.

In the previous version of the manuscript, the method used to determine 1/K1 (ATP-induced dissociation of the actomyosin complex) was described in the Material and Methods paragraph “Transient kinetic analysis of the actomyosin complex” and the values obtained for 1/K1 were given in Table 1. We now included the experimental data as an additional figure in the manuscript (Figure 8 – figure supplement 3). Furthermore, we also give the maximal dissociation rate k+2 and the apparent second-order rate constant for ATP-binding (K1k+2) for the WT and mutant actomyosin complex in Table 1. Therefore, we changed the paragraph in the Results section concerning this experiment to:

“The apparent ATP–affinity (1/K1), the maximal dissociation rate of NM2A from F-actin in the presence of ATP (k+2), and the apparent second-order rate constant of ATP binding (K1k+2) showed no significant differences for complexes formed between NM2A and WT or p.E334Q filaments (Table 1, Figure 8 – figure supplement 3).”

and the section in the Material and Methods to:

“The apparent ATP–affinity of the actomyosin complex was determined by mixing the apyrase–treated, pyrene–labeled, phalloidin–stabilized actomyosin complex with increasing concentrations of ATP at the stopped–flow system. Fitting an exponential function to the individual transients yields the ATP–dependent dissociation rate of NM2A–2R from F–actin (kobs). The kobs–values were plotted against the corresponding ATP concentrations and a hyperbola was fitted to the data. The fit yields the apparent ATP–affinity (1/K1) of the actomyosin complex and the maximal dissociation rate k+2.

The apparent second–order rate constant for ATP binding (K1k+2) was determined by applying a linear fit to the data obtained at low ATP concentrations (0 – 25 µM).”

For a better understanding of the numerous rate and equilibrium constants, we have now included a figure showing the kinetic reaction scheme of the myosin ATPase cycle (Figure 8 – figure supplement 1).

Recommendations for the authors:

Reviewer #1:

• The subdomains of actin are mislabeled in Fig. 1A.

The labeling of the subdomains has been corrected.

• Additional experimental data addressing the 3 weaknesses noted in the public review would be informative but are not essential in my opinion. Examining the effect of cofilin on severing by the TIRF assay in more detail and using a processivity assay for myosin V (immobilized actin) would be the two aspects I would most value.

The TIRF assay for cofilin severing was performed initially over the cofilin concentration range from 20 to 250 nM. The results obtained in the presence of 100 nM cofilin allow a particularly informative depiction of the differences observed with mutant and WT actin. This applies to the image series showing the changes in filament length, cofilin clusters, and filament number as well as to the graphs showing time dependent changes in the number of filaments and total actin fluorescence. We have not included the results for a 50:50 mixture of WT:mutant actin because its attenuating effect is documented in several other experiments in the manuscript.

Our results with Myo5A show a less productive interaction with mutant actin filaments as indicated by a 1.7-fold reduction in the average sliding velocity and an increase in the optimal Myo5A-HMM surface density from 770 to 3100 molecules per µm2. These results indicate a reduction in binding affinity and coupling efficiency, with a likely impact on processivity. Given that Myo5A is only one of many cytoskeletal myosin motors and that the motor properties of all myosins are modulated by the presence of tropomyosin isoforms and other actin binding proteins, we expect only a small incremental gain in knowledge by performing additional experiments with an inverted assay geometry.

Reviewer #2:

• The authors should address the concerns regarding the statistical methodologies.

We have gone through the manuscript carefully to correct any errors in the statistics, as explained below.

Figure 1B, 5B, 5C, 5D, 8D, 9B, and 8 – figure supplement 2 all show the mean ± SD, as also correctly reported for Figure 8E and 8F in the figure legend. The statement, that these figures show the mean ± SEM was wrong and we corrected this mistake for all the listed figures. Furthermore, we now give the exact N for every experiment in the figure legend.

Figure 2C, 2E, 2F, 4B, 5A, 6B-E indeed showed the mean ± SEM. As the reviewer rightly points out, this is not the appropriate way to deal with such sample sizes. We therefore corrected the figures to show the mean ± SD.

We still refer to the mean ± SEM in Figure 2B, where elongation rates for more than 100 filaments were recorded, and in Figure 8B, where sliding velocities for several thousand actin filaments were measured.

• The authors should present the actin titration of the steady state ATPase activity for at least one of the myosins, or preferably all of them.

An actin titration of the steady state ATPase activity of NM-2A has been included in the revised version of the manuscript (Fig 8C).

• The authors should consider the use of pyrene-actin in measuring the assembly/disassembly of actin.

Values for the rate of actin assembly/disassembly measured with pyrene-actin are given in Table 1. Based on the small changes observed, we did not determine the critical actin concentration for the mutant construct.

Author Response

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

Reviewer #1 (Recommendations for The Authors):

To hopefully contribute to more strongly support the conclusions of the manuscript, I am including a series of concerns regarding the experiments, as well as some recommendations that could be followed to address these issues:

(1) The Q-nMT bundle is largely unaffected by the nocodazole treatment in most phases during its formation. However, cells were only treated with nocodazole for a very short period of time (15 min). Have the authors analyzed Q-nMT stability after longer nocodazole exposures? Is a similar treatment enough to depolymerize the mitotic spindle? This result could be further substantiated by treatment with other MT-depolymerizing agents. Furthermore, the dynamicity of the Q-nMT bundle could be ideally also assessed by other techniques, such as FRAP.

The experiments suggested by the reviewer have been published in our previous paper (Laporte et al, JCB 2013). In this previous study, we presented data demonstrating the resistance of the Q-nMT bundle to several MT poisons: TBZ, benomyl, MBC (Sup Fig 2D) and to an increasing amount of nocodazole after a 90 min treatment (Sup Fig2E). These published figures are provided below.

Author response image 1.

The nMT array contains highly stable MTS. (A) Variation Of nuclear MT length in function Of time (second) in proliferating cells. Cells express GFP•Tubl (green) and Nup2•RFP (red). Bars, 2 pm. N = l, n is indicated. (B) Variation of the nMT array length in function of time measured for BirnlGFP—expressing cells In = 161, for 6-d•old Dad2GFP—expressing cells In = 171, for Stu2GFP—expressing cells (n = 17), and 6•d-old Nuf2• GFP—expressing cells (n = 17). Examples Of corresponding time lapse are shown. Time is in minutes experiments). Bar, 2 pm. (CJ Nuf2•GFP dots detected along nMT array (arrow) are immobile. Several time lapse images of cells are shown. Time is in minutes. gar, 2 pm _ MT organizations in proliferating cells and 4-d•old quiescent cells before and after a 90-min treatment With indicated drugs. Bar, 2 pm. (E) MT organizations in Sci-old quiescent cells before and after a 90min treatment With increasing concentrations Of nocodazole.

In the same article, we showed that Q-nMT bundles resist a 3h nocodazole treatment, while all MT structures assembled in proliferating cells, including mitotic spindle, vanished (see Fig 2E below). In addition, in our previous article, FRAP experiments were provided in Fig 2D.

Author response image 2.

The nuclear array is composed of stable MTS. Variation of the length in function of time of (A) aMTs in proliferating cells, (B) nMT array in quiescent cells (7 d), and the two MT structures in early quiescent cells (4 d). White arrows point ot dynamic aMTs. In A—C, N = 2, n is indicated ID) FRAP on 7-d-old quiescent cells. White arrows point to bleach areas. Error bars are SEM. In A—D. time is in seconds. (E) nMT array is not affected by nocodazole treatment. Before and various times after carbon exhaustion (red dashed line), cells were incubated for 3 h with 22.5 pg/pL nocodozole and then imaged. The corresponding control experiment is shown in Fig I A. In all panels, cells expressing GFP-TtJbl (green) and Nup2-RFP (red) are shown; bars, 2 pm.

This previous study was mentioned in the introduction and is now re-cited at the beginning of the results section (line 107-108).

As expected from our previous study, when proliferating cells were treated with Noc (30 µg/ml) in the same conditions as in Fig1, most of the short and the long mitotic spindles vanished after a 15 min treatment as shown in the graph below.

Author response image 3.

Proliferating cells expressing NOf2=GFP and mTQZ-TUb1 (00—2) were treated or not With NOC (30vgfmI) for 15 min.% Of cells With detectable MT and representative cells are shown. Khi-teet values are indicated. Bar: 2 pm,

(2) The graph in Figure 1B is somewhat confusing. Is the X-axis really displaying the length of the MTs as stated in the legend? If so, one would expect to see a displacement of the average MT length of the population as cells progress from phase II to phase III, as previously demonstrated in Figure 1A. Likewise, no data points would be anticipated for those phases in which the MT length is 0 or close to 0. Moreover, when the length of half pre-anaphase mitotic spindle was measured as a control, how can one get MT lengths that are equal or close to 0 in these cells? The length of the pre-anaphase spindle is between 2-4 um, so MT length values should range from 1 to 2 um if half the spindle is measured.

The graph in Fig1B represents the fluorescence intensity (a proxy for the Q-nMT bundle thickness) along the Q-nMT bundle length.

Fluorescence intensity is measured along a “virtual line” that starts 0,5 µm before the extremity of the QnMT bundle that is in contact with the SPB. In other words, we aligned all intensity measurements at the fluorescence increasing onset on the SPB side. We arbitrarily set the ‘zero’ at 0,5um before the fluorescence increased onset. That is why the fluorescence intensity is zero between 0 and 0,5 µm – The X-axis represents this virtual line, the 0 being set 0,5 µm before the Q-nMT bundle extremity on the SPB side. This virtual line allows us to standardize our “thickness” measurements for all Q-nMT bundles.

Using this standardization, it is clear that the length of the Q-nMT bundles increased from phase II to III (see the red arrow). Yet, as in phase II, Q-nMT bundles are not yet stable, their lengths are shorter in phase II than in phase II after a Noc treatment (compare the end of the orange line and the end of the blue line in phase II).

Author response image 4.

This is now explained in details in the Material and Methods section (line 539-545).

This is the same for the inset of Fig 1B and in Sup Fig 1A, in which we measured fluorescence intensity along the halfmitotic spindle just as we did for MT bundle. The X-axis represent a virtual line along the mitotic spindle, starting 0,5 µm before the SBP spindle extremity.

Author response image 5.

(3) Microtubules seem to locate next to or to extend beyond the nucleus in the control cells (DMSO) in Figure 1H. Since both nuclear MTs and cytoplasmic MTs emanate from the SPBs, it would have been desirable to display the morphology of the nucleus when possible. Moreover, since the nucleus is a tridimensional structure, it would also be advisable to image different Z-sections.

Analysis demonstrating that Q-nMT bundles are located inside the nucleus have been provided in our previous paper (Laporte et al, JCB 2013). In this article most of the images are maximal projections of Z-stacks in which the nuclear envelope is visualized via Nup2-RFP (see Fig1 of Laporte et al, JCB 2013 as an example below).

Author response image 6.

MTsare organized as a nuclear array in quiescent cells. (A) MT reorganization upon quiescence entry. Cells expressing GFP-Tub1 (green) and Nup2RFP (red) are shown. Glucose exhaustion is indicated as a red dashed line. Quiescent cells dl expressing Tub I-RFP and either Spc72GFP,

In Laporte et al, JCB 2013, we also provided EM analysis both in cryo and immune-gold (Fig 1E below).

Author response image 7.

(top) or coexpr;sse8 with Tub I-RFP (bottom). Arrows point dot along the nMT array. Bars: (A—C)) 2 pm. (E) AMT arroy visualized in WT cells by EMI Yellow arrows, MTS; red arrowheads, nuclear membrane; pink arrow, SPB. Insets: nMT cut transversally. Bar, 100 nm.

(4) Movies depicting the process of Q-nMT bundle formation in live cells would have been really informative to more precisely evaluate the MT dynamics. Likewise, together with still images (Fig 1D and Supp. Fig. 1D), movies depicting the changes in the localization of Nuf2-GFP would have further facilitated the analysis of this process.

In a new Sup Fig 1E, we now provide images of Q-nMT bundle formation initiation in phase I, in which it can be observed that Nuf2-GFP accompanies the growth of MT (mTQZ-TUB1) at the onset of Q-nMT bundle formation. Unfortunately, it is technically very challenging to follow the entire process of Q-nMT bundle formation in individual cells, as it takes > 48h. Indeed, for movies longer than 24h, on both microscope pads or specific microfluidic devices (Jacquel, et al, eLife 2021), phototoxicity and oxygen availability become problematic and affect cells’ viability.

(5) Western blot images displaying the relative protein levels for mTQZ-Tub1 and of the ADH2 promoter-driven mRuby-Tub1 at the different time points should be included to more strongly support the conclusion that new tubulin molecules are introduced in the Q-nMT bundle only after phase I. It is worth noting, in this sense, that the percentage of cells with 2 colors Q-nMT bundle is analyzed only 1 hour after expression of mRuby-Tub1 was induced for phase I cells, but after 24 hours for phase II cells.<br /> We have modified Fig 1F and now provide images of cells after 3, 6 and 24h after glucose exhaustion and the corresponding percentage of cells displaying Q-nMT bundle with the two colors. We also now provide a western blot in Sup Fig 1H using specific antibodies against mTQZ (anti-GFP) and mRuby (anti-RFP).

(6) In order to demonstrate that Q-nMT formation is an active process induced by a transient signal and that the Q-nMT bundle is required for cell survival, the authors treated cells with nocodazole for 24 h (Fig 1H and Supp Fig 1K). Both events, however, could be associated with the toxic effects of the extremely prolonged nocodazole treatment leading to cell death.

We have treated 5 days old cells for 24h with 30 µg/ml Noc. We then washed the drug and transferred the cells into a glucose free medium. We then followed both cell survival, using methylene blue, and the cell’s capacity to form a colony after refeeding. In these conditions, we did not observe any toxic effect of the nocodazole. This result is now provided in Sup Fig 1L and discussed line 172-176.

(7) The "Tub1-only" mutant displays shorter but stable Q-nMT bundles in phase II, although they are thinner than in wild-type cells. What happens in the "Tub3-only" mutant, which also has beta-tubulin levels similar to wild-type cells (Supp. Fig. 2B)?

In order to measure Q-nMT bundle length and thickness, we used Tub1 fused to GFP. This cannot be done in a Tub3-only mutant. Yet, we have measured Q-nMT bundle length in Tub3-only cells using Bim1-3GFP as a MT marker (as in Laporte et al, JCB 2013). As shown in the figure below, Q-nMT bundles were shorter in Tub3-only cells than in WT cells whatever the phase.

Author response image 8.

We do not know if this effect is directly linked to the absence of Tub1 or if it is very indirect and for example due to the fact that Tub1 and Tub3 interact differently with Bim1 or other proteins that are involved in Q-nMT bundle stabilization. As we cannot give a clear interpretation for that result, we decided not to present those data in our manuscript.

(8) Why were wild-type and ndc80-1 cells imaged after a 20 min nocodazole treatment to evaluate the role of KT-MT attachments in Q-nMT bundle formation (Fig 3A)? Importantly, this experiment is also missing a control in which Q-nMT length is analyzed in both wild-type and ndc80-1 cells at 25ºC instead of 37ºC.

In this experiment, we used nocodazole to test both the formation and the stability of the Q-nMT bundle. Fig 3A shows MT length distribution in WT (grey) and ndc80-1 (violet) cells expressing mTQZTub1 (green) and Nuf2-GFP (red), shifted to 37 °C at the onset of glucose exhaustion and kept at this non-permissive temperature for 12 or 96 h then treated with Noc. The control experiment was provided in Sup Fig 3B. Indeed, this figure shows MT length in WT (grey) and ndc80-1 (violet) expressing mTQZ-Tub1 (green) and Nuf2-GFP (red) grown for 4 d (96h) at 25 °C, and treated or not with Noc. This is now indicated in the text line 216 and in the figure legend line 976

Author response image 9.

(9) As a general comment linked to the previous concern, it is striking that in many instances, Q-nMT bundle length is measured after nocodazole treatment without any evident reason to do this and without displaying the results in untreated cells as a control. If nocodazole is used, the authors should explicitly indicate it and state the reason for it.

We provide control experiments without nocodazole for all of the figures. For the sake of figure clarity, for Fig.3A the control without the drug is in Sup. Fig. 3B, for Fig. 3B it is shown in Sup. Fig. 3D, for Fig. 4B, it is shown in Sup. Fig 4A. This is now stated in the text and in the figure legend: for Fig. 3A: line 216 and in the figure legend line 976; for Fig. 3B: line 222 and figure legend line 984; for Fig. 4B: line 280 and in the figure legend line 1017.

The only figures where the untreated cells are not shown is for Fig 1D since the goal of the experiment is to make dynamic MTs shorten.

In Fig. 5C and Sup. Fig. 5D to F, we used nocodazole to get rid of dynamic cytoplasmic MTs that form upon quiescence exit in order to facilitate Q-nMT bundle measurement. This was explained in our previous study (Laporte et al, JCB 2013). We now mention it in the figure legends, see for example Fig. 5 legend line 1054.

(10) Ipl1 inactivation using the ipl1-1 thermosensitive allele impedes Q-nMT bundle formation. The inhibitor-sensitive ipl1-as1 allele could have been further used to show whether this depends on its kinase activity, also avoiding the need to increase the temperature, which affects MT dynamics. As suggested, we have used the ipl1-5as allele. We have thus modified Fig 3B and now show that is it indeed the Ipl1 kinase activity that is required for Q-nMT bundle formation initiation (line 222). In any case, it is surprising that deletion of SLI15 does not affect Q-nMT formation (in fact, MT length is even larger), despite the fact that Sli15, which localizes and activates Ipl1, is present at the Q-nMT (Fig 3C). Likewise, deletion of BIR1 has barely any effect on MT length after 4 days in quiescence (Fig 3D). Do the previous observations mean that Ipl1 role is CPC-independent? Does the lack of Sli15 or Bir1 aggravate the defect in Q-nMT formation of ipl1-1 cells at non-permissive or semi-permissive temperature?

Thanks to the Reviewer’s comments, we have re-checked our sli15Δ strain and found that it was accumulating suppressors very rapidly. To circumvent this problem, we utilized the previously described sli15-3 strain (Kim et al, JCB 1999). We found that sli15-3 was synthetic lethal with both ipl1-1, ipl1-2 (as described in Kim et al, JCB 1999) and with ipl1-as5, preventing us from addressing the CPC dependence of the Ipl1 effect asked by the Reviewer. However, using the sli15-3 strain, we now show that inactivation of Sli15 upon glucose exhaustion does prevent Q-nMT bundle formation (See new Sup Fig 3F and the text line 226-227).

(11) Lack of both Bir1 and Bim1 act in a synergistic way with regard to the defect in Q-nMT bundle formation. Although the absence of both Sli15 and Bim1 is proposed to lead to a similar defect, this is not sustained by the data provided, particularly in the absence of nocodazole treatment (Supp. Fig 3E).

Deletion of bir1 alone has only a subtle effect on Q-nMT bundle length in the absence of Noc, yet in bir1Δ cells, Q-nMT bundles are sensitive to Noc. Deletion of BIM1 (bim1Δ) aggravates this phenotype (Fig. 3D). As mentioned above, Q-nMT bundle formation is impaired in sli15-3 cells. In our hands, and as expected from (Zimnaik et al, Cur Biol 2012), this allele is synthetic lethal with bim1Δ.

On the other hand, the simultaneous lack of Bir1 and Bim1 drastically reduces the viability of cells in quiescence and this is proposed to be evidence supporting that KT-MT attachments are critical for QnMT bundle assembly (Supp Fig 3G). However, similarly to what was indicated previously for the 24 h nocodazole treatment, here again, the lack of viability could be originated by other reasons that are associated with the lack of Bir1 and Bim1 and not necessarily with problems in Q-nMT formation. In fact, the viability defect of cells lacking Bir1 and Bim1 is similar to that of cells only lacking Bir1 (Supp Fig 3G).

We have previously shown that many mutants impaired for Q-nMT bundle formation (dyn1Δ, nip100Δ etc) have a reduced viability in quiescence (Laporte et al, JCB 2013). In the current study, a very strong phenotype is observed for other mutants impaired for Q-nMT bundle formation such as bim1Δ bir1Δ cells, but also for slk19Δ bim1Δ.

Importantly, as shown in the new Sup Fig 1L, in WT cells treated with Noc upon entry into quiescence, a treatment that prevents Q-nMT formation, showed a reduced viability, while a Noc treatment that does not affect Q-nMT bundle formation, i.e. a treatment in late quiescence, has no effect on cell survival. This solid set of data point to a clear correlation between the ability of cells to assemble a Q-nMT bundle and their ability to survive in quiescence. Yet, of course, we cannot formally exclude that in all these mutants, the reduction of cell viability in quiescence is due to another reason.

(12) Both Mam1 and Spo13 are, to my knowledge, meiosis-specific proteins. It is therefore surprising that mutants in these proteins have an effect on MT bundle formation (Fig 3G-H, Supp. Fig. 3G). Are Mam1 and Spo13 also expressed during quiescence? Transcription of MAM1 or SPO13 does not seem to be induced by glucose depletion in previously published microarray experiments, but if Mam1 are Spo13 are expressed in quiescent cells, the authors should show this together with their results.<br /> Indeed, it is interesting to notice that Mam1 and Spo13 are involved in both meiosis and Q-nMT bundle formation. As suggested by the Reviewer we have performed western blots in order to address the expression of those proteins in proliferation and quiescence (4d). We tagged Spo13 with either GFP, HA or Myc but none of the fusion proteins were functional. Yet, as shown in the new Sup Fig 3I, Mam1-GFP, Csm1-GFP and Lsr4-GFP were expressed both in proliferation and quiescence.

(13) In the laser ablation experiments that demonstrate that KT-MT attachments are not needed in order to maintain Q-nMT bundles once formed, anaphase spindles of proliferating cells were cut as a control (Supp. Fig 3I). However, late anaphase cells have already segregated the chromosomes, which lie next to the SPBs (this can be evidenced by looking at Dad2-GFP localization in Supp. Fig 3I), so that only interpolar MTs are severed in these experiments. The authors should have instead used metaphase cells as a control, since chromosomes are maintained at the spindle midzone and the length and width of the metaphase spindle is more similar to that of the Q-nMT bundle.

We have tried to “cut” short metaphase spindles, but as they are < 1 µm, after the laser pulse, it is difficult to verify that spindles are indeed cut and not solely “bleached”. Furthermore, after the cut, the remaining MT structure that is detectable is very short, and we are not confident in our length measurements. Yet, this type of experiment has been done in S. pombe (Khodjakov et al, Cur Biol 2004 and Zareiesfandabadi et al, Biophys. J. 2022). In these articles the authors have demonstrated that after a cut, metaphase spindles are unstable and rapidly shrink through the action of Kinesin14 and dynein. This is now mentioned in the text line 265.

(14) In the experiment that shows that cycloheximide prevents Q-nMT disassembly after quiescence exit, and therefore that this process requires de novo protein synthesis (Fig. 5A), cells are indicated to express only Spc42-RFP and Nuf2-GFP. However, Stu2-GFP images are also shown next to the graph and, according to the figure legend, it was indeed Stu2-GFP that was used to measure individual QnMT bundles in cells treated with cycloheximide. In the graph, additionally, time t=0 represents the onset of MT bundle depolymerization, but Q-nMT bundle disassembly does not take place after cycloheximide treatment. The authors should clarify these aspects of the experiment.

Following the Reviewer’s suggestion, to clarify these aspects we have split Fig. 5A into 2 panels.

Finally, some minor issues are:

(1) The text should be checked for proper spelling and grammar.

We have done our best.

(2) In some instances, there is no indication of how many cells were imaged and analyzed.

We now provide all these details either in the figure itself or in the figure legend.

(3) Besides the Q-nMT bundle, it is sometimes noticeable an additional strong cytoplasmic fluorescent signal in cells that express mTQZ-Tub1 and/or mRuby-Tub1 (e.g., Figs 1F, 1H and, particularly, Supp Fig 1H). What is the nature of these cytoplasmic MT structures?

We did mention this observation in the material and methods section (see line 526-528). This signal is a background fluorescence signal detected with our long pass GFP filter. It is not GFP as it is “yellowish” when we view it via the microscope oculars. This background signal can also be observed in quiescent WT cells that do not express any GFP. We do not know what molecule could be at the origin of that signal but it may be derivative of an adenylic metabolite that accumulates in quiescence and could be fluorescent in the 550nm –ish wavelength, but this is pure speculation.

(4) It is remarkable that a 20-30% decrease in tubulin levels had such a strong impact on the assembly of the Q-nMT bundle (Supp. Fig. 2). Can this phenotype be recovered by increasing the amount of tubulin in the mutants impaired for tubulin folding?

Yes, this is astonishing, but we believe our data are very solid since we observed that with both tub3Δ and in all the tubulin folding mutants we have tested (See Sup. Fig. 2). To answer Reviewer’s question, we would need to increase the amount of properly folded tubulin, in a tubulin folding mutant. One way to try to do that would be to find suppressors of GIM mutations, but this is a lengthy process that we feel would not add much strength to this conclusion.

(5) The graphs displaying the length of the Q-nMT bundle in several mutants in microtubule motors throughout a time course are presented in a different manner than in previous experiments, with data points for individual cells being only shown for the most extreme values (Fig 4C, 4H). It would be advisable, for the sake of comparison, to unify the way to represent the data.

We have now unified the way we present our figures.

(6) How was the exit from quiescence established in the experiments evaluating Q-nMT disassembly? How synchronous is quiescence exit in the whole population of cells once they are transferred to a rich medium?

We set the “zero” time upon cell refeeding with new medium. In fact, quiescence exit is NOT synchronous. We have reported this in previous publications, with the best description of this phenomena being in Laporte et al, MIC 2017 . <br /> The figures below are the same data but on the left graph, the kinetic is aligned upon SPB separation onset, while on the right graph (Fig 5A), it is aligned on MT shrinking onset.

Author response image 10.

We can add this piece of data in a Sup Figure if the Reviewer believes it is important.

Reviewer #2 (Recommendations For The Authors):

General:

• In general, more precise language that accurately describes the experiments would improve the text. <br /> We have tried to do our best to improve the text.

• The authors should clearly define what they mean by an active process and provide context to support this statement regarding the Q-nMT.

We have strived to clarify this point in the text (see paragraph form line 146 to 178).

• It is reasonable to assume that structures composed of microtubules are dynamic during the assembly process. The authors should clarify what they mean by "stable by default i.e., intrinsically stable." Do they mean that when Q-nMT assembly starts, it will proceed to completion regardless of a change in condition?

We mean that in phase I the Q-nMT bundle is stabilized as it grows and that stabilization is concomitant with polymerization. By contrast, MTs polymerized during phase II are not stabilized upon elongation beyond the phase I polymer, and get stabilized later, in a separate phase (i.e. in phase III). We hope to have clarified this point in the text (see line 108-110).

• In lines 33-34, the authors claim that the Q-nMT bundle functions as a "sort of checkpoint for cell cycle resumption." This wording is imprecise, and more significantly the authors do not provide evidence supporting a direct role for Q-nMT in a quiescence checkpoint that inhibits re-entry into the cell cycle.

We have softened and clarified the text in the abstract (see line 29-30)., in the introduction (line 101104), in the result section (line 331-332) and in the discussion (line 426-430).

• Many statements are qualitative and subjective. Quantitative statements supported by the results should be used where possible, and if not possible restated or removed.

We provide statistical data analysis for all the figures.

• The number of hours after glucose exhaustion used for each phase varies between assays. This is likely a logistical issue but should be explained.

This is indeed a logistical issue and when pertinent, it is explained in the text.

• It would be interesting to address how this process occurs in diploids. Do they form a Q-nMT? How does this relate to the decision to enter meiosis?

Diploid cells enter meiosis when they are starved for nitrogen. Upon glucose exhaustion diploids do form a Q-nMT bundle. This is shown and measured in the new Sup Fig1C. In fact, in diploids, Q-nMT bundles are thicker than in haploid cells.

• It would be interesting to address how the timescale of this process compares to the types of nutrient stress yeast would be exposed to in the environment.

We have transferred proliferating yeast cells to water, to try to mimic what could happen when yeast cells face rain in the wild. As shown below, they do form a Q-nMT bundle that becomes nocodazole resistant after 30h. This data is now provided in the new Sup Fig 1D.

• It is recommended that the authors use FRAP experiments to directly measure the stability of the QnMT bundles.

This experiment was published in (Laporte et al, 2013). Please see response to Reviewer #1.

• In many cases, the description of the experimental methods lacks sufficient detail to evaluate the approach or for independent verification of results.

We have strived to provide a more detailed material and methods section, as well as more detailed figure legends and statistical informations.

Specific comments on figures:

• In Figure 1 c), what do the polygons represent? They do not contain all the points of the associated colour.

The polygon represented the area of distribution of 90% of the data points. As they did not significantly add to the data presentation they have been removed.

• In Figure 2 a), is the use of two different sets of markers to control for the effect of the markers on microtubule dynamics?

Yes, we are always concerned about the influence of GFP on our results, so very often we replicate our experiments with different fluorescent proteins or even with different proteins tagged with GFP. This is now mentioned in the text (line 184-186).

• Is it accurate to say (line 201, figure 3 a)) that no Q-nMT bundles were detected in ndc80-1 cells shifted to 37 degrees, or are they just shorter?

As shown in Fig 3A, in ndc80-1 cells, most of the MT structures that we measured are below 0,5um. This has been re-phrased in the text (line 214-215).

• Lines 265-269, figure 4 b), how can the phenotype observed in cin8∆ cells be explained given the low abundance of Cin8 that is detected in quiescent cells?

Faint fluorescence signal is not synonymous of an absence of function. As shown in Sup Fig 4B, we do detect Cin8-GFP in quiescent cells.

• Quantification is needed in Figure 4 panels c) and h).

Fig 4C and 4H have been changed and quantification are provided in the figure legend.

Reviewer #3 (Recommendations For The Authors):

A few points should be addressed for clarity:

(1) Sup. Fig. 1K: are only viable cells used for the colony-forming assay? How were these selected? If not, the assay would just measure survival (as in the viability assay).

Yes, only viable cells were selected for the colony forming assay. We used methylene blue to stain dead cells. Then, we used a micromanipulation instrument (Singer Spore Play) that is commonly used for tetrad dissection to select “non blue cells” and position them on a plate (as we do with spores). Each micromanipulated cell is then allowed to grow on the plate and we count colonies (see picture in Sup Fig 1L right panel). This was described in Laporte et al, JCB 2011. We have added that piece of information in the legend (line 1129-1130) and in the M&M section (line 580-586).

(2) Could Tub3 have a role in phase I? It is not clear why the authors conclude involvement only in phase II.

As it can be seen in Fig 2D, MT bundle length and thickness are quite similar in WT and Tub1-only cells in phase I, indicating that the absence of Tub3 as no effect in phase I. In Tub1-only cells, MT bundles are thinner in both phase II and phase III, yet, they get fully stabilized in phase III. Thus, the effect of Tub3 is largely specific to the nucleation/elongation of phase II MTs. We hope to have clarified that point in the text (line 203-207).

(3) Quantifications, statistics: for all quantifications, the authors should clearly state the number of experiments (replicates), and number of cells used in each, and what number was used for statistics. For all quantifications in cells, it seems that the values from the total number of cells across different experiments were plotted and used for statistics. This is not very useful and results in extremely small p values. I assume that the values for individual cells were obtained from multiple, independent experiments. Unless there are technical limitations that allow only a very small sample size (not the case here for most experiments), for experiments involving treatments the authors should determine values for each experiment and show statistics for comparison between experiments rather than individual cells pooled from multiple experiments.

All the experiments have been done at least in replicate. In the new Fig. 1A, we now display each independent experiment with a specific color code. For Fig 2B and 2C we now provide the data obtained for each separate experiment in Sup Fig 2C. Additional details about quantifications and statistics are provided in the M&M section or in the specific figure legends.

Author Response

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

Reviewer #1 (Public Review):

We thank reviewer #1 for identifying the major caveats of the paper, and have split them out into separate comments below to address them.

Comment 1) The caveats are that ecosystem processes beyond water availability are not investigated although they are brought into play in the title and in the paper

Author response: We disagree that water availability is the only ecosystem process investigated in this study, as herbivory, plant mortality, and the maintenance of diversity in higher trophic levels are important processes within ecosystems. We have added text to the abstract and introduction clarifying that we consider these response measures to be ecosystem processes. Further language to this effect already exists in the abstract, methods, and discussion.

Comment 2) That herbivory beyond leaf damage was not reported (there might be none, the reader needs to be shown the evidence for this)

Author response: This is typically how herbivory is assessed in ecological studies, and our focus is on folivores. There may be additional herbivory in the form of fluid-sucking insects, shoot/root herbivory, etc., but these were not assessed. It would be interesting to assess these other forms of herbivory to see if they respond similarly with additional studies.

Comment 3) That herbivore diversity is defined by leaf damage (authors need to give evidence that this is a valid inference)

Author response: We thank reviewer #1 for pointing out the lack of written support for this claim. We have modified the methods (lines 138-139; 214-217) to clarify that this is a useful proxy for insect richness in the Piper system, and have added citations demonstrating it has been found to correlate well with insect richness in tropical forests.

Comment 4) That the plots were isolated from herbivores beyond their borders

Author response: This was not an assumption of the study. We have modified the methods (line 200) to make this clearer to the reader.

Comment 5) That the effects of extreme climate events were isolated to Peru

Author response: This was not an assumption of the study, rather it is an observation. While we consider it important to include observed climate differences between sites in the interpretation of our results, it was not necessary for there to be extreme climate events at other sites as we consider manipulated water availability to represent changes in precipitation that are expected to occur at these sites with climate change.

Comment 6) That intraspecific variation in the host plants needs to be explained and interpreted in more detail

Author response: We thank reviewer #1 for identifying that our current explanations needed development. We have modified the introduction to explore potential mechanisms relating intraspecific diversity to ecosystem function based on recent studies, and have modified the discussion to bring focus to why the effects of intraspecific differ from interspecific.

Reviewer #1 (Recommendations For The Authors):

Comment 1) Pare this material down to simpler results. The most significant to me is the intraspecific variation in damage. Were this broken out and reported in some detail it could be quite interesting. I find the results to be a confusing blizzard of multiple factors that differ among sites; after reading the paper twice I could not recall the takeaway lesson beyond that drought wrecks the diversity of herbivores and sometimes even kills the host plant.

Author response: We agree that the results are complicated given the variation in effects among sites, but this variation and complexity is important – and is in itself is one of the takeaway points. Unfortunately, nature is not simple. We have made several large edits to the results section, including the removal of methodological and otherwise redundant information, to hopefully bring the major takeaways into focus.

Reviewer #2 (Public Review):

Comment 1) This is an important and large experimental study examining the effects of plant species richness, plant genotypic richness, and soil water availability on herbivory patterns on Piper species in tropical forests.

A major strength is the size of the study and the fact that it tackled so many potentially important factors simultaneously. The authors examined both interspecific plant diversity and intraspecific plant diversity. They crossed that with a water availability treatment. And they repeated the experiment across five geographically separated sites.

The authors find that both water availability and plant diversity, intraspecific and interspecific, influence herbivore diversity and herbivory, but that the effects differ in important ways across sites. I found the study to be solid and the results to be very convincing. The results will help the field grapple with the importance of environmental change and biodiversity loss and how they structure communities and alter species interactions.

Author response: We thank reviewer #2 for their kind words.

Reviewer #2 (Recommendations For The Authors):

Comment 1) I was confused about why the authors measured species diversity/richness as a proportion of the species pool. This means that the metric of richness decreases if species are added to the species pool but not the plot/experiment. I think I understand it, but I suggest the authors explain this choice.

Author response: We thank reviewer #2 for pointing out that this was confusing. We have clarified the methods (lines 228-232) to explain that this choice was made to allow easier comparison between intra- and interspecific richness.

Comment 2) One of the stronger estimated relationships was a positive effect of plant species richness on insect richness. I found it a little hard to interpret this relationship. Is this just because there are host species specialists? So, with more host species there are more herbivore species? Or does insect richness increase multiplicatively with increasing plant species richness? One way to look for this would be for the authors to examine the relationship between plant species richness and the average number of herbivore damage types per plant species.

Author response: We agree that this is important for the reader to understand and have added text to the introduction and discussion sections explaining that this is the expectation based on theory and other empirical studies. We have additionally added text to the discussion (lines 386-388) pointing out that this pattern was not observed at all sites. While we agree that it would be interesting to explore if this effect was additive or multiplicative, we do not believe this is in the scope of the paper due to the methods used to measure insect richness.

Comment 3) Unless I missed it, some important information about the models was missing. E.g., what distributions were assumed for each of the variables? Any transformations?

Author response: We thank reviewer #2 for pointing this out, this information has been added to the methods (lines 272-274)

Comment 4) Why is there no model with water addition affecting insect richness directly but not percent herbivory directly?

Author response: While we originally decided to not include this model due to lack of theoretical support and low statistical performance, we have added references to this model (now model II) in the methods and results for consistency and to make model performance clearer to the reader. We have additionally moved supplemental table S1 to the main text to make the models and hypotheses tested by each model more accessible.

Comment 5) Fig. 2. What are the percentages above the figures? Maybe PD values?

Author response: These values are now clarified in the figure caption

Comment 6) L364 "can differ dramatically" This is vague and confusing. Differ in what way? From each other? Did the authors really expect plant richness to have the same effect on herbivory and plant survival? What would it mean anyway for plant richness to have the same effect on herbivory and plant survival?

Author response: We agree that the language here is confusing and thank reviewer #1 for drawing our attention to it. We have modified the discussion (lines 363-365) to clarify that the direction of effect of intraspecific richness can vary from the direction of effect of interspecific richness, rather than the effects on different response variables varying from each other.

Comment 7) L 375 "only meaningful differences" This statement feels a little overly strong. It seems like there is a good argument for this, but there could be other things going on.

Author response: We agree that the language here was unnecessarily strong, and have modified the discussion (lines 398-403) to focus on the lack of difference between methodologies at these two sites, and the observed differences in climate and community structure at each site.

Author Response

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

Public Reviews:

Reviewer #1 (Public Review):

In this study, the authors aimed to investigate how cells respond to dynamic combinations of two stresses compared to dynamic inputs of a single stress. They applied the two stresses - carbon stress and hyperosmotic stress - either in or out of phase, adding and removing glucose and sorbitol.

Both a strength and a weakness, as well as the main discovery, is that the cells' hyperosmotic response strongly requires glucose. For in-phase stress, cells are exposed to hyperosmotic shock without glucose, limiting their ability to respond with the well-studied HOG pathway; for anti-phase stress, cells do have glucose when hyperosmotically shocked, but experience a hypo-osmotic shock when both glucose and sorbitol are simultaneously removed. Responding with the HOG pathway and so amassing intracellular glycerol amplifies the impact of this hypo-osmotic shock. Counterintuitively then, it is the presence of glucose rather than the stress of its absence that is deleterious for the cells.

The bulk of the paper supports these conclusions with clean, compelling time-lapse microscopy, including extensive analysis of gene deletions in the HOG network and measurements of both division and death rates. The methodology the authors develop is powerful and widely applicable.

Some discussion of the value of applying periodic inputs would be helpful. Cells are unlikely to have previously seen such inputs, and periodic stimuli may reveal behaviours that are rarely relevant to selection.

We thank the referee for his review. To answer the reviewer’s last comment, our main objective was not to study conditions that are ecologically relevant, but rather to perturb the system in an original way to reveal new mechanisms and properties of the system. The main advantage of periodic inputs over more complex or unpredictible types of temporal fluctuations is that they can be defined with few parameters that are easy to interpret and to integrate in biophysical models. For instance, by using periodic inputs we were able to investigate how changing the phasing of two stresses impacted fitness while keeping other parameters constant (the duration of each stress was kept constant). We added two sentences at the beginning of the discussion to highlight the value of using periodic inputs.

We do not fully agree with the reviewer’s statement that periodic stimuli may reveal behaviours that are rarely relevant to selection. Indeed, many parameters of natural environments are known to vary periodically, such as light, temperature, predation, tides. Even if the periodic stimuli we use are artificial, they can still be a valuable tool to reveal new molecular processes. For instance, null mutants have been invaluable to understand biological systems despite being unlikely to reveal behaviours relevant to selection.

The authors' findings demonstrate the tight links that can exist between metabolism and the ability to respond to stress. Their study appears to have parted somewhat from their original aim because of the HOG pathway's reliance on glucose. It would be interesting to see if the cells behaviour is simpler in periodically varying sorbitol and a stress where there is little known connection to the HOG network, such as nitrogen stress.

The use of periodic nitrogen stress is a very interesting suggestion from both reviewers. However, we think it represents a large amount of work that deserves its own study. In particular, it would require first identifying a relevant period at which nitrogen fluctuations have an impact on division rate similar to what we observed for glucose fluctuations before performing experiments in AS and IPS conditions.

Nitrogen starvation is known to induce filamentous growth via activation of components of the HOG pathway (Cullen and Sprague, 2012), with potential cross-talk between filamentous growth and hyperosmotic stress response. Therefore, periodic osmotic stress and periodic nitrogen starvation may interact in a complex way.

Reviewer #2 (Public Review):

The authors have used microfluidic channels to study the response of budding yeast to variable environments. Namely, they tested the ability of the cells to divide when the medium was repeatedly switched between two different conditions at various frequencies. They first characterized the response to changes in glucose availability or in the presence of hyper-osmotic stress via the addition of sorbitol to the medium. Subsequently, the two stresses were combined by applying the alternatively or simultaneously (in-phase). Interestingly, the observed that the in-phase stress pattern allowed more divisions and low levels of cell mortality compared to the alternating stresses where cells were dividing slowly and many cells died. A number mutants in the HOG pathway were tested in these conditions to evaluate their responses. Moreover, the activation of the MAPK Hog1 and the transcriptional induction of the hyper-osmotic stress promoter STL1 were quantified by fluorescence microscopy.

Overall, the manuscript is well structured and data are presented in a clear way. The time-lapse experiments were analyzed with high precision. The experiments confirm the importance of performing dynamic analysis of signal transduction pathways. While the experiments reveal some unexpected behavior, I find that the biological insights gained on this system remain relatively modest.

In the discussion section, the authors mention two important behaviors that their data unveil: resource allocation (between glycolysis and HOG-driven adaptation) and regulation of the HOG-pathway based on the presence of glucose. These behaviors had been already observed in other reports (Sharifan et al. 2015 or Shen et al. 2023, for instance). I find that this manuscript does not provide a lot of additional insights into these processes.

We thank the referee for his review. We agree with the reviewer that the interaction between glucose availability and osmotic stress response has been investigated in previous studies. However, this interaction was investigated using experimental procedures that differed from our approach in critical ways, and therefore the behaviors observed were not the same. In Sharifian et al. (2015), the authors identified a new negative feedback loop regulating Hog1 basal activity and described underlying molecular mechanisms. This feedback loop is unlikely to explain differences of cell fitness we observed in IPS and AS conditions, because 1) differences of division rate was still observed in hog1 mutant cells and 2) differences of death rate involve glycerol synthesis, which is independent of the feedback loop described in Sharifian et al. (2015). In Shen et al. (2023), the authors observed a stronger expression of Hog-responsive genes at lower glucose concentrations, which seems contradictory with our observation of very low pSTL1-GFP expression in absence of glucose. However, they did not use fluctuating conditions and they did not report expression of stress-response genes when glucose was totally depleted (the lower glucose concentration they used was 0.02%) as we did, which may explain the different outcomes. We added three sentences in the discussion to compare our findings to those of Shen et al. (2023).

One clear evidence that is presented, however, is the link between glycerol accumulation during the sorbitol treatment and the cell death phenotype upon starvation in alternating stress condition. However, no explanations or hypothesis are formulated to explain the mechanism of resource allocation between glycolysis and HOG response that could explain the poor growth in alternating stresses or the lack of adaptation of Hog1 activity in absence of glucose.

In the revised version of the manuscript, we included a new result section and a supplementary figure (Figure 4 – figure supplement 2) where we tested three hypotheses to explain the lower division rate observed in AS condition relative to IPS condition. We found no evidence supporting these hypotheses, and the mechanisms responsible for the reduced growth in AS condition therefore remains elusive.

Another key question is to what extent the findings presented here can be extended to other types of perturbations. Would the use of alternative C-source or nitrogen starvation change the observed behaviors in dynamic stresses? If other types of stresses are used, can we expect a similar growth pattern between alternating versus in-phase stresses?

As mentioned above in our response to the other reviewer, these are very interesting questions that we think go beyond the scope of our study due to the amount of work involved.

Recommendations for the authors:

Reviewer #1

My comments are only minor.<br /> - More paragraphs would improve legibility.

To improve legibility, we split the longer section of the Results in three paragraphs (page 12, section entitled “Osmoregulation is impaired under in-phase stresses but not under alternating stresses.” However, we kept it as one section with a single title for global coherency: each section of the results corresponds to one main figure and have one main conclusion.

• I found AS and IPS confusing because what becomes important is whether sorbitol appears with glucose or not. For me, an acronym that makes that co-occurrence clear would be better or even better still no acronyms at all.

We tried several alternative names for the two conditions in previous drafts of the manuscript. Based on colleagues feedback, AS and IPS acronyms appeared as a good compromise between concision and clarity. To avoid confusion, the two acronyms are precisely defined when they are first used in the Results section. We think it is more important to emphasize the co-occurrence (or not) of the two stresses, rather than the co-occurrence of glucose and sorbitol. Indeed, standard yeast medium contains glucose but no sorbitol, and therefore we defined the two periodic conditions based on differences from standard medium. Even though we avoided using acronyms as much as possible in the manuscript, the use of these two acronyms to refer to the dual fluctuations of the environment seemed essential for concision. Indeed, IPS and AS acronyms are used many times in the results (16 occurrences on page 12 alone), figures and figure legends.

• I would consider moving some of Fig S2 to the main text: it helps clarify where Fig 2 is coming from and is referenced multiple times.

We fully agree with the reviewer and we moved panels A-D from Figure S2 to the main Figure 2.

• On page 10, "constantly facing a single stress that changes over time" is confusing. Perhaps "repetitively facing a single stress" instead?

We agree this sentence could be wrongly interpreted the way it was written. We changed it to: “cells grow more slowly when facing periodic alternation of the two stresses (AS) than when facing periodic co-occurrence of these stresses (IPS)”.

• Is there any knowledge on how cells resist hyperosmotic stress in the absence of glucose? That would help explain the IPS results.

Based on comments from both reviewers, we surveyed the literature to flesh out the discussion of hypotheses that would help explain observed differences between AS and IPS conditions. We found few studies that investigated cell responses in the absence of glucose, and because of significant differences in the experimental approaches it remains difficult to explain our results from conclusions of these previous studies. For instance, Shen et al., 2023 described and modeled the hyperosmotic stress response at various glucose concentrations. They found that Hog1p relocation to the nucleus after hyperosmotic shock lasted longer at lower glucose concentration, which is consistent with our finding in absence of glucose. However, they did not include the absence of glucose in their experiments or periodic fluctuations of glucose concentration. In addition, their model ignores the impact of cell signaling processes involved in growth arrest in response to hyperosmotic stress or glucose depletion. It is therefore difficult to relate their conclusions to our results. We have developed the discussion of our study to include these hypotheses and to clarify what is explained or not in our IPS and AS results.

There is knowledge on activation of the hyperosmotic stress pathway in response to glucose fluctuations, but not about the response to hyperosmotic stress in absence of glucose.

• On page 11, Figure 5a should be Figure 4a.

Correct.

• I would explain the components of the HOG pathway in the caption of Fig 1 or in the text when you cite Fig 1a. They are described later, but an early overview would be useful.

To give more context, we added the following sentences to the caption of Figure 1: “Yeast cells maintain osmotic equilibrium by regulating the intracellular concentration of glycerol. Glycerol synthesis is regulated by the activity of the HOG MAP kinase cascade that acts both in the cytoplasm (fast response) and on the transcription of target genes in the nucleus (long-term response). For simplicity, we only represented on the figure genes and proteins involved in this study.”

• On page 16, I wasn't sure what "redirect metabolic fluxes against glycerol synthesis" meant.

For more clarity, we modified this sentence to: “Since glucose is a metabolic precursor of glycerol, the absence of glucose may prevent glycerol synthesis and thereby fast osmoregulation."

• For Fig 2, having a dot-dash and dash-dash lines rather than both dash-dash would be better.

We made the proposed change, assuming the reviewer was referring to the gray dashed lines and not the colored ones.

• In the caption of Fig 3, 2% glucose is 20 g/L.

We thank the reviewer for catching this typo.

• In the Materials and Methods Summary, adding how you estimated death rates would be helpful: they are not often reported.

The calculation of death rates was explained in the Methods section. For more clarity, we modified the names of the parameters in the equation to make more explicit which ones refer to cell death.

Reviewer #2 (Recommendations For The Authors):

In Figure 2, it would be interesting to show individual growth rates of the perturbations at various frequencies as shown in Figures 3 c and d.

We thank the reviewer for this suggestion. We added a new supplementary figure (Figure 2 – figure supplement 2) showing the temporal dynamics of division rates at three different frequencies of osmostress and glucose depletion. We did not include high frequencies (periods below 48 minutes) because the temporal resolution of image acquisition in our experiments (1 image every 6 minutes) was too low. Very interestingly, this new analysis suggests that the positive relationship between the frequency of glucose depletion and division rate is explained by a delay between glucose removal and growth arrest rather than a delay between glucose addition and growth recovery. We therefore added the following conclusion:

“Under periodic fluctuations of 2% glucose, the division rate was lower during half-periods without glucose than during half-periods with glucose (Figure 2 – figure supplement 2d-f), as expected. However, this difference depended on the frequency of glucose fluctuations: the average division rate during half-periods without glucose was higher at high frequency (small period) than at low frequency (large period) of fluctuations (Figure 2 – figure supplement 2d-f). Therefore, the effect of the frequency of glucose availability on the division rate in 2% glucose is likely due to a delay between glucose removal and growth arrest: cell proliferation never stops when the frequency of glucose depletion is too fast.”

According to Sharifan et al. 2015, I would have expected that Hog1 would not relocate in the nucleus in 0% glucose. I wonder if this is due to the use of sorbitol as a stressor or the presence of low levels of glucose in the medium. I would suggest performing some control experiments with NaCl as hyperosmotic agent and test the addition of 2-deoxy-glucose to completely block glycolysis.

After careful reading of Sharifian et al. 2015, we fail to understand why the reviewer think Hog1 would be expected to not relocate to the nucleus after hyperosmotic stress in 0% glucose. In this previous study, the authors never combined glucose depletion with a strong hyperosmotic stress as we did in our study. They report the results of independent experiments where cells were exposed either to a single pulse of hyperosmotic stress (0.4 M NaCl) or to transient glucose starvation, but they did not combine these two stimuli. In this context, it is difficult to compare their results with ours. The fact that Sharifian et al. 2015 did not observe Hog1 nuclear relocation in 0% glucose (consistent with our result in Figure 6 – figure supplement 1a, yellow curve) is not inconsistent with our observation of Hog1 nuclear enrichment in 0% glucose + 1M sorbitol. One potential discrepancy between the two studies is the fact that they observed a small transient peak of Hog1 nuclear localization just after glucose is added back to the medium, while we failed to observe this peak in similar conditions (yellow curve in Figure 6 – figure supplement 1a). However, this could be simply explained by the temporal resolution of our experimental system: we image cells once every 6 minutes and the peak lasts less than 2 minutes in Sharifian et al. 2015. We added a sentence to discuss this minor point in the Results: “Although previous studies observed small transient (less than two minutes) peaks of Hog1-GFP nuclear localization after glucose was added back to the medium following glucose depletion (Sharifian et al., 2015, Piao et al., 2013), the temporal resolution in our experiments (one image every 6 minutes) may have been too low to detect these peaks.”.

While we agree many additional experiments would be interesting, such as testing the effects of different stress factors or the non-metabolizable glucose analog 2-deoxy-D-glucose, we think this is beyond the scope of this study because such experiments are likely to open broad perspectives and to not be conclusive in a reasonable amount of time.

When discussing Figure 7, the authors write that the HOG pathway is "overactivated" or "hyperactivated". I would refrain from using these terms because as seen in Figure 6, the Hog1 activity pattern, if anything, decreases as the number of alternative pulses increases. The high level of pSTL1mCitrine measured is mostly due to the long half-life of the fluorescent protein.

We used the formulation “hyper-activation” of the HOG pathway because Mitchell et al. 2015 used it to refer to the same phenomenon in their seminal study. This "hyper-activation" refers to the fact that both the integral activation of Hog1p (sum of areas under Hog1 nuclear peaks) and the global activation of transcriptional targets is much higher during fast periodic hyperosmotic stress than during constant hyperosmotic stress. That being said, we understand the point made by the reviewer about the decreasing size of Hog1 peaks over time during repeated pulses of osmotic stress. Therefore, we slightly modified the text to refer to hyper-activation of pSTL1-mCitrine transcription or expression instead of hyper-activation of the HOG pathway. For coherency, we replaced all instances of “overactivation” by “hyper-activation”.

Last but not least, the high level of pSTL1-mCitrine is both due to the long half-life of the protein and to the fact that pSTL1 transcription is never turned off due to high Hog1p activity under fast periodic osmostress.

Minor comments:

In the main text, I think it might be more intuitive to refer to doubling time in hours instead of division rates in 1/min which are harder to interpret.

In an early draft of the manuscript, we made figures with either division rates or with doubling times (ln(2)/division rate) and we received mixed opinions from colleagues on what measure was more intuitive to interpret. Both measures are widely used in the literature, and we decided to use division rates in the final version of the figures because it was more directly related to population growth rate and to fitness. For instance, the population growth rate shown in Figure 5 is simply calculated by subtracting the death rate from the division rate. For coherency, we therefore reported division rates instead of doubling times in figures and results. However, to address the reviewer’s comment we included the doubling times (in addition to the division rates) when mentioning the most important results. For instance, page 12: “Strikingly, cells divided about twice as fast under IPS condition (1.67 x 10-3 division/min, corresponding to an average doubling time of 415 minutes) than under AS condition (9.4 x 10-4 division/min, corresponding to an average doubling time of 737 minutes)”.

I found various capitalized version of "HOG /Hog pathway"

We corrected this incoherency and used “HOG pathway” everywhere.

Page 11. Figure 5a should refer to Figure 4a I believe.

Correct.

The methods are generally very thorough and precise. The explanation about the calculation of the division rate seems incomplete. For completeness, it would be good to mention the brand and model of valves used. In addition, it would be interesting to have an idea of the number of cells and microcolonies tracked in the various growth experiments.

We are not sure why the reviewer found the explanation of the calculation of division rate incomplete. For more clarity, we modified the names of parameters in the equations to make them more explicit. We also added a reference to Supplementary File 1 that contains all R scripts used to calculate division rates and death rates. We included the brand and model of valves used, as requested. As for the number of cells tracked in the various experiments, we mentioned in the Methods: “we selected 25 positions (25 fields of view) of the motorized stage (Prior Scientific ProScan III) that captured 10 to 50 cells in each of the 25 growth chambers of the chip and were focused slightly below the median cell plane based on cell wall contrast.” To address the reviewer’s comment, we also included the range of number of tracked cells for each experiment in corresponding figure legends.

Author Response

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

eLife assessment

This study of extrachromosomal DNA (ecDNA) aims to identify genes that distinguish ecDNA+ and ecDNA- tumors. This timely study is important in addressing the genes responding to the amplification of the ecDNA. The data presented are for the most part solid, there were concerns regarding the clarity in the description of the analysis methods and whether the evidence for specific genes required to maintain the ecDNA+ state was entirely conclusive.

Public Reviews:

Reviewer #1 (Public Review):

Recently discovered extrachromosomal DNA (ecDNA) provides an alternative non-chromosomal means for oncogene amplification and a potent substrate for selective evolution of tumors. The current work aims to identify key genes whose expression distinguishes ecDNA+ and ecDNA- tumors and the associated processes to shed light on the biological mechanisms underlying ecDNA genesis and their oncogenic effects. While this is clearly an important question, the analysis and the evidence supporting the claims are weak. The specific machine learning approach seems unnecessarily convoluted, insufficiently justified and explained, and the language used by the authors conflates correlation with causality. This work points to specific GO processes associated (up and down) with ecDNA+ tumors, many of which are expected but some seem intriguing, such as association with DSB pathways. My specific comments are listed below.

Response. As some of the specific questions below address similar concerns, we have answered them briefly here. As a high level point, the reviewer is correct in that other statistical or ML approaches could potentially have been used, and that some are simpler. However, the test used here directly addresses the question: Find a collection of genes whose expression value is predictive of ecDNA status in the sample. Because the underlying method in the Boruta analysis uses random forests, it can test predictive power without relying on a linearity assumption implicit in other methods. In this revision, we also compare against a Generalized Linear Model and show that it is less suited to the specific task above. We also address the reviewer concerns about specific parameter choices by showing robustness to the specific parameter.

(A) The claim of identifying genes required to 'maintain' ecDNA+ status is not justified - predictive features are not necessarily causal.

Response. We agree with the reviewer that predictive features are correlative and not causal. In the manuscript, we identify genes whose expression (when used as a feature) is predictive of ecDNA presence or absence. Such predictive genes are consistently over-expressed or consistently under-expressed in ecDNA(+) samples relative to ecDNA(-) samples even though they are not required to be on ecDNA. To our knowledge, we did not claim that these genes are causal for ecDNA formation or maintenance, only that such genes and the underlying biological processes are worth investigating. In the beginning of the manuscript, we had written the following paragraph, but we have removed the last line (struck out here):

“In lieu of identifying genes that are highly differentially expressed between ecDNA(+) and ecDNA(-) samples but driven by a small subset of cases (e.g. gene A in Fig. S1a), we sought to identify genes (e.g. gene B) whose expression level was predictive of ecDNA presence. We assumed that genes that were persistently over-expressed or under-expressed in ecDNA(+) samples relative to ecDNA(-) samples were more likely to be involved in ecDNA biogenesis or maintenance, or in mediating the cellular response to the presence of ecDNA.”

We revised the manuscript to make sure that there are no claims that refer to causality. We revisited all phrases where the words like “maintain” were used and added appropriate disclaimers, or replaced them by the phrase, “ecDNA presence.” The remaining statements say, for example, “These results are consistent with a pan-cancer role of CorEx genes in ecDNA biogenesis and maintenance,” and do not claim causality.

(B) The methods and procedures to identify the key genes is hyper-parameterized and convoluted and casts doubt on the robustness of the findings given the size and heterogeneity of the data.

(a) In the first two paragraphs of Boruta Analysis Methods section, authors describe an iterative procedure where in each iteration, a binomial p-value is computed for each gene based on number of iterations thus far in which the gene was selected (higher GINI index than max of shadow features). But then in the third paragraph they simply perform Random Forest in 200 random 80% of samples and pick a gene if it is selected in at least 10/200. It is ultimately not clear what was done. Why 10/200? Also "the probability that a gene is a "hit" or "non-hit" in each iteration is 0.5" is unclear. That probability is of a gene achieving GINI index higher than the max of shadow features. How can it be 0.5?

Response. We believe that there is some misunderstanding about the algorithm, and we agree that the description should have been more clear. We have greatly simplified the description in the manuscript. However, we want to provide some higher-level explanation here. Boruta is a standard feature extraction algorithm (Kursa, Journal of Statistical Software September 2010, Volume 36, Issue 11), and we used a Python implementation of the method. Given a gene expression data-set with class labels on samples, Boruta extracts features (genes) that best predict the class labels using a Random Forest Classifier, as long as the features are more predictive than permuted features added in each iteration. As we are using an implementation of a published method, we have removed non-essential details, referring directly to the publication. Nevertheless, to address the reviewer’s specific critique, the number of false-features added changes in each iteration (it equals the number of accepted+uncommitted features). Therefore, the choice of 0.5 by Boruta (it is fixed in the published method and not a user-specified parameter) is a conservative approach. If a gene was no better than a randomly chosen feature, its predictive performance would exceed the most predictive randomly chosen feature by at most 0.5 (but could be lower, making the choice of 0.5 conservative).

While Boruta iteratively picks genes that are significantly better than random features, the list of genes predicted might be specific to the data-set, and might change with different data-sets. Therefore, we employed a bootstrapping strategy: we performed 200 trials each time picking 80% of the ecDNA(+) samples and 80% of the ecDNA(-) samples at random, thus generating many data-sets while maintaining class imbalance. For each of the 200 trials, we performed a Boruta analysis. Finally, we picked a gene if it was selected as a Boruta feature in at least 10 of 200 trials.

The reviewer has a reasonable critique about why 10 (of 200) specifically, and why not fewer or more. Most genes are weak predictors by themselves. For example, RAE1, which is the top ranked gene, picked in all 200 Boruta trials, can only predict ecDNA status with poor recall for any meaningful precision.

Author response image 1.

Given the weakness of an individual gene as a classifier, its repeated selection in multiple Boruta trials is already a significant event. By requiring a gene to be picked in 5% of the trials (10/200), we were selecting a small, but more robust list of genes. However, to further explore the reviewer’s concerns, we also applied 8 other selection criteria ranging from 5 (of 200 Boruta trials) to 200 of 200 Boruta trials. See Figure below. The number of CorEx genes expectedly decreases. However, of the 187 GO terms that were enriched by 262 UP-genes using 10 of 200 Boruta trials as the selection criteria, 93 terms (49.7%) were enriched for each cut-off (see Author response image 2), and 155 terms (82.9%) were enriched in at least 5 of the 8 cut-off criteria. Given that the remaining analysis works on the hierarchy of GO terms and finds 4 GO-categories (Mitotic Cell Cycle, G1/S, G2/M; cell-division; DSB DNA Damage response; and the HOX Gene cluster) enriched by UP-regulated genes, those conclusions would hold regardless of the specific cut-off.

Author response image 2.

The number of GO terms that were enriched by DOWN-regulated genes is smaller, only 73, and falls rapidly for higher cut-offs, with 25 at a cut-off of 15. Therefore we see fewer terms enriched for more stringent cut-offs. However, they all support immune processes. These results do suggest that there are fewer genes that are consistently down-regulated in ecDNA(+) cancers, and expression change in a small number of genes may be sufficient to promote conditions for ecDNA.

Finally, we note that in the final section we discuss the 65 most highly ranked genes with a harmonic mean rank <= 3. These 65 CorEx genes (or a member of their cluster) appear in each of 200 Boruta trials. Thus, their choice is also not dependent on the cut-off of 10 in 200. In summary, the conclusions of the paper do not depend upon the specific cut-off of 10 in 200 trials.

We have added the figure as a supplemental figure and have added the following text to the manuscript on pages 17 and 18.

“Any CorEx gene is either a Core gene that was selected as a feature in at least 5% of 200 Boruta trials, or be highly co-expressed with a Core gene. Because the selection criterion of 5% is arbitrary, we also tested robustness with 8 other cut-offs ranging from 5-of-200 to 200-of-200 Boruta trials. The number of CorEx genes expectedly decreases with more stringent cut-offs. However, of the 187 GO terms that were enriched by 262 CorEx UP-genes using 10 of 200 Boruta trials as the selection criteria, 93 terms (49.7%) were enriched for each cut-off (Fig. S9), and 155 terms (82.9%) were enriched in at least 5 of the 8 cut-offs. Given that our subsequent analyses utilized the hierarchy of GO terms and identified 4 GO-categories enriched by UP-regulated genes, the conclusions would hold regardless of the specific cut-off.”

(b) The approach of combining genes with clusters is arbitrary. Why not start with clusters and evaluate each cluster (using some gene set summary score) for their ability to discriminate? Ultimately, one needs additional information to disambiguate correlated genes (i.e. in a coexpression cluster) in terms of causality.

Response. In general, the approach proposed by the reviewer is reasonable. However, we did consider that possibility and found that our approach was easier to implement. For example, if we clustered first, we would have the challenge of choosing the correct set of clusters. Also, the Boruta analysis would become very difficult while dealing with clusters (e.g., how to define falsefeatures?). We tested other methods of picking genes that were suggested by other reviewers such as generalized linear models. They turned out not to be as predictive of ecDNA status, as described later in the response. Finally, we performed many experiments to ensure the validity of the clustering. Specifically, we had the following text in the paper:

“Notably, among the 354 clusters, only 2 clusters (with 14 total genes) did not contain any Core genes. As most genes do not have completely identical expression patterns, we would expect one gene to be consistently picked as a Boruta gene over another co-expressed gene. Consistent with this hypothesis, most (344/354) clusters contained only 1 or 2 Core genes (Fig. 1c). When selecting clusters that contained at least 1 Core and 1 co-expressed gene, 53 of 71 clusters contained 1 to 3 Core genes (Fig. S1b), confirming that a few genes per co-expressed cluster provide sufficient predictive value, but other co-expressed genes might still play an important functional role in maintaining ecDNA(+) status.”

These experiments suggest that the genes found by extending the Core genes through clustering do not radically change the Core genes, but only enhance the set.

(c) The cross-validation procedure is not clear at all. There is a mention of 80-20 split but exactly how/if the evaluation is done on the 20% is muddled. The way precision-recall procedure is also a bit convoluted - why not simply use the area under the PR curve?

Response. We apologize if the method was unclear. We have rewritten the methods part to make things clearer. As a high level point, there are two places where we use the same 80-20 split, and that resulted in some confusion. We start by randomly picking 80% of the ecDNA(+) and 80% of ecDNA(-) samples to create an 80-20 split of all samples. This procedure is repeated to generate 200 80-20 split data-sets. These data-sets are hereafter called 200 training and test samples.

In the first usage, we use only the ‘training’ part of the 200 samples. We apply Boruta to each training set, and this helps us select the Core genes, which are then expanded to form the CorEx set. At this point, the CorEx genes are frozen for analysis in the rest of the paper. One question that we subsequently answer is what is the predictive power of the CorEx genes in determining if the sample is ecDNA(+) or ecDNA(-)? We also compare the predictive performance of CorEx genes relative to (a) Core genes, (b) LFC genes, and (c) random genes. In the revised manuscript, we have added another list of 3,012 genes selected using a single gene generalized linear model (GLM) for feature prediction. To make these comparisons, we utilized the same 200 training and test data-sets as before. In each test, we trained a random forest classifier on the training set and predicted on the ‘test’ set, for each of the 5 gene lists. This provided a uniform and fair method for testing which of the 5 gene lists was the better predictor of ecDNA status.

The precision recall values are plotted in Fig. 2b (also included below). We note that none of the gene lists was a great predictor of ecDNA status of a sample. However, the CorEx and Core genes were significantly more predictive than GLM, LFC, and random genes. The predictive power of GLM genes was very similar to LFC, and better than random.

For each of these 200 tests, we obtained a separate area under the precision-recall curve number for each of the gene-sets. To address the reviewer’s comments regarding a single number, we reported the average of the AUPRC for each of the gene-sets in the revision. The mean AUPRC values were added to the manuscript and are described here as well: Core_408_genes: 0.495 CorEx_643_genes: 0.48 Random_643_genes: 0.36 top_lfc_643_genes: 0.429 GLM_R_3012_genes: 0.426

We also changed Figure 2b to show box-plots showing distribution of recall values for specific precision windows instead of maximum recall. For ease of checking, the figure is reproduced below.

Author response image 3.

(d) The claim is that Boruta genes are different from differentially expressed genes but the differential expression seems to be estimated without regards to cancer type, which would certainly be highly biased and misleading. Why not do a simple regression of gene expression by ecDNA status, cancer type and select the genes that show significant coefficient for ecDNA status?

Response. As requested by the reviewer, and in the more detailed questions below, we added an alternative model with a generalized linear model (GLM) analysis that controlled for tumor subtype. The method itself is described in the Methods section and pasted below. The GLM genes were tested along with the LFC, CorEx, Core genes as described in response to the previous question, and those results are now presented in Figure 2b and on pages 6 and 7 of the revised manuscript.

“We tested each of 16,309 genes independently in a separate logistic regression model using the glm() function in the R stats package (v4.2.0), and retained genes that were significant (p-value 0.01). Specifically, the model was defined as glm(𝑦 ~ 𝑔𝑗 + 𝑡𝑡, data = 𝑀, family = binomial(link = 'logit')), where y is the response vector where 𝑦𝑖=1 if sample 𝑖 ∈ {1, . . . ,870} is ecDNA(+) and 𝑦𝑖 =0 otherwise, 𝑔𝑗 is the vector of expression values for gene j ∈ {1, . . . ,16309} in samples 𝑖 ∈ {1,. . . ,870}, t is the covariate vector representing the tumor subtypes of samples 𝑖 ∈ {1, . . . ,870}, and 𝑀 is the data matrix containing values of gene expression, tumor subtype, and ecDNA status for all samples. The equation for the binomial logistic regression described above 𝑝𝑝 is formulated as where p is the probability that the dependent variable y is 1, 𝑋 are the independent variables, and 𝛽 are the coefficients of the model. In this case, k=1 represents independent variable gene j and k=2 represents the tumor subtype covariate t. Of the 16,309 genes tested independently, 3,012 genes were significant at pvalue<0.01.”

(C) After identifying key features (which the authors inappropriate imply to be causal) they perform a series of enrichment/correlative analysis.

Response. We have reviewed the document to ensure that we did not use the word ‘causal.’ If the reviewer can point to specific text, we are happy to change the phrasing.

(a) It is known that ecDNA status associates with poor survival, and so are cell cycle related signal. Then the association between Boruta genes and those processes is entirely expected. Is it not? The same goes for downregulation of immune processes.

Response. We agree with the reviewer that cell cycle related signals and immune related signals are associated with low survival, and so does ecDNA. However, many cellular processes could be associated with low survival (including for example, metabolic processes, protein and DNA biosynthesis, etc.). The unexpected part is that there appear to be only 4 major processes that are upregulated in ecDNA(+) cancers relative to ecDNA(-) cancers, and only one (immune response) that is downregulated.

(b) The association with DSB specifically is interesting. Further analysis or discussion of why this should be would strengthen the work.

Response. We thank the reviewer for their comment, and agree with their perspective. Note that we devoted a fair amount of text to analysis of DSB pathways. Specifically, we parsed the 4 main pathways in Figure 3b, and found our data to suggest that many genes in the classical nonhomologous end joining repair pathway are down-regulated in ecDNA(+) samples relative to ecDNA(-) samples. In contrast, Alternative end-joining and homology directed repair pathways are upregulated. This is a surprising result because c-NHEJ is considered to be an important mechanism of DSB repair. We have some lines in the discussion that address this:

“The DNA damage genes are broadly up-regulated in ecDNA(+) samples, especially in double-strand break repair. Within this broad category of mechanisms, our analysis suggests that alternative DSB repair pathways such as Alt-EJ are preferred relative to classical NHEJ. This is consistent with previous observations of small microhomologies at breakpoint junctions, and has important implications in therapeutic selection that will need to be validated in future experimental studies. We note, however, the microhomology analyses typically study breakpoint junctions, and might ignore double-strand breaks in non-junctional sequences which could be observed, for example at replication-transcription junctions.”

We note that additional experimental work to corroborate these findings is significant effort and will be part of ongoing research in our collaborators’ laboratories.

(c) On page 15, second paragraph, when providing the up versus down CorEx genes, please also provide up versus down for non-CorEx genes as well to get a sense of magnitude.

Response. We thank the reviewer for the comment. We note that Supplementary Table S15 has the complete contingency tables as well as the Fisher Exact Test statistic for all categories. For the specific categories mentioned in the paper, the chi-square tables are reproduced below. As we are citing TableS15 (containing all numbers and the statistic p-value) in the main text, we thought it was better to leave the text as it was.

Category: Inflammation (p-value: 0.005)

CorEx: 18 (UP), 76 (DOWN)

Non-CorEx: 325 (UP), 657 (DOWN)

Category: Leukocyte migration and chemotaxis (p-value: 0.03)

CorEx: 13 (UP), 49 (DOWN)

Non-CorEx: 213 (UP), 410 (DOWN)

Category: Lymphocyte activation (p-value: 0.0075)

CorEx: 23 (UP), 75 (DOWN)

Non-CorEx: 334 (UP), 560 (DOWN)

Category: Cytokine production (p-value: 0.117)

CorEx: 6 (UP), 28 (DOWN)

Non-CorEx: 93 (UP), 208 (DOWN)

(d) The finding that Boruta genes are associated with high mutation burden is intriguing because in general mutation burden is associated with better survival and immunotherapy response. This counter-intuitive result should be scrutinized more to strengthen the work.

Response. We agree with the reviewer that it is an intriguing observation. However, we are cautious in our interpretation. This is for the following reasons (all mentioned in the text):

(1) The total mutation burden was significantly higher in ecDNA(+) samples relative to ecDNA(-) samples (Fig. 5a). However, when controlling for cancer type, only glioblastoma, low-grade gliomas, and uterine corpus endometrial carcinoma continued to show differential total mutational burden (Fig. S7b).

(2) We tested if specific genes were differentially mutated between the two classes (Fig. 5b). For deleterious/high-impact mutations, TP53 was the only gene whose mutational patterns were significantly higher in ecDNA(+) compared to ecDNA(-) (OR 2.67, Bonferroni adjusted p-value 4.22e-07). BRAF mutations, however, were more common in ecDNA(-) samples and were significant to an adjusted p-value < 0.1 (OR 0.27).

(3) In response to another reviewer’s comment, we also tested correlation with variant allele frequencies, and did not find any significant correlation except for TP53. We decided not to include that result in the paper.

These tissue specific cases might be confounding the main observation, but we have placed all of them together so that the reader can gain a better understanding. It is worth noting that the correlation between high TMB and immunotherapy response is also now controversial, and perhaps not true for all cancer types. See for example (https://www.annalsofoncology.org/article/S0923-7534(21)00123-X/fulltext), which suggests that this relationship is not true for Glioma, and in Glioma (which is ecDNA enriched), higher TMB is associated with worse immunotherapy response. Our results are consistent with that finding. We have modified the discussion paragraph to better reflect this.

“Mutation data alone does not provide as clear a picture of the genes involved in ecDNA maintenance. We did observe that the total mutation burden (TMB) was higher in ecDNA(+) samples. However, that relationship is much less clear after controlling for cancer type. High TMB has been positively correlated with sensitivity to immunotherapy52, and better patient outcomes; however, the gene expression patterns suggest that immunomodulatory genes are downregulated in ecDNA(+) samples, and patients with ecDNA(+) tumors have worse outcomes2. Notably, other results have suggested that the correlation between TMB and response to immunotherapy is not uniform, and it can vary across different tumor subtypes53. Specifically, our data is consistent with previous results which showed that Gliomas with high TMB have worse response to immunotherapy relative to gliomas with low TMB53. In general, no collection of gene mutations was predictive of ecDNA status, although mutations in TP53 were more likely in ecDNA(+) samples, and perhaps are an important driver for ecDNA formation5.”

(e) On page 17 "12 of the 47 genes not specifically enriching any known GO biological Process" is confusing. How can individual gene enrich for a GO process?

Response. We agree that the statement was incorrectly phrased. We have changed it to state that “Only 12 of the 47 genes were not included in the gene sets of any enriched GO term.”

Reviewer #2 (Public Review):

In their manuscript entitled "Transcriptional immune suppression and upregulation of double stranded DNA damage and repair repertoires in ecDNA-containing tumors" Lin et al. describe an important study on the transcriptional programs associated with the presence of extrachromosomal DNA in a cohort of 870 cancers of different origin. The authors find that compared to cancers lacking such amplifications, ecDNA+ cancers express higher levels of DNA damage repair-associated genes, but lower levels of immune-related gene programs.

This work is very timely and its findings have the potential to be very impactful, as the transcriptional context differences between ecDNA+ and ecDNA- cancers are currently largely unknown. The observation that immune programs are downregulated in ecDNA+ cancers may initiate new preclinical and translational studies that impact the way ecDNA+ cancers are treated in the future. Thus, this study has important theoretical implications that have the potential to substantially advance our understanding of ecDNA+ cancers.

Strengths

The authors provide compelling evidence for their conclusions based on large patient datasets. The methods they used and analyses are rigorous.

Weaknesses

The biological interpretation of the data remains observational. The direct implication of these genes in ecDNA(+) tumors is not tested experimentally.

Response. We agree with the reviewer that experimental tests would be ideal. Towards that, there are some challenges. The immune system genes cannot be tested in cell line models as they need a tumor microenvironment. Tests of DSB repair mechanisms and cell cycle control can be performed in cell-lines, but not with the TCGA samples which are not available. Some of our collaborators are actively working on these topics, but that extensive experimental work is beyond the scope of this paper.

Reviewer #3 (Public Review):

Summary:

Using a combination of approaches, including automated feature selection and hierarchical clustering, the author identified a set of genes persistently associated with extrachromosomal DNA (ecDNA) presence across cancer types. The authors further validated the gene set identified using gene ontology enrichment analysis and identified that upregulated genes in extrachromosomal DNA-containing tumors are enriched in biological processes like DNA damage and cell proliferation, whereas downregulated genes are enriched in immune response processes.

Major comments:

(1) The authors presented a solid comparative analysis of ecDNA-containing and ecDNA-free tumors. An established automated feature selection approach, Boruta, was used to select differentially expressed genes (DEG) in ecDNA(+) and ecDNA(-) TCGA tumor samples, and the iterative selection process and two-tier multiple hypothesis testing ensured the selection of reliable DEGs. The author showed that the DEG selected using Boruta has stronger predictive power than genes with top log-fold changes.

(2) The author performed a thorough interpretation of the findings with GO enrichment analysis of biological processes enriched in the identified DEG set, and presented interesting findings, including the enrichment in DNA damage process among the genes upregulated in ecDNA(+) tumors.

(3) Overall, the authors achieved their aims with solid data mining and analysis approaches applied to public data tumor data sets.

(4) While it may not be the scope of this study, it will be interesting to at least have some justification for choosing Boruta over other feature selection methods, such as Recursive Feature Elimination (RFE) and backward stepwise selection.

Response. We actually agree with the reviewer that some other feature selection methods could work just as well, and note that the Boruta analysis is not our creation, but a published feature selection method (Kursa, Journal of Statistical Software September 2010, Volume 36, Issue 11). We use Boruta to identify relevant genes, but the bulk of the paper is to understand the biological processes driven by that gene selection. Even if we had chosen another method that performed slightly better, it likely would not change the main conclusions. However, to address the reviewers concerns on over-reliance on one method, we added a different gene list created by a generalized linear model analysis, with the goal of checking if the expression of a gene could predict the ecDNA status of the sample after controlling for tumor subtype. Thus, we tested 5 different genelists in terms of their power in predicting ecDNA. While none of the lists is a great predictor of ecDNA status, the Core and CorEx gene lists are significantly better than the other lists. The Figure below replaces the previous Figure panels 2b and 2c.

Author response image 4.

(1) The authors showed that DESEQ-selected DEGs with top log-fold changes have less strong predictive power and speculated that this may be due to the fact that genes with top log-fold changes (LFC) are confined only to a small subset of samples. It will be interesting to select DEGs with top log-fold changes after first partitioning the tumor samples. For example, randomly partition the tumor samples, identify the DEGs with top LFC, combine the DEGs identified from each partition, then evaluate the predictive power of these DEGs against the Boruta-selected DEGs.

Response. This is a great comment. We added a generalized linear model test for selecting genes whose expression is predictive of ecDNA status. The GLM list described above uses a standard methodology (Analysis of Variance) controls for tumor type as a covariate, and its predictive performance is only slightly better than the Top-|LFC| genes, while improving over a random gene set.

(2) While the authors showed that the presence of mutations was not able to classify ecDNA(+) and (-) tumor samples, it will be interesting to see if variant allele frequencies of the genes containing these mutations have predictive power.

Response. This is a great suggestion. To address the reviewer’s question, we used allelic counts (REFs and ALTs) information from the MC3 variant callset, and calculated allele frequencies of all variants from samples where ecDNA status was available. Next, we conducted a Wilcoxon rank-sum test between VAFs of the ecDNA(+) group and VAFs of the ecDNA(-) group for every mutated gene. We found 1,073 genes with p<0.05, but among them, only TP53 passed the multiple testing correction (padj<0.05, Benjamini-Hochberg). As the results are identical to the tests based solely on presence of mutations, we decided not to include this data.

Reviewer #1 (Recommendations For The Authors):

(A) The presentation should be substantially streamlined.

(B) Preferably use a more intuitive simpler ML approach with fewer parameters to make it more credible. Because there are relatively few samples across numerous cancer types with greater variability in representation, a simpler procedure with transparent controls will be more convincing.

Response. We accept the reviewer’s criticism in that other statistical or ML approaches could potentially have been used, and that some are simpler. However, the test used here directly addresses the question: Find a collection of genes whose expression value is predictive of ecDNA status in the sample. Because the underlying method in the Boruta analysis uses random forests, it can test predictive power without relying on a linearity assumption implicit in other methods. In this revision, we also compare against a Generalized Linear Model (regression analysis) and show that it is less suited to the specific task above. We address the reviewer concerns about specific parameter choices by showing robustness to the specific parameter. All details are provided in the initial questions, and in the revised manuscript.

(C) Avoid using any term implying causality unless you can bring in direct experimental evidence (e.g. mutagenesis experiment followed by ecDNA measurement. Some places you use the word 'maintain ecDNA' and other places 'ecDNA impact'. But these are all associations. How can you distinguish causal genes from downstream effects without additional data?

Response. We note that the word causal does not appear anywhere in the manuscript, and was not intended. Additionally we have revised the manuscript and are open to specific changes requested by the reviewer or the editors.

(D) Along these lines, if Boruta genes are indeed causal, one would expect Boruta-Up genes to be amplified more than expected in the ecDNA+; converse for Boruta-down genes.

Response. We did not understand the reviewer’s question. By “amplified,” if the reviewer means “amplification of transcript level,” then that is exactly what the Boruta analysis is showing. Specifically, for each gene, we have the ability to pick a transcript level cut-off ‘t’ so that samples in which the expression is higher than t are more likely to be ecDNA(+). However, we are not claiming that there is causality, just that the transcript level is (weakly) predictive of the ecDNA status of the sample.

(E) A strawman control should be a simple regression-based gene identification that controls for ecDNA status and cancer type.

Response. We agree that this was a very good suggestion. In the revision, we have applied a GLM, which controls for tumor type. Thus, we have 5 gene-lists (including the Core and CorEx genes). As described in the revised manuscript but also in response to the main comments above, none of the lists are a great predictor. However, the CorEx and Core genes are significantly better at predicting ecDNA status of a sample.

Reviewer #2 (Recommendations For The Authors):

Comments

(1) The analysis hinges on a classification of tumors into ecDNA(+) and ecDNA(-) using AmpliconClassifier. It would be good to know how robust the outcomes are with respect to the performance of AmpliconClassifier - how many false positives and negatives will AmpliconClassifier generate on this dataset and how would this influence the CorEx genes?

Response. This is a very reasonable request. AA has been extensively tested on established cell-lines for its ability in predicting ecDNA status, and this information is published in multiple venues, including Kim, Nature genetics 2020, and shows precision 85% for recall 83%. For completeness, we have reproduced the relevant plot from that paper here, and the relevant text here, but are not including it in the manuscript.

“To evaluate the accuracy of the AmpliconArchitect predictions, we analyzed whole-genome sequencing data from a panel of 44 cancer cell lines, and examined tumor cells in metaphase. We used 35 unique fluorescence in-situ hybridization (FISH) probes in combination with matched centromeric probes (81 distinct “cell-line, probe” combinations) to determine the intranuclear location of amplicons (Supplementary Table 2). Following automated analysis >1,600 images, we observed that 85% of amplicons characterized as ‘Circular’ by whole genome sequencing profile demonstrated an extrachromosomal fluorescent signal, representing the positive predictive value. Of the amplicons corresponding to extrachromosomally located FISH probes, 83% were classified as Circular, representing the sensitivity (Extended Data Fig. 1A).”

Author response image 5.

(2) It is unclear why genes are labeled Boruta genes when they are present in 10 out of 200 runs, this seems like an unexpectedly low number. How did the authors arrive at this number? Do the authors have any ground truth to estimate how well Boruta works in this setting and implementation?

Response. This is a great question and asked by another reviewer as well. Given the weakness of an individual gene as a classifier, its repeated selection in multiple Boruta trials is already a significant event. By requiring a gene to be picked in 5% of the trials (10/200), we were selecting a small, but more robust list of genes. However, to further explore the reviewer’s concerns, we also applied 8 other selection criteria ranging from 5 (of 200 Boruta trials) to 200 of 200 Boruta trials. See Figure below. The number of CorEx genes expectedly decreases with increasing stringency. However, of the 187 GO terms that were enriched by UP-genes, 93 terms (50%) were enriched regardless of the cut-off (see Figure below), and 153 terms (82%) were enriched in at least 5 of the 8 cut-offs. Given that the remaining analysis works on the hierarchy of GO terms and finds 4 GO-categories (Mitotic Cell Cycle, G1/S, G2/M; cell-division; DSB DNA Damage response; and the HOX Gene cluster) enriched by UP-regulated genes, those conclusions would hold regardless of the specific cut-off.

Author response image 6.

The number of GO terms that were enriched by DOWN-regulated genes is smaller, only 73, and falls rapidly for higher cut-offs, with 25 at a cut-off of 15. Therefore we see fewer terms enriched for more stringent cut-offs. However, they all support immune processes. These results do suggest that there are fewer genes that are consistently down-regulated in ecDNA(+) cancers, and expression change in a small number of genes may be sufficient to promote conditions for ecDNA.

We have added the figure as a supplemental figure and have added the following text to the manuscript on pages 17 and 18.

“Any CorEx gene is either a Core gene that was selected as a feature in at least 5% of 200 Boruta trials, or be highly co-expressed with a Core gene. Because the selection criterion of 5% is arbitrary, we also tested robustness with 8 other cut-offs ranging from 5-of-200 to 200-of-200 Boruta trials. The number of CorEx genes expectedly decreases with more stringent cut-offs.

However, of the 187 GO terms that were enriched by 262 CorEx UP-genes using 10 of 200 Boruta trials as the selection criteria, 93 terms (49.7%) were enriched for each cut-off (Fig. S9), and 155 terms (82.9%) were enriched in at least 5 of the 8 cut-offs. Given that our subsequent analyses utilized the hierarchy of GO terms and identified 4 GO-categories enriched by UP-regulated genes, the conclusions would hold regardless of the specific cut-off.”

(3) Authors extend the core gene set with co-expressed genes, arguing that "gene C" would not add predictive power in addition to "gene B" and is therefore not identified as a Boruta gene. However, from its description in the manuscript (summarized: "Boruta [...] selects the highest feature importance score, s, of shadow features as a cut off, and returns features with a higher score than s."), it isn't immediately obvious to me why Boruta would not return both genes B and C. Maybe the authors could explain this better.

Response. We consider the following.

(1) Consider 100 ecDNA(+) and 100 ecDNA(-) samples. Let the expression levels of genes B and C in the data-sets be as described in the figure below; y-axis is the gene expression, and x-axis is just a listing of all samples, with green color denoting ecDNA(+) samples and orange color denoting ecDNA(-) samples.

Author response image 7.

(2) Then, if we choose gene B and a transcript level of 1.25, we have a perfect prediction of ecDNA status because all samples where gene B has a transcript level higher than 1.25 are ecDNA(+) and otherwise they are ecDNA(-). Similarly, using Gene C, we can get perfect predictions. Thus, when Boruta has to select a gene, it will pick either Gene B or Gene C, because picking both will not improve prediction. We can therefore use Boruta to pick one gene, and then co-expression clustering to pick the other gene.

As an example, cluster #3 consists of 21 genes that were up-regulated in ecDNA(+) samples and enriched in cell-cycle related biological processes (Table S3). While these genes were expressed similarly in ecDNA(+) samples, and separately, in ecDNA(-) samples, out of the 21 genes, only 9 genes were selected in at least 10 out of 200 Boruta trials (i.e., Core genes). Of the 12 remaining genes (i.e., CorEx genes), 8 genes were not selected by the Boruta method at all, 3 genes were selected in less than 5 out of 200 Boruta trials, and 1 gene was selected in 9 out of 200 Boruta trials.

Author response image 8.

(4) In Fig 2a, I would like to see the variability of the precision and recall in the main text, not only the maximum values. Authors could plot mean + standard deviation for precision and recall separately, or use S2a/b.

Response. We have replaced Figures 2b and 2c with a combined figure (Fig. 2b) that gives a box-plot describing the distribution of recall values for 5 gene lists: four from the original manuscript, and another gene list created using a Generalized Linear Model (GLM).

Author response image 9.

(5) Since the authors analyze bulk RNA, the gene expression signatures they notice could, in principle, originate from non-tumor cells as well. I do not believe this is the case, however, the paper would be strengthened by an analysis that shows that the difference in expression patterns of the Corex genes between ecDNA(+) and ecDNA(-)-samples does come from tumor cells. One way of showing this would be by using single-cell mRNA-sequencing data, and another way of showing this would be to show that Corex gene-expression correlates with tumor purity in bulk samples.

Response. The reviewer is correct. Unfortunately, our analysis requires data with whole-genome sequencing (WGS) for ecDNA prediction, as well as RNA-seq for transcriptome profiling. The TCGA data-set is the only available data-set with a significant number of samples that includes both WGS and RNA-seq. They have not made tissue samples available for scRNA analysis, to our knowledge. The reviewer raises an important question regarding purity, but testing if CorEx gene expression correlates with tumor purity would require a large range of purity values, something that scientists would avoid when collecting samples.

However, the presence of non-cancer tissue (impurity) could reduce sensitivity of ecDNA detection, and therefore, change the results. To better investigate this, we started with a publication that investigated multiple tumor purity metrics and devised a composite score (CPE; Aran et al., 2015). Using their composite tumor purity, we find that ecDNA(-) samples have slightly lower purity than ecDNA(+) samples (p-value 0.0036; Fig. S2a).

This result is not surprising because one would expect lower detection of ecDNA in less pure samples. The presence of undetected ecDNA in ecDNA(-) samples would confound the results by reducing the discriminating power of genes, but would not give false results. To test this, we measured the expression directionality in CorEx genes in all samples versus samples which had a high tumor purity (CPE 0.8). The results suggest that the p-values of directionality in the pure samples were highly correlated with the expression data from all samples (Fig. S2b).

Author response image 10.

(6) The biological interpretation of the data remains a bit too observational. Can the authors offer an interpretation of the enriched GO terms? And are any of these genes already implicated in ecDNA(+) tumors?

Response. To answer the second question first, prior to our study, the focus was on genes that were amplified on ecDNA. Indeed many oncogenes known to be amplified in cancer are in fact amplified on ecDNA (Turner, Nature 2017, Kim Nature genetics 2020). This study is unique in that it identifies genes whose expression values are predictive of ecDNA(+) status. The Figure below lists 24 genes most frequently amplified on ecDNA from Kim, Nature Genetics 2020. With the exception of EGFR and CDK4, none of these 24 genes was included in the list of the 65 genes reported by us as the most frequently selected genes in the Boruta trials (lowest harmonic rank). Thus, most persistent CorEx genes do not lie on ecDNA. However, they all play important roles in biological processes relevant to cancer pathology including Immune Response, Mitotic cell Cycle, Cell division, and DSB repair. We agree with the reviewer that the results are observational (although statistically significant in populations), and some of our collaborators are actively working to experimentally validate some of these genes. The experimental work, however, is beyond the scope of this paper.

We have added the following statement to the manuscript. “Notably, of the 24 genes most frequently expressed on ecDNA,2 only EGFR and CDK4 were included in the list of 65 genes, suggesting that the most persistent CorEx genes do not themselves appear frequently on ecDNA.”

Author response image 11.

Reviewer #3 (Recommendations For The Authors):

Minor comments:

(1) The authors performed gene ontology enrichment test but referred to it as gene set enrichment analysis. Usually gene set enrichment analysis does not refer to Fischer's exact test-based analysis but rather the one described in Subramanian et al 2005. The term correction should be made to avoid confusion.

Response. We have rephrased text in the manuscript to prevent confusion between enrichment analysis on gene sets using an one-sided Fisher’s exact test and the Gene Set Enrichment Analysis (GSEA) method that exists as a software. We have also revised the header in the methods section from “Gene set enrichment analysis” to “Gene Ontology (GO) enrichment analysis”.

(2) A couple of figures could use more detailed labels and captions. In Figure 2c, it is unclear what the numbers 100 and 54 right next to the Cliff's Delta heatmap indicate. In Figures 3a and 4a, it is not immediately clear what the barplot on top of the heatmap indicates and there is no label for the y-axis.

Response. These are good suggestions, and we have added descriptions to the figure captions.

Author Response

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

First, we would like to thank you and all the reviewers for acknowledging the meaningful contribution of our manuscript to the field. Your useful comments helped us improve the manuscript's quality. We understood the key issues of the manuscript were the quantification of inference accuracy and applicability to methylome data. We here therefore present a revised version of the manuscript addressing all major comments.

For each demographic inference we have added the root mean square error as demanded by the reviewers. These results confirm the previous interpretation of the graphs especially in recent times. We also added TMRCA inference analysis as requested by one reviewer as a proof of principle that integrating multiple markers can improve ARG inference.

The discussion was rewritten to further discuss the challenges of application to empirical methylation data. We clarify that in the case epimutations are well understood and modelled, they can be integrated into a SMC framework to improve the approaches accuracy. When epimutations are not well understood, our approach can help understand the epimutations process through generations at the evolutionary time scale along the genome. Hence, in both cases our approach can be used to unveil marker evolution processes through generations, and/or deepen our understanding of the population past history. We hope our discussion underlies better how our approach is designed and can be used.

eLife assessment

This important study advances existing approaches for demographic inference by incorporating rapidly mutating markers such as switches in methylation state. The authors provide a solid comparison of their approach to existing methods, although the work would benefit from some additional consideration of the challenges in the empirical use of methylation data. The work will be of broad interest to population geneticists, both in terms of the novel approach and the statistical inference proposed.

Public Reviews:

Reviewer #1 (Public Review):

The authors developed an extension to the pairwise sequentially Markov coalecent model that allows to simultaneously analyse multiple types of polymorphism data. In this paper, they focus on SNPs and DNA methylation data. Since methylation markers mutate at a much faster rate than SNPs, this potentially gives the method better power to infer size history in the recent past. Additionally, they explored a model where there are both local and regional epimutational processes.

Integrating additional types of heritable markers into SMC is a nice idea which I like in principle. However, a major caveat to this approach seems to be a strong dependence on knowing the epimutation rate. In Fig. 6 it is seen that, when the epimutation rate is known, inferences do indeed look better; but this is not necessarily true when the rate is not known. A roughly similar pattern emerges in Supp. Figs. 4-7; in general, results when the rates have to be estimated don't seem that much better than when focusing on SNPs alone. This carries over to the real data analysis too: the interpretation in Fig. 7 appears to hinge on whether the rates are known or estimated, and the estimated rates differ by a large amount from earlier published ones.

Overall, this is an interesting research direction, and I think the method may hold more promise as we get more and better epigenetic data, and in particular better knowledge of the epigenetic mutational process. At the same time, I would be careful about placing too much emphasis on new findings that emerge solely by switching to SNP+SMP analysis.

Answer: We thank the reviewer 1 for his positive comments and acknowledging the future promises of our method as better and more reliable data will be available in different species. We appreciate the reviewer noticing the complete set of work undertaken here to integrate local and regional effects of methylation into a model containing as much knowledge of the epigenetics mutational processes as possible. Note that in Figure 2 of the manuscript we observed a gain of accuracy even when the rates are unknown. Our results thus suggests that the accuracy gain of additional marker with unknown rates is also possible, although it is most likely be scenario and rate dependent.

At last, as noticed and highlighted by the very recent work of the Johannes lab (Yao et al. Science 2023) using phylogenetic methods, knowing the epimutation rate is essential at short time scale to avoid confounding effects of homoplasy. In our estimation of the coalescent trees, the same applies, though our model considers finite site markers. We now provide additional evidence for the potential gain of power to infer the TMRCA (Supplementary Table S7) when knowing or not the epimutation rates and revised the discussion to clarify the potential shortcomings/caveats for the analysis of real data.

Reviewer #2 (Public Review):

A limitation in using SNPs to understand recent histories of genomes is their low mutation frequency. Tellier et al. explore the possibility of adding hypermutable markers to SNP based methods for better resolution over short time frames. In particular, they hypothesize that epimutations (CG methylation and demethylation) could provide a useful marker for this purpose. Individual CGs in Arabidopsis tends to be either close to 100% methylated or close to 0%, and are inherited stably enough across generations that they can be treated as genetic markers. Small regions containing multiple CGs can also be treated as genetic markers based on their cumulative methylation level. In this manuscript, Tellier et al develop computational methods to use CG methylation as a hypermutable genetic marker and test them on theoretical and real data sets. They do this both for individual CGs and small regions. My review is limited to the simple question of whether using CG methylation for this purpose makes sense at a conceptual level, not at the level of evaluating specific details of the methods. I have a small concern in that it is not clear that CG methylation measurements are nearly as binary in other plants and other eukaryotes as they are in Arabidopsis. However, I see no reason why the concept of this work is not conceptually sound. Especially in the future as new sequencing technologies provide both base calling and methylating calling capabilities, using CG methylation in addition to SNPs could become a useful and feasible tool for population genetics in situations where SNPs are insufficient.

Answer: We thank the reviewer 2 for his positive comments. Indeed, surveys of CG methylation in other plant species show that its distribution is clearly bimodal (i.e. binary). This is not the case for non-CG methylation, such as CHG and CHH (where H=C,T,A). However, these later types of methylation contexts are also not heritable across generations and can therefore not be used as heritable molecular markers.

Reviewer #3 (Public Review):

I very much like this approach and the idea of incorporating hypervariable markers. The method is intriguing, and the ability to e.g. estimate recombination rates, the size of DMRs, etc. is a really nice plus. I am not able to comment on the details of the statistical inference, but from what I can evaluate it seems sound and reasonable. This is an exciting new avenue for thinking about inference from genomic data. I have a few concerns about the presentation and then also questions about the use of empirical methylation data sets.

I think a more detailed description of demographic accuracy is warranted. For example, in L245 MSMC2 identifies the bottleneck (albeit smoothed) and only slightly overestimates recent size. In the same analysis the authors' approach with unknown mu infers a nonexistent population increase by an order of magnitude that is not mentioned.

Answer: We thank the reviewer 3 for his positive comments and refer to our answer to reviewer 1 above. We added RMSE (Root Mean Square Error) analyses to quantify the inference accuracy. We apologize for not mentioning this last point. Thank you for pointing this out and we have now fixed it (line 245-253).

Similarly, it seems problematic that (L556) the approach requiring estimation of site and region parameters (as would presumably be needed in most empirical systems like endangered nonmodel species mentioned in the introduction) does no better than using only SNPs. Overall, I think a more objective and perhaps quantitative comparison of approaches is warranted.

Answer : See answer to reviewer 1 above, and more elaborate answers below. We provide now new RMSE analyses to quantify the accuracy of our demographic inference (Supplementary Tables 1,6,7,8,9,10). We also discuss the validity and usefulness of our approach when the epimutation rates are unknown. In short, the discussion was rewritten to further discuss the challenges of application to empirical methylation data. We clarify that in the case epimutations are well known and modelled (as much is known in A. thaliana for example), they can be integrated into a SMC framework to improve the accuracy of the method approach. When epimutations are not well understood and rates unknown, our approach can help understand the epimutational process through generations at the evolutionary time scale. Hence, whether makers are understood or not, our approach can be used to study the marker evolutionary processes through generations and/or to deepen our understanding of the population past history. We hope our discussion underlies better how our approach is designed and can be used.

The authors simulate methylated markers at 2% (and in some places up to 20%). In many plant genomes a large proportion of cytosines are methylated (e.g. 70% in maize: https://www.ncbi.nlm.nih.gov/pmc/articles/PMC8496265/). I don't know what % of these may be polymorphic, but this leads to an order of magnitude more methylated cytosines than there are SNPs. Couldn't this mean that any appreciable error in estimating methylation threatens to be of a similar order of magnitude to the SNP data? I would welcome the authors' thoughts here.

Answer : The reviewer is correct and this is an interesting question. First, studies show that heritable epimutations in plants are restricted to CG dinucleotides that are located well outside of the target regions of de novo methylation pathways in plants. Most of these CGs tend of fall within so-called gene body methylated regions. While it is true that plant species can differ substantially in their proportion of methylation at the genome-wide scale, the number of gene body methylated genes (i.e. genic CG methylation) is relatively similar, and at least well within the same order of magnitude (Takuno et al. Nature Plants 2016, review in Muyle et al. Genome Biol Evol 2022). Moreover, spontaneous CG epimutations in gene body methylated regions has been shown to be neutral (van Der Graaf et al. 2015, Vidali et al. 2016, Yao et al. 2023), which is an ideal property for phylogentic and demographic inference.

Second, CG methylation calls are sometimes affected by coverage or uncertainty. Stringent filtering for reliable SMP calls typically reduces the total proportion of CG sites that can be used as input for demographic inference. Here we only kept CG sites where the methylation information could be fully trusted after SMP calling (i.e. >99.9% posteriori certainty). Overall, this explains why the percentage of sites with methylation information is so small, and why we have decided to work on simulation with 2% of reliable methylated markers.

Nevertheless, for the sake of generality, it may be that in some species such as maize a higher percentage of polymorphic methylated sites can be used, and the number of SMPs could be higher than that of SNPs when the effective population size is very small (due to past demographic history and/or life history traits). In this case, any error in the epimutation rate and variance due to the finite site model estimation (and homoplasy) are not corrected by the lack of SNPs and can lead to mis-inference.

A few points of discussion about the biology of methylation might be worth including. For example, methylation can differ among cell types or cells within a tissue, yet sequencing approaches evaluate a pool of cells. This results in a reasonable fraction of sites having methylation rates not clearly 0 or 1. How does this variation affect the method? Similarly, while the authors cite literature about the stable inheritance of methylation, a sentence or so more about the time scale over which this occurs would be helpful.

Answer: We thank reviewer 3 for asking those very interesting questions, which we further developed below and mention in the discussion (lines 716-722).

For Arabidopsis thaliana:

Following up on our previous comment above, the majority of the CG sites that serve as input to our approach are located in body methylated genes. Previous work has shown that CG methylation in these regions shows essentially no tissue and cellular heterogeneity (e.g. Horvath et al. 2019). This means that bulk methylation measurements only show limited susceptibility to measurement error. That said, to guard against any spurious SMPs call that could arise from residual measurement variation, we applied stringent filtering of CG methylation. We have kept sites where the methylation percentage is close to either 0% or 100% (the rest being removed from the analysis). We have used similar filtering strategies in previous studies of epimutational processes in mutation accumulation lines and long-lived perennials (work of the Johannes lab). In these later studies we found that the SMP calls sufficiently accurate for inferences of phylogenetic parameters in experimental settings (Sharyhary et al. Genome Biology 2021, Yao et al. Science, 2023).

For other species:

It is true that currently, evaluating the methylation state of a site from a pool of cells may be problematic for some species for two main reasons: 1) it will add noise to the signal and SMP calling could be erroneous, and 2) the methylation state used in analysis might originate from different tissues at different location of the genome/methylome. Overall, this will lead to spurious SMPs and can render the inference inaccurate (see Sellinger et al 2021 for the effect of spurious SNPs). Hence, caution is advised when calling SMPs in other species and for different tissues.

Finally, in some species methylated cytosines have mutation rates an order of magnitude higher than other nucleotides. The authors mention they assume independence, but how would violation of this assumption affect their inference?

Answer: Indeed, we assume the mutation and epimutation process to be independent thus the probability for a SNP to occur does not depend on the local methylation state. If this was the case, the mutation rate use would indeed be wrong to a degree function of the dependency between the processes. We suggest that by ignoring this dependence, we are in the same situation as ignoring the variation of mutation rate along the genome. We have previously documented the effect of ignoring this biological feature of genomes in Strüt et al 2023 and Sellinger et al 2021. The variation in mutation rate along the genome if too extreme and not accounted for can lead to erroneous inference results. However, this problem could be easily solved (modelled) by adapting the emission matrix. To correctly model this dependency, additional knowledge is needed: either the mutation and epimutation rates must be known to quantify the dependency, or the dependency must be known to quantify the resulting rates. As far as we know, these data are at the moment not available, but could maybe be obtained using the MA lines of A. thaliana (used in Yao et al. 2023).

Recommendations for the authors:

All three reviewers liked this approach and found it a valuable contribution. I think it is important to address reviewer 1/3 concerns about quantifying the accuracy of inference (the TMRCA approach from reviewer 1 sounds pretty reasonable), and reviewer 1 also highlights an intriguing point about model accuracy being worse when the mutation rate is known. Additionally, I think some discussion is warranted about challenges dealing with empirical methylation data (points from Rev 2 and 3 as well as Rev 1's question about inferred vs published rates of epigenetic mutation).

Answer : We have added tables containing the root mean square error (RMSE) of every demographic inference in the manuscript to better quantify accuracy. We have below given the explanation on why accuracy in presence of site and region epimutations can in some cases decrease when real rates are known (because methylation state at the region level needs to be first inferred). We added evidence that accounting for methylation can improve the accuracy when recovering the TMRCA along the genome when the rates are known. We also have enhanced the discussion on the challenges of dealing with epimutations data for inference. As is suggested, we hope this study will generate an interest in tackling these challenges by applying the methods to various methylome datasets from different species.

Reviewer #1 (Recommendations For The Authors):

Major comments:

• For all of the simulated demographic inference results, only plots are presented. This allowsfor qualitative but not quantitative comparisons to be made across different methods. It is not easy to tell which result is actually better. For example, in Supp. Fig. 5, eSMC2 seems slightly better in the ancient past, and times the trough more effectively, while SMCm seems a bit better in the very recent past. For a more rigorous approach, it would be useful to have accompanying tables that measure e.g. mean-squared error (along with confidence intervals) for each of the different scenarios, similar to what is already done in Tables 1 and 2 for estimating $r$.

Answer : We understand the concern of reviewer #1 for a more quantitative approach to compare the inference results. We agree that plots are not sufficient to fully grasp a method performance. To provide better supports to quantity approaches performance, we added Sup tables 1,6,8,9 and 10 containing the RMSE (in log10 for visibility) for all Figures. The root mean-squared error is calculated as in Sellinger 2021 and a description of how the root mean-squared error is calculated and now found in the method section lines 886-893.

• 434: The discussion downplays the really odd result that inputting the true value of themutation rate, in some cases, produces much worse estimates than when they are learned from data (SFig. 6)! I can't think of any reason why this should happen other than some sort of mathematical error or software bug. I strongly encourage the authors to pin down the cause of this puzzling behaviour.

Answer : There are unfortunately no errors in this plot and those results are perfectly normal and coherent, but we understand they can be confusing at first.

As described in the method section and in the appendix, when accounting for regionlevel epimutations, our algorithm requires the regional methylation status which needs to be inferred as a first step from the data (real or simulated). Because region and single site epimutation events are occurring at similar rates in our simulated scenario, the methylation state of the region is very hard to correctly recover (e.g. there will be unmethylated site in methylated regions and methylated sites in unmethylated regions). In other words, the accuracy of the region estimation HMM procedure is decreased by the joint action of site and region epimutation processes.

When subsequently applying the HMM for inference, as described in the appendix, the probabilities of two CG site being in the same or different methylation state depends on the methlylation state of the "region". Hence the mislabelling of the region methylation state is (to some extent) equivalent to spurious SMPs (or inaccurate SMP calling).

If the true rates for site and region epimutations are given as input, the model forces the demography (and other inferred parameters) to fit the observed distribution of SMPs (given the inputted rates), resulting in the poor accuracy observed in the Figure (Now Supplementary Figure 7).

Note: The estimated rates from real data in A. thaliana suffer from the same issue as the region and site epimutation rates are independently estimated, and the existence of regions first quantified using an independent HMM method (Denkena et al. 2022).

However, when rates are freely inferred, they are inferred accordingly to the estimated methylation status of regions and SNPs. Therefore, even if the inferred rates are wrong, they are used by the SMC in a more consistent way.

Note: When methylation rates violate the infinite site assumption, such as here, we first estimate the tree sequence along the genome using SNPs (i.e. DNA mutations). The algorithm then infers the epimutations rates given the inferred coalescent times and the observed methylation diversity.

To summarise: when inputting rates to the model, if the model fails to correctly recover the region methylation status there will be conflicting information between SNPs and SMPs leading to accuracy loss. However if the rates are inferred this is realized with the help of SNPs, leading to less conflicting information and potentially smaller loss of accuracy. We apologize that the explanations were missing from the manuscript and have added them lines 449-460 and 702-716.

A further argument is that if region and site epimutations occur at rates of at least two orders of magnitude difference, the inference results are better (and accurate) when the true rates are given. The reason is that one epimutational process overrides the other (see Supplementary Table 2). In that case one epimutation process is almost negligible and we fall back to results from Figure 5 or Supplementary Figure 6.

• As noted at 580, all of the added power from integrating SMPs/DMRs should come fromimproved estimation of recent TMRCAs. So, another way to study how much improvement there is would be to look at the true vs. estimated/posterior TMRCAs. Although I agree that demographic inference is ultimately the most relevant task, comparing TMRCA inference would eliminate other sources of differences between the methods (different optimization schemes, algorithmic/numerical quirks, and so forth). This could be a useful addition, and may also give you more insight into why the augmented SMC methods do worse in some cases.

Answer : We fully agree with reviewer 1. We have added a comparison in TMRCA inference as proof of principle between using or not using methylation sites. The results are written in Supplementary Table 7 and methodology is inspired by Schiffels 2014 and described at the end of the method section (line 894-907). Those results demonstrate the potential gain in accuracy when using methylation polymorphic. However, TMRCA (or ARG) inference is a very vast and complex subject in its own right. Therefore, we are developing a complete TMRCA/ARG inference investigation and an improve methodology than the one presented in this manuscript. To do so we are currently working on a manuscript focusing on this topic specifically. We hence consider further investigations of TMRCA/ARG inference beyond the scope of this current study.

• A general remark on the derivations in Section 2 of the supplement: I checked theseformulas as best I could. But a cleaner, less tedious way of calculating these probabilities would be to express the mutation processes as continuous time Markov chains. Then all that is needed is to specify the rate matrices; computing the emission probabilities needed for the SMC methods reduces to manipulating the results of some matrix exponentials. In fact, because the processes are noninteracting, the rate matrix decomposes into a Kronecker sum of the individual rate matrices for each process, which is very easy to code up. And this structure can be exploited when computing the matrix exponential, if speed is an issue.

Answer: We thank the reviewer for this very interesting suggestion! Unfortunately, it is a bit late to re-implement the algorithm and reshape the manuscript according to this suggestion. Speed is not yet an issue but will most likely become one in the future when integrating many different rates or when using a more complex SMC model. Hence, we added reviewer #1 suggestions to the discussion (line 648) and hope to be using it in our future projects.

• Most (all?) of the SNP-only SMC methods allow for binning together consecutiveobservations to cut down on computation time. I did not see binning mentioned anywhere, did you consider it? If the method really processes every site, how long does it take to run?

Answer: This is a very good question. We do the binning exactly as described in Mailund 2013 & Terhorst 2017, and added this information in the method section (lines 801-809). However, as described in Terhorst 2017, one can only bin observation of the same "type" (to compute the Baum-Welch algorithm). Therefore, the computation time gain by binning is reduced when different markers spread along the genome in high proportion. This is the approach we used throughout the study when facing multiple markers as it had the best speed performance. As for example, when the proportion of site with methylated information is 1% or less, computation time is only slightly affected (i.e. same order of magnitude).

However, the binning method presented in Mailund 2013 can be extended to observation of different types, but parameters need to be estimated through a full likelihood approach (as presented in Figure 2). In our study this approach did not have the best speed performance. However, as our study is the first of its kind, it remains sub-optimal for now. Hence, we did not further investigate the performance of our approach in presence of many multiple different genomic marker (e.g. 5 different markers each representing ~20% of the genome each). Currently, with SMC approaches a high proportion of sites contain the information "No SNPs", making the Baum welch algorithm described in Terhorst 2017 very efficient. But when further developing our theoretical approach, we expect that most of the sites in a genome analysis will contain some "information", which could render the full likelihood approach computationally more tractable.

• 486: The assumed site and region (de)methylation rates listed here are several OOMdifferent from what your method estimated (Supp. Tables 5-6). Yet, on simulated data your method is usually correct to within an order of magnitude (Supp. Table 4). How are we to interpret this much larger difference between the published estimates and yours? If the published estimates are not reliable, doesn't that call into question your interpretation of the blue line in Fig. 7 at 533?

Answer: We thank the reviewer for asking this question. We believe answering this question is indeed the most interesting aspect of our study. Beyond demographic inference, our study has indeed unveiled a discrepancy between rates inferred through biological experiment and our study through the use of SNPs and branch length. There are several reasons which could explained the discrepancy between both approaches:

• Firstly, our underlying HMM hypotheses are certainly violated. We ignoredpopulation structure, variation of mutations and recombination rate along the genome as well as the effect of selection. Hence, the branch lengths used for methylation rate estimations are to some extent inaccurate. We note that this is especially likely for the short branches of coalescent tree originating from background selection events in the coding regions and which are especially observable when using the methylation sites with a higher mutation rate than SNPs (Yao et al. 2023) at body methylated genes.

• Secondly, calling single methylation site polymorphism is not 100 % reliable. If theerror rate is 0.1%, as the study was conducted on ~10 generations a minimum epimutation rate of 10-4 is to be expected. However, because our approach works at the evolutionary time scale, we expect that it suffers less from this bias as the proportion of diversity originating from actual epimutations, and not SMP calling error, should be greater.

• Thirdly, as mentioned above, recovering the methylation status of a region is veryhard. Hence false region status inference could affect our inference accuracy as shown in Supplementary Figure 4.

• Lastly and most importantly, the reason behind this discrepancy is the modelling ofepimutation and methylation between sites and regions. As we discuss, the current combination of rates and models is still limited to describe the observed diversity along the genome (as we intend in SMC methods). This is in contrast to the recent study by Yao et al. where very few regions of polymorphic SMPs are chosen, which implicitly avoids the influence of the methylation region effect. A study just published by Biffra et al. (Cell reports 2023) also uses a functional model of methylation modelling using a mix of region and site epimutation, albeit not tuned for evolutionary analyses. Thus we suggest, in line with functional studies, that epimutations are not independent from the local methylation context and may tend to stabilize the methylation state of a region. Therefore, the estimated methylation rates show a discrepancy to the previously measured ones. Indeed, the biological experiment would reveal a fast epimutation rate because epimutations can actually be tracked at sites which can mutate, while region mutation rate is much slower. However, because the methylation state of a region is rather stable through time it would reduce the methylation diversity over long time scale, and these rates would differ between methylated or unmethylated regions (i.e. the methylation rate is higher in methylated regions). Our results are thus in agreement with the observation by Biffra et al. that region methylation modelling is needed to explain patterns of methylation across the genome.

To solve the discrepancy, one would need to develop a theoretical region + site epimutation model capable of describing the observed diversity at the evolutionary time scale (possibly based on the Biffra et al. model within an underlying population evolution model), and then use this model to reanalyse the sequence data from the biological experiment (i.e. in de Graaf et al. 2015 & Denkena et al. 2022) to re-estimate the methylation region sizes and epimutation rates.

Minor comments:

• 189: "SMCtheo" first occurs here, but it's not mentioned until 247 that this is the newmethod being presented.

Answer : Fixed

• 199: Are the estimates in this section from a single diploid sequence? Or is it n=5 (diploid) as mentioned in the earlier section?

Answer : Yes, those results were obtained with 5 diploid individuals. We added it in the Table 1 description.

• 336: I'm confused by the wording: it sounds like the test rejects the null if there is positivecorrelation in the methylation status across sites. But then, shouldn't 339 read "if the test is significant" (not non-significant)?

Answer : We apologize for the confusion and rewrote the sentence line 339-348, the choice of word was indeed misleading .

• Fig. 6: for some reason fewer simulations were run for 10Mb (panels C nad D) than for100Mb (A and B). Since it's very difficult to tell what's happening on average in the 10Mb case, I suggest running the same number of simulations.

Answer : Yes we understand your concern. Actually, the same number of simulations were run but we plotted only the first 3 runs as it was less visually confusing. We now have added the missing lines to the plot C and D.

Typos:

• 104: "or or"

• 292: build => built

• 388: fulfil

• 683: sample => samples

Answer : Many thanks to reviewer 1 for pointing out the typos. They are all now fixed.

Reviewer #2 (Recommendations For The Authors):

The authors may find some valuable information in Pisupati et al (2023) "On the causes of gene-body methylation variation in Arabidopsis thaliana" on interpreting epimutation rates.

Answer: Many thanks for the recommended manuscript. We add it to the cited literature as it strongly supports our use of heritability or methylation. We also added the recent Biffra et al. paper.

Reviewer #3 (Recommendations For The Authors):

There are many places throughout the manuscript with minor grammatical errors. Please review these. A few noted below as I read:

L104: extra "or"

L123: built not build

L 160 "relies" instead of "do rely"

L161 "events"

L 336 "from methylation data"

L 378 "exists"

L 379 "regions are on average shorter" instead of "there are shorter"

L 338 "a regional-level"

L 349 "," instead of "but"

L 394 DMRs

Table 1 legend: parentheses not brackets?

Answer : Many thanks to reviewer #3 for finding those mistakes. They are all now fixed.

I think a paragraph in the discussion of considerations of when to use this approach might be helpful to readers. Comparison to e.g. increased sample size in MSMC2, while not necessary, might be helpful here. It may often be the case that doubling the number of haplotypes with SNP data may be easier and cheaper estimating methylation accurately.

Answer : We discuss (lines 691-698) that our approach is always useful by design, but cannot always be used for the same purpose. If the evolutionary properties of the used marker used are not understood, we suggest that our approach can be used to investigate the marker heritability process through generations. This could help to correctly design experiments aiming to study the marker heritability through lineages. And if the properties of the marker are well understood and modelled, it can be integrated into the SMC framework to improve inference accuracy.

Other minor notes:

L 486 "known" is a stretch. empirically estimated seems appropriate.

Answer : Fixed

L 573 ARG? You are not estimating the full ARG here.

Answer : We apologize for the wrong choice of word and have rephrased the sentence.

Fig. 2 is not super useful and could be supplemental.

Answer : We moved Figure 2 to the appendix (now sup fig 1)

Author Response

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

Reviewer #1 (Public Review):

Summary:

This study examines the role of host blood meal source, temperature, and photoperiod on the reproductive traits of Cx. quinquefasciatus, an important vector of numerous pathogens of medical importance. The host use pattern of Cx. quinquefasciatus is interesting in that it feeds on birds during spring and shifts to feeding on mammals towards fall. Various hypotheses have been proposed to explain the seasonal shift in host use in this species but have provided limited evidence. This study examines whether the shifting of host classes from birds to mammals towards autumn offers any reproductive advantages to Cx. quinquefasciatus in terms of enhanced fecundity, fertility, and hatchability of the offspring. The authors found no evidence of this, suggesting that alternate mechanisms may drive the seasonal shift in host use in Cx. quinquefasciatus.

Strengths:

Host blood meal source, temperature, and photoperiod were all examined together.

Weaknesses: The study was conducted in laboratory conditions with a local population of Cx. quinquefasciatus from Argentina. I'm not sure if there is any evidence for a seasonal shift in the host use pattern in Cx. quinquefasciatus populations from the southern latitudes.

We agree on the reviewers observation about the evidence on seasonal shift in the host use pattern in Cx. quinquefasciatus populations from southern latitudes. We include a paragraph in the Introduction section regarding this. Unfortunately, studies conducted in South America to understand host use by Culex mosquitoes are very limited, and there are virtually no studies on the seasonal feeding pattern. In Argentina, there is some evidence (Stein et al., 2013, Beranek, 2019) regarding the seasonal change in host use by Culex species, including Cx. quinquefasciatus, where the inclusion of mammals during the autumn has been observed. As part of a comprehensive study on characterising bridge vectors for SLE and WN viruses, our research group is currently working on the molecular identification of blood meals from engorged females to gain deeper insights into the seasonal feeding pattern of Culex mosquitoes. While the seasonal change in host use by Culex quinquefasciatus has not been reported in Argentina so far, there has been an observed increase in reported cases of SLE virus in humans between summer and fall (Spinsanti et al., 2008). It is based on this evidence that we hypothesise there is a seasonal change in host use by Cx. quinquefasciatus, similar to what occurs in the United States. This is also considering that both countries (Argentina and the United States) have regions with similar climatic conditions (temperate climates with thermal and hydrological seasonality). Since we work on the same species and in a similar temperate climate regimen, we assumed there is a seasonal shift in the host use by this mosquito species.

Reviewer #1 (Recommendations for the authors):

Abstract

Line 23: fed on two different hosts.

Accepted as suggested.

I think the concluding statement should be rewritten to say that immediate reproductive outcomes do not explain the shift in host use pattern of Cx. quinquefasciatus mosquitoes from birds to mammals towards autumn.

Accepted as suggested.

Introduction

No comments.

Materials and Methods

Please mention sample sizes in the text as well (n = ?) for each treatment.

Accepted as suggested.

Page 99: ......C. quinquefasciatus, since C. pipiens and its hybrids are present as well in Cordoba.

Accepted as suggested.

Results – Line 146: subsequently instead of posteriorly

Accepted all changes as suggested.

Line 148: were counted instead of was counted.

Accepted all changes as suggested.

Line 160: Subsequently instead of posteriorly

Accepted all changes as suggested.

Line 171: on fertility

Accepted all changes as suggested.

Line 174: there was an interaction effect on…

Accepted all changes as suggested.

Line 175: there were no differences in the number of eggs

Accepted all changes as suggested.

Discussion

I think the first paragraph in the discussion section is redundant and should be deleted.

The whole discussion was rewritten to be focused on our aims and results.

Line 282: this sentence needs to be rewritten.

Accepted as suggested.

Line 299: at 28{degree sign}C

Line 300: at 30{degree sign}C

Sorry, but we are not sure about your comment here. We checked. Temperatures are written as stated, 28°C and 30°C.

Line 363: I think the authors need to discuss more about the bigger question they were addressing. I think that the discussion section can be strengthened greatly by elaborating on whether there is evidence for a seasonal shift in host use pattern in Cx. quinquefasciatus in the southern latitudes. If yes, what alternate mechanisms they believe could be driving the seasonal change in host use in this species in the southern latitudes now that they show the 'deriving reproductive advantages' hypothesis to be not true for those populations.

Thanks for this observation. We agree and so the Discussion section was restructured to align it with our results, as suggested.

Reviewer #2 (Public Review):

Summary:

Conceptually, this study is interesting and is the first attempt to account for the potentially interactive effects of seasonality and blood source on mosquito fitness, which the authors frame as a possible explanation for previously observed host-switching of Culex quinquefasciatus from birds to mammals in the fall. The authors hypothesize that if changes in fitness by blood source change between seasons, higher fitness in birds in the summer and on mammals in the autumn could drive observed host switching. To test this, the authors fed individuals from a colony of Cx. quinquefasciatus on chickens (bird model) and mice (mammal model) and subjected each of these two groups to two different environmental conditions reflecting the high and low temperatures and photoperiod experienced in summer and autumn in Córdoba, Argentina (aka seasonality). They measured fecundity, fertility, and hatchability over two gonotrophic cycles. The authors then used a generalized linear mixed model to evaluate the impact of host species, seasonality, and gonotrophic cycle on fecundity and fertility and a null model analysis via data randomization for hatchability. The authors were trying to test their hypothesis by determining whether there was an interactive effect of season and host species on mosquito fitness. This is an interesting hypothesis; if it had been supported, it would provide support for a new mechanism driving host switching. While the authors did report an interactive impact of seasonality and host species, the directionality of the effect was the opposite of that hypothesized. While this finding is interesting and worth reporting, there are significant issues with the experimental design and the conclusions that are drawn from the results, which are described below. These issues should be addressed to make the findings trustworthy.

Strengths:

(1) Using a combination of laboratory feedings and incubators to simulate seasonal environmental conditions is a good, controlled way to assess the potentially interactive impact of host species and seasonality on the fitness of Culex quinquefasciatus in the lab.

(2) The driving hypothesis is an interesting and creative way to think about a potential driver of host switching observed in the field.

Weaknesses:

(1) There is no replication built into this study. Egg lay is a highly variable trait, even within treatments, so it is important to see replication of the effects of treatment across multiple discrete replicates. It is standard practice to replicate mosquito fitness experiments for this reason. Furthermore, the sample size was particularly small for some groups (e.g. 15 egg rafts for the second gonotrophic cycle of mice in the autumn, which was the only group for which a decrease in fecundity and fertility was detected between 1st and 2nd gonotrophic cycles). Replicates also allow investigators to change around other variables that might impact the results for unknown reasons; for example, the incubators used for fall/summer conditions can be swapped, ensuring that the observed effects are not artefacts of other differences between treatments. While most groups had robust sample sizes, I do not trust the replicability of the results without experimental replication within the study.

We agree egg lay is a variable trait and so we consider high numbers of mosquitoes and egg lay during experiments compared to our studies of the same topics. Evaluating variables such as fecundity, fertility, or other types of variables (collectively referred to as "life tables") is a challenging issue that depends on several intrinsic and extrinsic factors. Because all of this, in some experiments, sample sizes might not be very large, and in several articles, lower sample sizes could be found. For instance, in Richards et al. (2012), for Culex quinquefasciatus, during the second gonotrophic cycle, some experiments had 13 or even 6 egg rafts. For species like Aedes aegypti, the sample size for life table analysis is also usually small. As an example, Muttis et al. (2018) reported between 1 and 4 engorged females (without replicates). In addition, small sample size would be a problem if we would not have obtained any effect, which is not the case due to the fact that we were interested in finding an effect, regardless of the effect size. Because of this, we do find our sample sizes quite robust for our results.

Regarding the need to repeat the experiments in order to give more robustness to the study we also agree. However, after a review of the literature (articles cited in the original manuscript), it is apparent that similar experiments are not frequently repeated as such. Examples of this are the studies of Richards et al. (2012), Demirci et al. (2014) or Telang & Skinner (2019), which even they manipulate several cages at a time as “replicates”, they are not true replicates because they summarise and manipulate all data together, and do not repeat the experiment several times. We see these “replicates” as a way of getting a greater N.

As was stated by the reviewer, repetition is a resource and time-consuming activity that we are not able to do. Replicating the experiment poses a significant time and resources challenge. The original experiment took over three months to complete, and it is anticipated that a similar timeframe would be necessary for each replication (6 months in total considering two more replicates). Given our existing commitments and obligations, dedicating such an extensive period solely to this would impede progress on other crucial projects and responsibilities.

Given the limitations of resources and time and the infrequent use of experimental replication in this type of studies, we performed a simulation-based analysis via a Monte Carlo approach. This approach involved generating synthetic data that mimics the expected characteristics of the original experiment and subsequently subjecting it to the same analysis routine. The main goal of this simulation was to evaluate the potential spuriousness and randomness of the results that might arise due to the experimental conditions. So, evaluating the robustness and confidence of our results and data.

(2) Considering the hypothesis is driven by the host switching observed in the field, this phenomenon is discussed very little. I do not believe Cx. quinquefasciatus host switching has been observed in Argentina, only in the northern hemisphere, so it is possible that the species could have an entirely different ecology in Argentina. It would have been helpful to conduct a blood meal analysis prior to this experiment to determine whether using an Argentinian population was appropriate to assess this question. If the Argentinian populations don't experience host switching, then an Argentinian colony would not be the appropriate colony to use to assess this question. Given that this experiment has already been conducted with this population, this possibility should at least be acknowledged in the discussion. Or if a study showing host switching in Argentina has been conducted, it would be helpful to highlight this in the introduction and discussion.

Thanks for this observation. We agree. However, we conducted the experiment beside host use data from Argentina since we used the mosquito species, and the centre region of Argentina (Córdoba) has a similar temperate weather regimen that those observed in the east coast of US.

We are aware that few studies regarding host shifting in South America are available, some such that those conducted by Stein et al. (2013) and Beranek (2019) reported a moderate host switch for Culex quinquefasciatus in Argentina. We have already performed a study about seasonal host feeding patterns for this species. However, even though there are few studies regarding host shifting, our hypothesis is based mainly in the seasonality of human cases of WNV and SLEV, a pattern that has been demonstrated for our region, see for example the study of Spinsanti et al. (2008).

We include a new paragraph in the Introduction and Discussion sections. Please see answers Reviewer #1.

(3) The impacts of certain experimental design decisions are not acknowledged in the manuscript and warrant discussion. For example, the larvae were reared under the same conditions to ensure adults of similar sizes and development timing, but this also prevents mechanisms of action that could occur as a result of seasonality experienced by mothers, eggs, and larvae.

We understand the confusion that may have arisen due to a lack of further details in the methodology. If we are not mistaken, you are referring to our oversight regarding the consideration of carry-over effects of larvae rearing that could potentially impact reproductive traits. When investigating the effects of temperature or other environmental factors on reproductive traits, it is possible to acclimate either larvae or adults. This is due to the significant phenotypic plasticity that mosquitoes exhibit throughout their entire ontogenetic cycle. In our study, we followed an approach similar to that of other authors where the adults are exposed to experimental conditions (temperature and photoperiod). For a similar approach you can refer to the studies conducted by Ferguson et al. (2018) for Cx. pipiens, Garcia Garcia & Londoño Benavides (2007) for Cx. quinquefasciatus or Christiansen-Jucht et al. (2014, 2015) for Anopheles gambiae.

(4) There are aspects of the data analysis that are not fully explained and should be further clarified. For example, there is no explanation of how the levels of categorical variables were compared.

The methodology and statistical analysis were expanded for a better understanding.

(5) The results show the opposite trend as was predicted by the authors based on observed feeding switches from birds to mammals in the autumn. However, they only state this once at the end of the discussion and never address why they might have observed the opposite trend as was hypothesized.

The discussion was restructured to focus on our results and our model.

(6) Generally speaking, the discussion has information that isn't directly related to the results and/or is too detailed in certain parts. Meanwhile, it doesn't dig into the meaning of the results or the ways in which the experimental design could have influenced results.

As mentioned above, the discussion was restructured to reflect our findings. We also included the effect that our design might have influenced our results. However, as stated above we do not fully agree that the design is inadequate for our analysis, we performed standard protocols followed by other researchers and studies in this research field.

(7) Beyond the issue of lack of replication limiting trust in the conclusions in general, there is one conclusion reached at the end of the discussion that would not be supported, even if additional replicates are conducted. The results do not show that physiological changes in mosquitoes trigger the selection of new hosts. Host selection is never measured, so this claim cannot be made. The results don't even suggest that fitness might trigger selection because the results show that physiological changes are in the opposite direction as what would be hypothesized to produce observed host switches. Similarly, the last sentence of the abstract is not supported by the results.

We agree with this observation. However, we did not evaluate the impact of fitness on host selection in this study. Instead, we aimed to investigate the potential influence of seasonality on mosquito fitness as a potential trigger for a shift in host selection. We agree that we have incorrectly used the term “host selection” when we should actually be discussing “host use change”. Our results indicate a seasonal alteration in mosquito fitness in response to temperature and photoperiod changes. Building upon this observation, we re-discussed our hypothesis and theoretical model to explain this seasonal shift in host use.

(8) Throughout the manuscript, there are grammatical errors that make it difficult to understand certain sentences, especially for the results.

All English grammar and writing of the manuscript was revised and corrected to be easily understood.

This study is driven by an interesting question and has the potential to be a valuable contribution to the literature.

Reviewer #2 (Recommendations for The Authors):

I hope that the authors will consider the suggested revisions and experimental replication to improve the quality of the study and paper.

This study tests a very interesting hypothesis. I understand that additional replicates are difficult to conduct, but I do believe that fitness studies absolutely require experimental replicates. Unless you are able to replicate the observed effects, I personally would not trust the results of this study. I hope that you will consider conducting replicates so that this important question can be answered in a more robust manner. Below, I expand upon some additional points in the public review and also provide more specific suggestions. I provided some copy-editing feedback, but was not able to point out all grammatical mistakes. I suggest that you use ChatGPT to help you edit the English. For example, you can feed ChatGPT your MS and ask it to bold the grammatical errors or you can ask it to edit grammatical errors and bold the sections that were edited. I understand that writing in a second language is very difficult (from personal experience!), so I view ChatGPT as a great tool to help even the playing field for publishing. Below are line item suggestions. Apologies that wording is curt, I was trying to be efficient in writing.

20-21: I suggest that you emphasize that you are investigating the interactive effect.

Accepted as suggested.

22: they weren't "reared" (from larvae) in different conditions, they were "maintained" as adults

Accepted as suggested.

26-27: increased/decreased is a bit misleading since you did not evaluate these groups sequentially in time. It might be more accurate to describe it as less than/greater than. Also, if you say increased/decreased or less than/greater than, you should always say what you are comparing to. The same applies throughout the MS.

Accepted as suggested.

29-30: "finding the" is not correct here; could be "with the lowest..."

Accepted as suggested.

34-36: I do not think that your results suggest this, even if you were to replicate the results of this experiment. You haven't shown metabolic changes.

We understand the point. Accepted as suggested.

42-44: "one of the main responsible" should be "one of the main species responsible..."

Accepted as suggested.

48: I think that "host preference" is better than selection here; -philic denotes preference

Accepted as suggested.

50: "Moreover" isn't the correct transition word here

Accepted as suggested.

57: "could" isn't correct here; consider saying "... species sometimes feed primarily on mammal hosts, including humans, in certain situations."

Accepted as suggested.

58: Different isn't correct word here

Accepted as suggested.

60: delete "feeding"

Accepted as suggested.

66-68: I am not familiar with any blood meal analysis studies in the southern hemisphere that show host switching for Culex species between summer and autumn. If this hasn't been shown, then this critique of the host migration hypothesis doesn't make sense.

There are some studies pointing this out (Stein et al., 2013, Beranek 2019), and unpublished data from us). However, our hypothesis has supported by epidemiological data observed in human population which indicate a seasonal activity pattern. It was explained in depth in the Introduction section.

68: ensures is not the right word; I suggest "suggests"

Accepted as suggested.

68-70: this explanation isn't clear to me; please revise

It will be revised. Accepted as suggested.

70: change cares to care

Accepted as suggested.

76-77: can you explain how they were not supported by the data for the benefit of those who are not familiar with these papers please?

Accepted as suggested.

87-89: I suggest the following wording: "In the autumn, we expect a greater number of eggs (fecundity) and larvae (fertility) in mosquitoes after feeding on a mammal host compared to an avian host, and the opposite relationship in the summer."

Accepted as suggested.

99: edit for grammar

Accepted as suggested.

102: suggest: "...offered a blood meal from a restrained chicken twice a month"

Accepted as suggested.

107: powder

Accepted as suggested.

108: inbred? Is this the term you meant to use?

Changed as suggested.

109: "several" cannot be used to describe 20 generations; suggest using "over twenty generations"; also, it would be good to acknowledge in your discussion that lab adaptation could force evolution, especially since mosquitoes are kept at constant temperatures and fed with certain hosts (with easy access) in the lab. Also, it would be good to know when the experiments were conducted to know the lapse of time between the creation of the colony and the experiments.

Accepted as suggested.

110-111: Does humidity vary between summer and fall in Córdoba? If so, I suggest acknowledging in the discussion that if humidity differences are involved in a potential interaction between host species and seasonality, then this would not have been captured by your experimental design.

Several variables change during seasons. We were interested in capturing the effects of temperature and photoperiod, since humidity is a variable difficult to control.

113-116: I suggest combining into one sentence to make more concise.

Accepted as suggested.

135: You might be obscuring the true impact of seasonality by rearing the larvae under the same conditions. There may be signals that mothers/eggs/larvae receive that influence their behavior (e.g. I believe this is the case for diapause), so this limitation should also be acknowledged. I understand why you decided to do this to control for development time and size, but it is something that should be considered in the discussion.

As it was explained above, Cx. quinquefasciatus do not suffer diapause in our country. Maintaining mosquitoes from adults was an approach selected by us based on other studies.

138: edit: "with cotton pads soaked in... on plastic..."; what is plastic glass? Do you mean plastic dishes?

Accepted as suggested.

141: here and throughout paragraph, full should be "fully"

Accepted as suggested.

144: located should be "placed"

Accepted as suggested.

147: suggest editing to "at which point, they were fixed with 1 mL of 96% ethanol and the number of L1 larvae per raft was counted."

Accepted as suggested.

154-155: edit for grammar

Accepted as suggested.

157: Your GLM explanation doesn't say anything about how you made pairwise comparisons between your levels; did you use emmeans?

This revised version includes a more detailed methodology and statistical analysis. Accepted as suggested.

158-160: I don't understand why you took this approach - it seems strange to me to use this analysis, but I am not familiar with it, so it might be that I lack the knowledge to be able to adequately evaluate. Please provide more explanation so that readers can better understand this analysis. A citation for this kind of application of the analysis would be helpful.

It was changed to be in accordance with the remaining analyses.

173: replace neither with either

Accepted as suggested.

174: this applies throughout; edit to : "An interaction effect was observed..."

Accepted as suggested.

175: "it was not found" is grammatically incorrect; instead : "We did not find ..." or "no differences in... were detected", etc

Accepted as suggested.

183: "it was detected" is grammatically incorrect

Accepted as suggested.

185-186: "being this treatment... in terms of fitness": I do not understand what this means. Please rephrase

Accepted as suggested.

170-199: you should provide the effect sizes and p values in text and/or in the figure for the pairwise comparisons

Accepted as suggested.

193-196. These two sentences are confusing and I am not sure what you mean, especially in the first sentence.

It was rewritten. Accepted as suggested.

Figure 1: This figure is great and easy to read and interpret! Thank you for the comment! 218-219: it is important to state which mosquito species you are referring to here.

Accepted as suggested.

226-227: you definitely should acknowledge the small sample size here.

Considered.

227: "it was observed" should be "We observed" or "A greater hatching rate.... was observed."

Accepted as suggested.

228-229: is the result really comparable even though you took very different approaches to the analysis for these outcomes?

Changed to be comparable.

230-278: the discussion of these hypotheses is too long and detailed, especially since the comparison of mouse vs chicken wasn't your main question; you really wanted to understand this in the context of seasonality. I suggest cutting this down a lot and making room to dig into your results more, and also to discuss the potential impacts of your experimental design/limitations on the results.

Discussion was changed to focus on our results and model. Accepted as suggested.

281: Hoffman is an old citation; I suggest you cite a modern review.

Accepted as suggested. We deleted it due to the re-writing of the manuscript.

282: "It can be recognise".. I am not sure what you are trying to say here

Accepted as suggested.

1. After the first time you write a species name, you can abbreviate the genus in all future mentions unless it is at the beginning of a sentence.

Accepted as suggested.

303-305: Revise this sentence. E.g "Fewer studies are available regarding photoperiod and show mixed results; Mogi (1992) found that mid and long day lengths induced greater fecundity while Costanzo et al. (2015) did not find differences in fecundity by day length."

Accepted as suggested.

315-316: typically, unpublished data shouldn't be referenced; I'm not sure if eLife has a policy on this.

We will check this with eLife guidelines. However, since the lack of evidence on this pattern we consider important to include this unpublished data.

316: Aegypti should be lowercase

Accepted as suggested.

328-330: This sentence is redundant with the first sentence of the paragraph

Accepted as suggested.

321-336: You never reintroduced your hypothesis in your discussion. I suggest that you center your whole discussion more directly around the hypothesis that motivated the study. If you decide not to restructure your discussion, you should at least reintroduce your hypothesis here and discuss how your results do not support the hypothesis.

Accepted as suggested.

337-348: This paragraph is a bit confusing as you jump between fertility and hatchability

Accepted as suggested.

353: is viral transmission the right word to use here? I think you might mean bridge vector transmission to humans specifically?

Accepted as suggested.

357: you say "neither" but never define which traits you are referring to

Accepted as suggested.

361: I suggest "two variables previously analyzed separately..."

Accepted as suggested.

General: There is no statement about the availability of data; it is eLife policy to require all data to be publicly available. Also, it would be helpful to share your code to help understand how you conducted pairwise comparisons, etc.

In the submission it was not mentioned anything about data availability. However, all data and scripts will be uploaded with the VOR if it is required.

Recommendations for the authors:

I found your study interesting and potentially promising. However, there are some fundamental problems with the study design and the hypothesis, including:

<(1) Seasonality simulation - Seasonality is strongly associated with time, so it is unusual to simulate seasonal factors without accounting for time. The actual factors associated with seasonal change in reproductive output may be neither a difference in host blood meal nor temperature and photoperiod. It is therefore, odd to reduce seasonality to a difference in photoperiod and temperature in summer and autumn without even mentioning the time of year when the experiment was carried (except for the mention of February as the time the stock samples were collected from the wild).

The temperature and photoperiod settings are established according to a representative day in both autumn and summer. To determine these settings, we utilized climate data spanning a 3-year period (2020-2022), encompassing the most frequently occurring temperatures and day lengths. The weather conditions remained notably consistent throughout this time frame, which is why the specific year was not mentioned. Moreover, including the year in laboratory experiment details is uncommon, as evident in various papers. This practice can be corroborated by referring to multiple sources (cited in the original manuscript). We mention this in the new version.

(2) Hypothesis - While the hypothesis alludes to the 'reason' for seasonal host shift, the prediction is on the outcome of the interaction between blood meal type and season.

It might be nicer to frame your hypothesis to be consistent with the aim, which is, testing the partial contributions of blood meal type, versus photoperiod and temperature to seasonal change in the reproductive output of Culex quinquefasciatus. A hypothesis like that can be accompanied by alternative predictions according to the expected individual and interactive effects of both factors.

It was rewritten in the revised version to be consistent with our predictions and findings.

Blood meal type, temperature, and photoperiod are all components of seasonality, so the strength of the study is its potential to decouple the effect of blood meal type from that of temperature and photoperiod on the seasonal reproductive output of Culex quinquefasciatus by comparing the two blood meal types under simulated summer and winter conditions. Ideally, this should have been over a natural summer and winter because a natural time difference captures the effect of other seasonal factors other than temperature and photoperiod.

Furthermore, the hypothesis stemmed from field observations, while the study itself was conducted under laboratory conditions using a local population of Culex quinquefasciatus from Argentina. It remains uncertain whether there is supporting evidence for a seasonal shift in host usage in Culex quinquefasciatus from the stock population. Discussing the field observations within the stock population would provide valuable insights.

It was considered in the new version.

Author Response

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

eLife assessment

This important study enhances our understanding of the effects of landscape context on grassland plant diversity and biomass. Notably, the authors use a well-designed field sampling method to separate the effects of habitat loss and fragmentation per se. Most of the data and analyses provide solid support for the findings that habitat loss weakens the positive relationship between grassland plant richness and biomass.

Response: Thanks very much for organizing the review of the manuscript. We are grateful to you for the recognition. We have carefully analyzed all comments of the editors and reviewers and revised our manuscript to address them. All comments and recommendations are helpfully and constructive for improving our manuscript. We have described in detail our response to each of comment below.

In addition to the reviewers' assessments, we have the following comments on your paper.

(1) Some of the results are not consistent between figures. The relationships between overall species richness and fragmentation per se are not consistent between Figs. 3 and 5. The relationships between aboveground biomass and habitat loss are not consistent between Figs. 4 and 5. How shall we interpret these inconsistent results?

Response: Thanks for your insightful comments. The reason for these inconsistencies is that the linear regression model did not take into account the complex causal relationships (including direct and indirect effects) among the different influencing factors. The results in Figures 3 and 4 just represent the pairwise relationship pattern and relative importance, respectively. The causal effects of habitat loss and fragmentation per se on plant richness and above-ground biomass should be interpreted based on the structural equation model results (Figure 6). We have revised the data analysis to clear these inconsistent results. Line 225-228

In the revised manuscript, we have added the interpretation for these inconsistent results. The inconsistent effects between Figures 3 and 6 suggest that fragmentation per se actually had a positive effect on plant richness after accounting for the effects of habitat loss and environmental factors simultaneously.

The inconsistent effects between Figures 4 and 6 are because the effects of habitat loss and fragmentation per se on above-ground biomass were mainly mediated by plant richness and environmental factors, which had no significant direct effect (Figure 6). Thus, habitat loss and fragmentation per se showed no significant relative effects on above-ground biomass after controlling the effects of plant richness and environmental factors (Figure 4).

(2) One of the fragmentation indices, mean patch area metric, seems to be more appropriate as a measure of habitat loss, because it represents "a decrease in grassland patch area in the landscape".

Response: Thanks for your insightful comments. We apologize for causing this confusion. The mean patch area metric in our study represents the mean size of grassland patches in the landscape for a given grassland amount. Previous studies have often used the mean patch metric as a measure of fragmentation, which can reflect the processes of local extinction in the landscape (Fahrig, 2003; Fletcher et al., 2018). We have revised the definition of the mean patch area metric and added its ecological implication in the revised manuscript to clarify this confusion.

(3) It is important to show both the mean and 95% CI (or standard error) of the slope coefficients regarding to Figs. 3 and 6.

Response: Thanks for your suggestions. We have added the 95% confidence intervals to the Figure 3 and Figure 6 in the revised manuscript.

(4) It would be great to clarify what patch-level and landscape-level studies are in lines 302-306. Note that this study assesses the effects of landscape context on patch-level variables (i.e., plot-based plant richness and plot-based grassland biomass) rather than landscape-level variables (i.e., the average or total amount of biomass in a landscape).

Response: Thanks for your insightful comment. We agree with your point that our study investigated the effect of fragmented landscape context (habitat loss and fragmentation per se) on plot-based plant richness and plot-based above-ground biomass rather than landscape-level variables.

Therefore, we no longer discussed the differences between the patch-level and landscape-level studies here, instead focusing on the different ecological impacts of habitat loss and fragmentation per se in the revised manuscript.

Line 369-374:

“Although habitat loss and fragmentation per se are generally highly associated in natural landscapes, they are distinct ecological processes that determine decisions on effective conservation strategies (Fahrig, 2017; Valente et al., 2023). Our study evaluated the effects of habitat loss and fragmentation per se on grassland plant diversity and above-ground productivity in the context of fragmented landscapes in the agro-pastoral ecotone of northern China, with our results showing the effects of these two facets to not be consistent.”

(5) One possible way to avoid the confusion between "habitat fragmentation" and "fragmentation per se" could be to say "habitat loss and fragmentation per se" when you intend to express "habitat fragmentation".

Response: Thanks for your constructive suggestions. To avoid this confusion, we no longer mention habitat fragmentation in the revised manuscript but instead express it as habitat loss and fragmentation per se.

Reviewer #1 (Public Review):

This is a well-designed study that explores the BEF relationships in fragmented landscapes. Although there are massive studies on BEF relationships, most of them were conducted at local scales, few considered the impacts of landscape variables. This study used a large dataset to specifically address this question and found that habitat loss weakened the BEF relationships. Overall, this manuscript is clearly written and has important implications for BEF studies as well as for ecosystem restoration.

Response: We are grateful to you for the recognition and constructive comments. All the comments and suggestions are very constructive for improving this manuscript. We have carefully revised the manuscript following your suggestions. All changes are marked in red font in the revised manuscript.

My only concern is that the authors should clearly define habitat loss and fragmentation. Habitat loss and fragmentation are often associated, but they are different terms. The authors consider habitat loss a component of habitat fragmentation, which is not reasonable. Please see my specific comments below.

Response: We agree with your point. In the revised manuscript, we no longer consider habitat loss and fragmentation per se as two facets of habitat fragmentation. We have clearly defined habitat loss and fragmentation per se and explicitly evaluated their relative effects on plant richness, above-ground biomass, and the BEF relationship.

Reviewer #1 (Recommendations For The Authors):

Title: It is more proper to say habitat loss, rather than habitat fragmentation.

Response: Thanks for your suggestion. We have revised the title to “Habitat loss weakens the positive relationship between grassland plant richness and above-ground biomass”

Line 22, remove "Anthropogenic", this paper is not specifically discussing habitat fragmentation driven by humans.

Response: Thanks for your suggestion. We have removed the “Anthropogenic” from this sentence.

Line 26, revise to "we investigated the effects of habitat loss and fragmentation per se on plant richness... in grassland communities by using a structural equation model".

Response: Thanks for your suggestion. We have revised this sentence.

Line 25-28:

“Based on 130 landscapes identified by a stratified random sampling in the agro-pastoral ecotone of northern China, we investigated the effects of landscape context (habitat loss and fragmentation per se) on plant richness, above-ground biomass, and the relationship between them in grassland communities using a structural equation model.”

Line 58-60, habitat fragmentation generally involves habitat loss, but habitat loss is independent of habitat fragmentation, it is not a facet of habitat fragmentation.

Response: Thanks for your insightful comment. We have no longer considered habitat loss and fragmentation per se as two facets of habitat fragmentation. In the revised manuscript, we consider habitat loss and fragmentation as two different processes in fragmented landscapes.

Line 65-67, this sentence is not very relevant to this paragraph and can be deleted.

Response: Thanks for your suggestion. We have deleted this sentence from the paragraph.

Line 87-90, these references are mainly based on microorganisms, are there any references based on plants? These references are more relevant to this study. In addition, this is a key mechanism mentioned in this study, this section needs to be strengthened with more evidence and further exploration.

Response: Thanks for your comment and suggestion. Thanks for your comment and suggestion. We have added some references based on plants here to strengthen the evidence and mechanism of habitat specialisation determines the BEF relationship.

Line 89-95:

“In communities, specialists with specialised niches in resource use may contribute complementary roles to ecosystem functioning, whereas generalists with unspecialised in resource use may contribute redundant roles to ecosystem functioning due to overlapping niches (Dehling et al., 2021; Denelle et al., 2020; Gravel et al., 2011; Wilsey et al., 2023). Therefore, communities composed of specialists should have a higher niche complementarity effect in maintaining ecosystem functions and a more significant BEF relationship than communities composed of generalists.”

Denelle, P., Violle, C., DivGrass, C., Munoz, F. 2020. Generalist plants are more competitive and more functionally similar to each other than specialist plants: insights from network analyses. Journal of Biogeography 47: 1922-1933.

Dehling, D.M., Bender, I.M.A., Blendinger, P.G., Böhning-Gaese, K., Muñoz, M.C., Neuschulz, E.L., Quitián, M., Saavedra, F., Santillán, V., Schleuning, M., Stouffer, D.B. 2021. Specialists and generalists fulfil important and complementary functional roles in ecological processes. Functional Ecology 35: 1810-1821.

Wilsey, B., Martin, L., Xu, X., Isbell, F., Polley, H.W. 2023. Biodiversity: Net primary productivity relationships are eliminated by invasive species dominance. Ecology Letters.

Line 129-130, Although you can use habitat loss in the discussion or the introduction, here preferably use habitat amount or habitat area, rather than habitat loss in this case. Habitat loss represents changes in habitat area, but the remaining grasslands could be the case of natural succession or other processes, rather than loss of natural habitat.

Response: Thanks for your insightful comment. We agree with your point. In the revised manuscript, we have explicitly stated that habitat loss was represented by the loss of grassland amount in the landscape.

Since the remaining grassland fragments in this region were mainly caused by grassland loss due to human activities such as cropland expansion (Chen et al., 2019; Yang et al., 2020), we used the percentage of non-grassland cover in the landscape to represent habitat loss in our study.

Line 132-135:

“Habitat loss was represented by the loss of grassland amount in the landscape. As the remaining grassland fragments in this region were mainly caused by grassland loss due to human activities such as cropland expansion (Chen et al., 2019; Yang et al., 2020), the percentage of non-grassland cover in the landscape was used in our study to represent habitat loss.”

Lines 245-246, please also give more details of the statistical results, such as n, r value et al in the text.

Response: Thanks for your suggestion. We have added the details of the statistical results in the revised manuscript.

Line 283-290:

“Habitat loss was significantly negatively correlated with overall species richness (R = -0.21, p < 0.05, Figure 3a) and grassland specialist richness (R = -0.41, p < 0.01, Figure 3a), but positively correlated with weed richness (R = 0.31, p < 0.01, Figure 3a). Fragmentation per se was not significantly correlated with overall species richness and grassland specialist richness, but was significantly positively correlated with weed richness (R = 0.26, p < 0.01, Figure 3b). Habitat loss (R = -0.39, p < 0.01, Figure 3c) and fragmentation per se (R = -0.26, p < 0.01, Figure 3d) were both significantly negatively correlated with above-ground biomass.”

Fig. 5, is there any relationship between habitat amount and fragmentation per se in this study?

Response: Thanks for your insightful comment. We have considered a causal relationship between habitat loss and fragmentation per se in the structural equation model. We have discussed this relationship in the revised manuscript.

Line 290-293, how about the BEF relationships with different fragmentation levels? I may have missed something somewhere, but it was not shown here.

Response: Thanks for your insightful comment. We have added the BEF relationships with different fragmentation per se levels here.

Line 323-340:

“The linear regression models showed that habitat loss had a significant positive modulating effect on the positive relationship between plant richness and above-ground biomass, and fragmentation per se had no significant modulating effect (Figure 5). The positive relationship between plant richness and above-ground biomass weakened with increasing levels of habitat loss, strengthened and then weakened with increasing levels of fragmentation per se.

Author response image 1.

Relationships between grassland plant richness and above-ground biomass at different levels of habitat loss and fragmentation per se from 130 landscapes in the Tabu River Basin, a typical agro-pastoral ecotone of northern China: (a) high habitat loss and low fragmentation per se, (b) high habitat loss and moderate fragmentation per se, (c) high habitat loss and high fragmentation per se, (d) moderate habitat loss and low fragmentation per se, (e) moderate habitat loss and moderate fragmentation per se, (f) moderate habitat loss and high fragmentation per se, (g) low habitat loss and low fragmentation per se, (h) low habitat loss and moderate fragmentation per se. The R2 values in each panel are from linear regression models. The n in each panel is the number of surveying sites used in the linear regression models. The blue solid and dashed trend lines represent the significant and not significant effects, respectively. The shaded area around the trend line represents the 95% confidence interval. * represent significance at the 0.05 level. ** represent significance at the 0.01 level.”

Discussion

The Discussion (Section 4.2) needs to be revised and focused on your key findings, it is habitat loss, not fragmentation per se, that weakens the BEF relationships.

Response: Thanks for your insightful comment and suggestion. In the revised manuscript, we have rephrased the Discussion (Section 4.2) to mainly discuss the inconsistent effects of habitat loss and fragmentation per se on the BEF relationship.

Line 414-416:

“4.2 Habitat loss rather than fragmentation per se weakened the magnitude of the positive relationship between plant diversity and ecosystem function”

The R2 in the results are low (e.g., Fig. 3), please also mention other variables that might influence the observed pattern in the Discussion, such as soil and topography, though I understand it is difficult to collect such data in this study.

Response: Thanks for your insightful comment and suggestion. We agree with you and reviewer 3 that the impact of environmental factors should also be considered.

Therefore, we have considered two environmental factors related to water and temperature (soil water content and land surface temperature) in the analysis and discussed their impacts on plant diversity and above-ground biomass in the revised manuscript.

Lines 344-345, its relative importance was stronger in the intact landscape than that of the fragmented landscape?

Response: We apologize for making this confusion. We have rephrased this sentence.

Line 422-426:

“Our study found grassland plant diversity showed a stronger positive impact on above-ground productivity than landscape context and environmental factors. This result is consistent with findings by Duffy et al. (2017) in natural ecosystems, indicating grassland plant diversity has an important role in maintaining grassland ecosystem functions in the fragmented landscapes of the agro-pastoral ecotone of northern China.”

Reviewer #2 (Public Review):

Summary:

In this manuscript, Yan et al. assess the effect of two facets of habitat fragmentation (i.e., habitat loss and habitat fragmentation per se) on biodiversity, ecosystem function, and the biodiversity-ecosystem function (BEF) relationship in grasslands of an agro-pastoral ecotone landscape in northern China. The authors use stratified random sampling to select 130 study sites located within 500m-radius landscapes varying along gradients of habitat loss and habitat fragmentation per se. In these study sites, the authors measure grassland specialist and generalist plant richness via field surveys, as well as above-ground biomass by harvesting and dry-weighting the grass communities in each 3 x 1m2 plots of the 130 study sites. The authors find that habitat loss and fragmentation per se have different effects on biodiversity, ecosystem function and the BEF relationship: whereas habitat loss was associated with a decrease in plant richness, fragmentation per se was not; and whereas fragmentation per se was associated with a decrease in above-ground biomass, habitat loss was not. Finally, habitat loss, but not fragmentation per se was linked to a decrease in the magnitude of the positive biodiversity-ecosystem functioning relationship, by reducing the percentage of grassland specialists in the community.

Strengths:

This study by Yan et al. is an exceptionally well-designed, well-written, clear and concise study shedding light on a longstanding, important question in landscape ecology and biodiversity-ecosystem functioning research. Via a stratified random sampling approach (cf. also "quasi-experimental design" Butsic et al. 2017), Yan et al. create an ideal set of study sites, where habitat loss and habitat fragmentation per se (usually highly correlated) are decorrelated and hence, separate effects of each of these facets on biodiversity and ecosystem function can be assessed statistically in "real-world" (and not experimental, cf. Duffy et al. 2017) communities. The authors use adequate and well-described methods to investigate their questions. The findings of this study add important empirical evidence from real-world grassland ecosystems that help to advance our theoretical understanding of landscape-moderation of biodiversity effects and provide important guidelines for conservation management.

Weaknesses:

I found only a few minor issues, mostly unclear descriptions in the study that could be revised for more clarity.

Response: Thanks very much for your review of the manuscript. We are grateful to you for the recognition. All the comments and suggestions are very insightful and constructive for improving this manuscript. We have carefully studied the literature you recommend and revised the manuscript carefully following your suggestions. All changes are marked in red font in the revised manuscript.

Reviewer #2 (Recommendations For The Authors):

Specific comments

(1) Some aspects of the Methods section were not entirely clear to me, could you revise them for more clarity?

(a) Whereas you describe 4 main facets of fragmentation per se that are used to create the PC1 as a measure of overall fragmentation per se, it looks as if this PC1 is mainly driven by 3 facets only (ED, PD and AREA_MN), and patch isolation (nearest neighbour distance, ENN) having a relatively low loading on PC1 (Figure A1). I think it would be good to discuss this fact and the consequences of it, that your definition of fragmentation is focused more on edge density, patch density and mean patch area, and less on patch isolation in your Discussion section?

Response: Thanks for your insightful comment and suggestion. We agree with your point. We have discussed this fact and its implications for understanding the effects of fragmentation per se in our study.

Line 384-389:

“However, it is important to stress that the observed positive effect of fragmentation per se does not imply that increasing the isolation of grassland patches would promote biodiversity, as the metric of fragmentation per se used in our study was more related to patch density, edge density and mean patch area while relatively less related to patch isolation (Appendix Table A1). The potential threats from isolation still need to be carefully considered in the conservation of biodiversity in fragmented landscapes (Haddad et al., 2015).”

(b) Also, from your PCA in Figure A1, it seems that positive values of PC1 mean "low fragmentation", whereas high values of PC1 mean "high fragmentation", however, in Figure A2, the inverse is shown (low values of PC1 = low fragmentation, high values of PC1 = high fragmentation). Could you clarify in the Methods section, if you scaled or normalized the PC1 to match this directionality?

Response: We apologize for making this confusion. In order to be consistent with the direction of change in fragmentation per se, we took the inverse of the PC1 as a single fragmentation per se index, which was positively correlated with patch density, edge density, mean nearest-neighbor distance metric, and negatively with mean patch area (Appendix Figure A1 and Table A1). We have clarified this point in the Method section.

Line 160-163:

“We took the inverse of the PC1 as a single fragmentation per se index, which was positively correlated with patch density, edge density, mean nearest-neighbor distance metric, and negatively with mean patch area (Appendix Figure A1 and Table A1).”

(c) On line 155 you describe that you selected at least 20 landscapes using stratified sampling from each of the eight groups of habitat amount and fragmentation combination. Could you clarify: 1) did you randomly sample within these groups with a minimum distance condition or was it a non-random selection according to other criteria? (I think you could move the "To prevent overlapping landscapes..." sentence up here to the description of the landscape selection process) 2) Why did you write "at least 20 landscapes" - were there in some cases more or less landscapes selected? 130 study landscapes divided by 8 groups only gives you 16.25, hence, at least for some groups there were less than 20 landscapes? Could you describe your final dataset in more detail, i.e. the number of landscapes per group and potential repercussions for your analysis?

Response: Thanks for your insightful comments. In the revised manuscript, we have rephrased the method to provide more detail for the sampling landscape selection.

(1) Line 169-172

We randomly selected at least 20 grassland landscapes with a minimum distance condition using stratified sampling from each of the remaining eight grassland types as alternative sites for field surveys. The minimum distance between each landscape was at least 1000 m to prevent overlapping landscapes and potential spatial autocorrelation.

(2) Line 184-191

The reason for selecting at least 20 grassland landscapes of each type in this study was to ensure enough alternative sites for the field survey. This is because the habitat type of some selected sites was not the natural grasslands, such as abandoned agricultural land. Some of the selected sites may not be permitted for field surveys.

Thus, we finally established 130 sites in the field survey. The types of the 130 sites were: 19 high-moderate, 14 high-low, 19 moderate-high, 16 moderate-moderate, 18 moderate-low, 16 low-high, 17 low-moderate, 11 low-low habitat amount and fragmentation per se.

(d) On line 166, you describe that you established 130 sites of 30 m by 30 m - I assume they were located (more or less) exactly in the centre of the selected 500 m - radius landscapes? Were they established so that they were fully covered with grassland? And more importantly, how did you establish the 10 m by 10 m areas and the 1 m2 plots within the 30 m by 30 m sites? Did you divide the 30 m by 30 m areas into three rectangles of 10 m by 10 m and then randomly established 1 m2 plots? Were the 1 m2 plots always fully covered with grassland/was there a minimum distance to edge criterion? Please describe with more detail how you established the 1 m2 study sites, and how many there were per landscape.

Response: Thanks for your insightful comments. In the revised manuscript, we have provided more detailed information on how to set up 130 sites of 30 m by 30 m and three plots of 1 m by 1 m.

(1) As these 130 sites were selected based on the calculation of the moving window, they were located (more or less) exactly in the centre of the 500-m radius buffer.

(2) These sites were fully covered with grassland because their size (30 m by 30 m) was the same as the size of the grassland cell (30 m by 30 m) used in the calculation of the moving window.

(3) We randomly set up three 1 m * 1 m plots in a flat topographic area at the 10 m * 10 m centre of each site. Thus, there was a minimum distance of 10 m to the edge for each 1 m * 1 m plot.

(4) There are three 1 m * 1 m plots per landscape.

Line 182-191:

“Based on the alternative sites selected above, we established 130 sites (30 m * 30 m) between late July to mid-August 2020 in the Tabu River Basin in Siziwang Banner, Inner Mongolia Autonomous Region (Figure 1). The types of the 130 sites were: 19 high-moderate, 14 high-low, 19 moderate-high, 16 moderate-moderate, 18 moderate-low, 16 low-high, 17 low-moderate, 11 low-low habitat amount and fragmentation per se. In order to exclude the impact of historical agricultural activities, the habitat type of the established sites was natural grasslands with regional vegetation characteristics. Each site was not abandoned agricultural land, and there was no sign of agricultural reclamation.

At the 10 m * 10 m center of each site, we randomly set up three 1 m * 1 m plots in a flat topographic area to investigate grassland vascular plant diversity and above-ground productivity.”

(e) Line 171: could you explain what you mean by reclaimed?

Response: Thanks for your comment. The “reclaimed” means that historical agricultural activities. We have rephrased this sentence to make it more explicit.

Line 186-189:

“In order to exclude the impact of historical agricultural activities, the habitat type of the established sites was natural grasslands with regional vegetation characteristics. Each site was not abandoned agricultural land, and there was no sign of agricultural reclamation.”

(f) Line 188 ff.: Hence your measure of productivity is average-above ground biomass per 1 m2. I think it would add clarity if you highlighted this more explicitly.

Response: Thanks for your suggestion. We have highlighted that the productivity in our study was the average above-ground biomass per 1 m * 1 m plots in each site.

Line 215-217:

“For each site, we calculated the mean vascular plant richness of the three 1 m * 1 m plots, representing the vascular plant diversity, and mean above-ground biomass of the three 1 m * 1 m plots, representing the above-ground productivity.”

(2) All figures are clear and well-designed!

(a) Just as a suggestion: in Figures 3 and 6, you could maybe add the standard errors of the mean as well?

Response: Thanks for your suggestion. In the revised manuscript, we have added the standard errors of the mean in Figures 3 and 6.

(b) Figure 4: Could you please clarify: Which models were the optimal models on which these model-averaged standardized parameter estimates were based on? And hence, the optimal models contained all 4 predictors (otherwise, no standardized parameter estimate could be calculated)? Or do these model-averaged parameters take into account all possible models (and not only the optimal ones)?

Response: Thanks for your suggestion. We selected the four optimal models based on the AICc value to calculate the model-averaged standardized parameter estimates. The four optimal models contained all predictors in Figure 4. We have added the four optimal models in Appendix Table A3.

Appendix:

Author response table 1.

Four optimal models of landscape context, environment factors, and plant diversity affecting above-ground biomass.

Note: AGB: above-ground biomass; HL: habitat loss; FPS: fragmentation per se; SWT: soil water content; LST: land surface temperature; GSR: grassland specialist richness; WR: weed richness; **: significance at the 0.01 level.”

(c) Please add in all Figures (i.e., Figures 4, 5 and 6, Figure 6 per "high, moderate and low-class") the number of study units the analyses were based on.

Response: Thanks for your suggestion. In the revised manuscript, we have added the number of study units the analyses were based on in all Figures.

(d) Figure 6: I think it would be more consistent to add a second plot where the BEF-relationship is shown for low, moderate and high levels of habitat fragmentation per se. Could you also add a clearer description in the Methods and/or Results section of how you assessed if habitat amount or fragmentation per se affected the BEF-relationship? I.e. based on the significance of the interaction term (habitat amount x species richness) in a linear model?

Response: Thanks for your insightful comment and suggestion. We have added a second plot in Figure 5 to show the BEF relationship at low, moderate and high levels of fragmentation per se.

Line 328-340:

Author response image 2.

Relationships between grassland plant richness and above-ground biomass at different levels of habitat loss and fragmentation per se from 130 landscapes in the Tabu River Basin, a typical agro-pastoral ecotone of northern China: (a) high habitat loss and low fragmentation per se, (b) high habitat loss and moderate fragmentation per se, (c) high habitat loss and high fragmentation per se, (d) moderate habitat loss and low fragmentation per se, (e) moderate habitat loss and moderate fragmentation per se, (f) moderate habitat loss and high fragmentation per se, (g) low habitat loss and low fragmentation per se, (h) low habitat loss and moderate fragmentation per se. The R2 values in each panel are from linear regression models. The n in each panel is the number of surveying sites used in the linear regression models. The blue solid and dashed trend lines represent the significant and not significant effects, respectively. The shaded area around the trend line represents the 95% confidence interval. * represent significance at the 0.05 level. ** represent significance at the 0.01 level.”

We determined whether habitat loss and fragmentation per se moderated the BEF relationship by testing the significance of their interaction term with plant richness. We have added a clearer description in the Methods section of the revised manuscript.

Line 245-250:

“We then assessed the significance of interaction terms between habitat loss and fragmentation per se and plant richness in the linear regression models to evaluate whether they modulate the relationship between plant richness and above-ground biomass. Further, we used a piecewise structural equation model to investigate the specific pathways in which habitat loss and fragmentation per se modulate the relationship between plant richness and above-ground biomass.”

(3) While reading your manuscript, I missed a discussion on the potential non-linear effects of habitat amount and fragmentation per se. In your study, it seems that the effects of habitat amount and fragmentation per se on biodiversity and ecosystem function are quite linear, which contrasts previous research highlighting that intermediate levels of fragmentation/heterogeneity could maximise spatial asynchrony, biodiversity and ecosystem function (e.g. Redon et al. 2014, Thompson & Gonzalez 2016, Tscharntke et al. 2012, Wilcox et al. 2017). I think it would add depth to your study if you discussed your finding of linear effects of habitat amount and fragmentation on biodiversity, ecosystem functioning and BEF. For example:

Response: Thanks for your constructive suggestions. We have carefully studied the literature (e.g. Redon et al. 2014, Thompson & Gonzalez 2016, Tscharntke et al. 2012, Wilcox et al. 2017), which highlights that intermediate levels of fragmentation/heterogeneity could maximise spatial asynchrony, biodiversity and ecosystem function.

In the revised manuscript, we have added the discussion about the linear positive effects of fragmentation on plant diversity and above-ground productivity and discussed possible reasons for this linear effect.

Line 402-413:

“In our study, a possible mechanism for the positive impacts of fragmentation per se on plant diversity and above-ground productivity (indirect positive impact via plant diversity) is that fragmentation per se increases the habitat heterogeneity in the landscape, which can promote biodiversity through spatial asynchrony and spatial insurance effects (Tscharntke et al., 2012). Previous studies indicated that heterogeneity typically has nonlinear effects on biodiversity and ecosystem function, as moderate heterogeneity can maximise spatial asynchrony (Redon et al., 2014; Wilcox et al., 2017). However, our study did not observe nonlinear patterns between fragmentation per se and plant diversity and above-ground productivity. This may be due to the low spatial heterogeneity of this area as a result of agricultural intensification (Benton et al., 2003; Chen et al., 2019). The gradient of fragmentation per se in our study may not cover the optimal heterogeneity levels for maximising plant diversity and above-ground productivity (Thompson and Gonzalez, 2016).”

Meanwhile, we also discussed the nonlinear pattern of the BEF relationship with increasing levels of fragmentation per se to add depth to the discussion.

Line 442-451:

“In addition, our study found that the BEF relationship showed a nonlinear pattern with increasing levels of fragmentation per se. For a given level of habitat loss, the positive BEF relationship was strongest at moderate fragmentation per se level and became neutral at high fragmentation per se level. This can be explained by the increased spatial asynchrony at moderate fragmentation per se level, which can promote niche complementary among species in the community and thus strengthen the BEF relationship (Gonzalez et al., 2020; Thompson and Gonzalez, 2016; Tscharntke et al., 2012). The neutral BEF relationship at high fragmentation per se level may be due to edge effects enhancing environmental filtering, thereby leading to functional redundancy among species and decoupling the BEF relationship (Fetzer et al., 2015; Hu et al., 2016; Zambrano et al., 2019).”

(a) Line 74-75: I was wondering if you also thought of spatial insurance effects or spatial asynchrony effects that can emerge with habitat fragmentation, which could lead to increased ecosystem functioning as well? (refs. above).

Response: Thanks for your constructive suggestions. In the revised manuscript, we have explicitly considered the spatial insurance effect or spatial asynchrony as the important mechanism for fragmentation per se to increase plant diversity, ecosystem function, and the BEF relationship.

Line 74-77:

“In theory, habitat loss and fragmentation per se can regulate ecosystem function and the BEF relationship by altering species composition, interactions, and spatial asynchrony regardless of changes in species richness (Liu et al., 2018; Thompson and Gonzalez, 2016; Tscharntke et al., 2012).”

Line 402-408:

“In our study, a possible mechanism for the positive impacts of fragmentation per se on plant diversity and above-ground productivity (indirect positive impact via plant diversity) is that fragmentation per se increases the habitat heterogeneity in the landscape, which can promote biodiversity through spatial asynchrony and spatial insurance effects (Tscharntke et al., 2012). Previous studies indicated that heterogeneity typically has nonlinear effects on biodiversity and ecosystem function, as moderate heterogeneity can maximise spatial asynchrony (Redon et al., 2014; Wilcox et al., 2017).”

Line 442-451:

“In addition, our study found that the BEF relationship showed a nonlinear pattern with increasing levels of fragmentation per se. For a given level of habitat loss, the positive BEF relationship was strongest at moderate fragmentation per se level and became neutral at high fragmentation per se level. This can be explained by the increased spatial asynchrony at moderate fragmentation per se level, which can promote niche complementary among species in the community and thus strengthen the BEF relationship (Gonzalez et al., 2020; Thompson and Gonzalez, 2016; Tscharntke et al., 2012). The neutral BEF relationship at high fragmentation per se level may be due to edge effects enhancing environmental filtering, thereby leading to functional redundancy among species and decoupling the BEF relationship (Fetzer et al., 2015; Hu et al., 2016; Zambrano et al., 2019).”

(b) I was wondering, if this result of linear effects could also be the result of a fragmentation gradient that does not cover the whole range of potential values? Maybe it would be good to compare the gradient in habitat fragmentation in your study with a theoretical minimum maximum/considering that there might be an optimal medium degree of fragmentation.

Response: Thanks for your insightful comment. We agree with your point that the linear effect of fragmentation per se in our study may be due to the fact that the gradient of fragmentation per se in this region may not cover the optimal heterogeneity levels for maximising spatial asynchrony. This is mainly because the agricultural intensification in the agro-pastoral ecotone of northern China could lead to lower spatial heterogeneity in this region. We have explicitly discussed this point in the revised manuscript.

Line 406-413:

“Previous studies indicated that heterogeneity typically has nonlinear effects on biodiversity and ecosystem function, as moderate heterogeneity can maximise spatial asynchrony (Redon et al., 2014; Wilcox et al., 2017). However, our study did not observe nonlinear patterns between fragmentation per se and plant diversity and above-ground productivity. This may be due to the low spatial heterogeneity of this area as a result of agricultural intensification (Benton et al., 2003; Chen et al., 2019). The gradient of fragmentation per se in our study may not cover the optimal heterogeneity levels for maximising plant diversity and above-ground productivity (Thompson and Gonzalez, 2016).”

(4) Some additional suggestions:

(a) Line 3: Maybe add "via reducing the percentage of grassland specialists in the community"?

Response: Thanks for your suggestion. We have revised this sentence.

Line 19:

“Habitat loss can weaken the positive BEF relationship via reducing the percentage of grassland specialists in the community”

(b) Lines 46-48: Maybe add "but see: Duffy, J.E., Godwin, C.M. & Cardinale, B.J. (2017). Biodiversity effects in the wild are common and as strong as key drivers of productivity. Nature."

Response: Thanks for your suggestion. We have added this reference here.

Line 47-49:

“When research expands from experiments to natural systems, however, BEF relationships remain unclear in the natural assembled communities, with significant context dependency (Hagan et al., 2021; van der Plas, 2019; but see Duffy et al., 2017).”

(c) Lines 82-87 and lines 90-93: Hence, your study actually is in contrast to these findings, i.e., fragmented landscapes do not necessarily have a lower fraction of grassland specialists? If yes, could you highlight this more explicitly?

Response: Thanks for your insightful comment. We have explicitly highlighted this point in the revised manuscript.

Line 434-439:

“Meanwhile, our study demonstrates that habitat loss, rather than fragmentation per se, can decrease the degree of habitat specialisation by leading to the replacement of specialists by generalists in the community, thus weakening the BEF relationship. This is mainly because fragmentation per se did not decrease the grassland specialist richness in this region, whereas habitat loss decreased the grassland specialist richness and led to the invasion of more weeds from the surrounding farmland into the grassland community (Yan et al., 2022; Yan et al., 2023).”

(d) Line 360: Could you add some examples of these multiple ecosystem functions you refer to?

Response: Thanks for your suggestion. We have added some examples of these multiple ecosystem functions here.

Line 456-457:

“Therefore, future studies are needed to focus on multiple ecosystem functions, such as below-ground productivity, litter decomposition, soil carbon stocks, etc.”

Reviewer #3 (Public Review):

Summary:

The authors aim to solve how landscape context impacts the community BEF relationship. They found habitat loss and fragmentation per se have inconsistent effects on biodiversity and ecosystem function. Habitat loss rather than fragmentation per se can weaken the positive BEF relationship by decreasing the degree of habitat specialization of the community.

Strengths:

The authors provide a good background, and they have a good grasp of habitat fragmentation and BEF literature. A major strength of this study is separating the impacts of habitat loss and fragmentation per se using the convincing design selection of landscapes with different combinations of habitat amount and fragmentation per se. Another strength is considering the role of specialists and generalists in shaping the BEF relationship.

Response: We are grateful to you for the recognition and constructive comments. All the comments and suggestions are very constructive for improving this manuscript. We have carefully revised the manuscript following your suggestions. All changes are marked in red font in the revised manuscript.

Weaknesses:

(1) The authors used five fragmentation metrics in their study. However, the choice of these fragmentation metrics was not well justified. The ecological significance of each fragmentation metric needs to be differentiated clearly. Also, these fragmentation metrics may be highly correlated with each other and redundant. I suggest author test the collinearity of these fragmentation metrics for influencing biodiversity and ecosystem function.

Response: Thanks for your constructive suggestion. The fragmentation metrics used in our study represent the different processes of breaking apart of habitat in the landscape, which are widely used by previous studies (Fahrig, 2003; Fahrig, 2017). In the revised manuscript, we have provided more detailed information about the ecological significance of these fragmentation indices.

Line 142-148:

“The patch density metric reflects the breaking apart of habitat in the landscape, which is a direct reflection of the definition of fragmentation per se (Fahrig et al., 2019). The edge density metric reflects the magnitude of the edge effect caused by fragmentation (Fahrig, 2017). The mean patch area metric and the mean nearest-neighbor distance metric are associated with the area and distance effects of island biogeography, respectively, reflecting the processes of local extinction and dispersal of species in the landscape (Fletcher et al., 2018).”

Meanwhile, we have calculated the variance inflation factors (VIF) for each fragmentation metric to assess their collinearity. The VIF of these fragmentation metrics were all less than four, suggesting no significant multicollinearity for influencing biodiversity and ecosystem function.

Author response table 2.

Variance inflation factors of habitat loss and fragmentation per se indices for influencing plant richness and above-ground biomass.

(2) I found the local environmental factors were not considered in the study. As the author mentioned in the manuscript, temperature and water also have important impacts on biodiversity and ecosystem function in the natural ecosystem. I suggest authors include the environmental factors in the data analysis to control their potential impact, especially the structural equation model.

Response: Thanks for your constructive suggestion. We agree with you that environmental factors should be considered in our study. In the revised manuscript, we have integrated two environmental factors related to water and temperature (soil water content and land surface temperature) into the data analysis to control their potential impact. The main results and conclusions of the revised manuscript are consistent with those of the previous manuscript.

Reviewer #3 (Recommendations For The Authors):

(1) L60-63. The necessity to distinguish between habitat loss and fragmentation per se is not clearly stated. More information about biodiversity conservation strategies can be given here.

Response: Thanks for your suggestion. In the revised manuscript, we have provided more evidence about the importance of distinguishing between habitat loss and fragmentation per se for biodiversity conservation.

Line 62-67:

“Habitat loss is often considered the major near-term threat to the biodiversity of terrestrial ecosystems (Chase et al., 2020; Haddad et al., 2015), while the impact of fragmentation per se remains debated (Fletcher Jr et al., 2023; Miller-Rushing et al., 2019). Thus, habitat loss and fragmentation per se may have inconsistent ecological consequences and should be considered simultaneously to establish effective conservation strategies in fragmented landscapes (Fahrig et al., 2019; Fletcher et al., 2018; Miller-Rushing et al., 2019).”

(2) L73-77. The two sentences are hard to follow. Please rephrase to improve the logic. And I don't understand the "however" here. There is no twist.

Response: Thanks for your suggestion. We have rephrased the two sentences to improve their logic.

Line 74-79:

“In theory, habitat loss and fragmentation per se can regulate ecosystem function and the BEF relationship by altering species composition, interactions, and spatial asynchrony regardless of changes in species richness (Liu et al., 2018; Thompson and Gonzalez, 2016; Tscharntke et al., 2012). This is because species in communities are not ecologically equivalent and may respond differently to habitat loss and fragmentation per se, and contribute unequally to ecosystem function (Devictor et al., 2008; Wardle and Zackrisson, 2005).”

(3) L97. Are grasslands really the largest terrestrial ecosystem? Isn't it the forest?

Response: We apologize for making this confusion. We have rephrased this sentence here.

Line 101-104:

“Grasslands have received considerably less attention, despite being one of the largest terrestrial ecosystems, and suffering severe fragmentation due to human activities, such as agricultural reclamation and urbanisation (Fardila et al., 2017).”

(4) Fig.1, whether the four sample plots presented in panel b are from panel a. Please add the scale bar in panel b.

Response: Thanks for your comment. The four sample plots presented in panel b are from panel a in Figure 1. We have also added the scale bar in panel b.

(5) L105. This statement is too specific. Please remove and consider merging this paragraph with the next.

Response: Thanks for your suggestion. We have removed this sentence and merged this paragraph with the next.

(6) L157. The accuracy and kappa value of the supervised classification should be given.

Response: Thanks for your suggestion. We have added the accuracy and kappa value of the supervised classification in the revised manuscript.

Line 176-177:

“The overall classification accuracy was 84.3 %, and the kappa coefficient was 0.81.”

(7) I would recommend the authors provide the list of generalists and specialists surveyed in the supplementary. Readers may not be familiar with the plant species composition in this area.

Response: Thanks for your suggestion. We agree with your point. We have provided the list of generalists and specialists surveyed in the Appendix Table A4.

Line 282-283:

“A total of 130 vascular plant species were identified in our study sites, including 91 grassland specialists and 39 weeds (Appendix Table A4).”

(8) Fig.4, it is better to add the results of variation partition to present the relative contribution of habitat fragmentation, environmental factors, and plant diversity.

Response: Thanks for your suggestion. We have integrated the landscape context, environmental factors, and plant diversity into the multi-model averaging analysis and redraw Figure 4 to present their relative importance for above-ground biomass.

Line 313-319:

Author response image 3.

Standardised parameter estimates and 95% confidence intervals for landscape context, plant diversity, and environmental factors affecting above-ground biomass from 130 landscapes in the Tabu River Basin, a typical agro-pastoral ecotone of northern China. Standardised estimates and 95% confidence intervals are calculated by the multi-model averaging method based on the four optimal models affecting above-ground biomass (Appendix Table A3). ** represent significance at the 0.01 level.

(9) Please redraw Fig.2 and Fig.5 to integrate the environmental factors. Add the R-square to Fig 5.

Response: Thanks for your suggestion. We have integrated two environmental factors into the structural equation model and redraw Figure 2 and Figure 5 in the revised manuscript. And we have added the R-square to the Figure 5.

(10) L354. The authors should be careful to claim that habitat loss could reduce the importance of plant diversity to ecosystem function. This pattern observed may depend on the type of ecosystem function studied.

Response: Thanks for your suggestion. We have avoided this claim in the revised manuscript and explicitly discussed the importance of simultaneously focusing on multiple ecosystem functions, such as below-ground productivity, litter decomposition, soil carbon stocks, etc.

Line 454-457:

“This inconsistency can be explained by trade-offs between different ecosystem functions that may differ in their response to fragmentation per se (Banks-Leite et al., 2020). Therefore, future studies are needed to focus on multiple ecosystem functions, such as below-ground productivity, litter decomposition, soil carbon stocks, etc.”

Author Response

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

eLife assessment

This valuable study seeks to disentangle the different selective forces shaping the evolutionary dynamics of transposable elements (TEs) in the wild grass Brachypodium distachyon. Using haplotype-length metrics, and genetic and environmental differentiation tests, the authors present in large parts convincing evidence that positive selection on TE polymorphisms is rare, and that the distribution of TE ages points to purifying selection being the main force acting on TE evolution in this species. A caveat of this study, as of other studies that seek to assess TE insertion polymorphisms with short reads, is that the rates of false negatives and false positives are difficult to estimate, which may have major effects on the interpretation. This study will be relevant for anyone interested in the role of TEs in evolution and adaptation.

Thank you for considering our manuscript for publication in eLife. We appreciate the constructive comments and suggestions of the reviewers. We have addressed the raised issues by the reviewers. Below, we provide a more detailed response to each of the reviewer comments.

Public Reviews:

Reviewer #1:

The study presented in this manuscript presents very convincing evidence that purifying selection is the main force shaping the landscape of TE polymorphisms in B. distachyon, with only a few putatively adaptive variants detected, even though most conclusions are based on the 10% of polymorphisms contributed by retrotransposons. That first conclusion is not novel, however, as it had already been clearly established in natural A. thaliana strains (Baduel et al. Genome Biol 2021) and in experimental D. simulans lines (Langmüller et al. NAR 2023), two studies that the authors do not mention, or improperly mention. In contrast to the conclusions reached in A. thaliana, however, Horvath et al. report here a seemingly deleterious effect of TE insertions even very far away from genes (>5kb), a striking observation for a genome of relatively similar size. If confirmed, as a caveat of this study is the lack of benchmarking of the TE polymorphisms calls by a pipeline known for a high rate of false positives (see detailed Private Recommendations #1), this set of observations would make an important addition to the knowledge of TE dynamics in the wild and questioning our understanding of the main molecular mechanisms through which TEs can impact fitness.

Thank you for your positive evaluation of our paper. We have now adjusted the manuscript to include the mentioned studies (Line 330-333) and to address the issue of false positive and false negative calls. The detailed responses to all the raised points are below.

Reviewer #2:

Summary:

Transposable elements are known to have a strong potential to generate diversity and impact gene regulation, and they are thought to play an important role in plant adaptation to changing environments. Nevertheless, very few studies have performed genome-wide analyses to understand the global effect of selection on TEs in natural populations. Horvath et al. used available whole-genome re-sequencing data from a representative panel of B. distachyon accessions to detect TE insertion polymorphisms (TIPs) and estimate their time of origin. Using a thorough combination of population genomics approaches, the authors demonstrate that only a small amount of the TE polymorphisms are targeted by positive selection or potentially involved in adaptation. By comparing the age-adjusted population frequencies of TE polymorphisms and neutral SNPs, the authors found that retrotransposons are affected by purifying selection independently of their distance to genes. Finally, using forward simulations they were able to quantify the strength of selection acting on TE polymorphisms, finding that retrotransposons are mainly under moderate purifying selection, with only a minority of the insertions evolving neutrally.

Strengths:

Horvath et al., use a convincing set of strategies, and their conclusions are well supported by the data. I think that incorporating polymorphism's age into the analysis of purifying selection is an interesting way to reduce the possible bias introduced by the fact that SNPs and TEs polymorphisms do not occur at the same pace. The fact that TE polymorphisms far from genes are also under purifying selection is an interesting result that reinforces the idea that the trans-regulatory effect of TE insertions might not be a rare phenomenon, a matter that may be demonstrated in future studies.

Weaknesses:

TEs from different classes and orders strongly differ in multiple features such as size, the potential impact of close genes upon insertion, insertion/elimination ratio (ie, MITE/TIR excision, solo-LTR formation), or insertion preference. Given such diversity, it is expected that their survival rates on the genome and the strength of selection acting on them could be different. The authors differentiate DNA transposons and retrotransposons in some of the analyses, the specificities of the most abundant plant TE types (ie, LTR/Gypsy, LTR/Copia, MITE DNA transposons) are not considered.

The authors used a short-read-based approach to detect TIPs and TAPs. It is known that detecting TE polymorphisms is challenging and can lead to false negatives, depending on the method used and the sequencing coverage. The methodology used here (TEPID) has been previously applied to other species, but it is unclear if the sensitivity of the TIP/TAP caller is equivalent to that of the SNP caller and how these potential differences may affect the results.

Thank you for your positive evaluation of our paper. We have now adjusted the manuscript and the discussion to include the mentioned points on the different TE superfamilies and the reliability of the TE calls. The detailed responses to all the raised points are below.

Private Recommendations:

Reviewer #1:

(1) TE polymorphisms (presence and absence variants) were called from short-read sequencing data using a pipeline (TEPID, Stuart et al. eLife 2016) that is known to have a low specificity as well as a low sensitivity in its detection of presence variants (Baduel et al. MIMB 2021). An assessment of the rate of false positives and false negatives in the data presented in this study and how it varies across TE superfamilies is therefore of crucial importance as it may bias all downstream analyses, especially if it impacts the identification of polymorphisms contributed by retrotransposons, as these are the basis of most conclusions of the manuscript. Nonetheless, the fact that the PCA of the polymorphisms contributed by DNA transposons is less able to distinguish genetic clades than with those contributed by retrotransposons, suggests the issue of false positives is most preeminent for DNA transposons. However, high rates of false positives may explain why no significant increase in TE frequency is detected within selective sweep regions, a result that runs against the expectation of hitch-hiking of neutral or weakly deleterious polymorphisms which the authors claim is the category of many TE polymorphisms. Furthermore, given that the reference genome belongs to the B_east clade, and the TEPID is better at calling absence than presence it may bias analyses in this clade (where clade-specific insertions will take the form of absence in other clades which are well detected) compared to other clades (where clade-specific insertions will be presence polymorphisms and may be missed). A benchmark of TE polymorphism calls could be done by de novo assembling one genome from each clade or by cross-checking at least the presence variant calls from TEPID with those made with another of the many TE calling pipelines available.

We agree with this issue raised by both reviewers regarding the effects of false negative and false positive TE calls. We also think that some reasonable follow-ups should be done to check the potential impact of the false negative and false positive TE calls on the presented results, without turning the manuscript in a method comparison paper as this is not the main goal of this study. Therefore, we generated a subsample of our dataset that included only accession with an average genome wide mapping coverages of at least 20x, as the false negative TE call rate is correlated with the mapping coverage and a high mapping coverage is expected to lead to a reduction in the false negative TE call rates. We then used this subsample to check if our results would change if our dataset had a lower false negative TE call rate. However, reducing the rate of false negative calls through the use of only higher coverage samples did not change our results and interpretations.

Re-running the ANCOVA analyses revealed similar results regarding the accumulation of TEs in selective sweep regions. This was added to the main text Line 143-148: “Similar results were obtained when investigating the number of fixed TE polymorphisms (Additional file 2: Table S1) and the allele frequency of TE polymorphisms (Additional file 2: Table S2) in high iHS regions using a subset of our dataset with an expected lower false negative TE call rate, that only included samples with a genome-wide mapping coverage of at least 20x (see Discussion and Materials and Methods for more details).” and in Additional file 2: Table S1 and S2.

Further, we re-ran the age-adjusted SFS based on this subset of our dataset and found that the results and conclusions from the age-adjusted SFS were not only driven by false negative TE calls. This was also included in the text Line 338-349: “One caveat of the approach used in this study is that TE calling pipelines based on short-reads tend to have higher false positive and false negative call rates than SNP calling pipelines, which is also the case for the TEPID TE calling pipeline used here [57, 59]. A high false negative TE calling rate however might bias our TE frequency estimates toward lower frequencies, which could drive the observed patterns in the age-adjusted SFS. To assess if the false negative TE calling rate in our study substantially affected our results, we re-run the age-adjusted SFS on a subset of our dataset only including samples with a genome-wide mapping coverage of at least 20x, as higher mapping coverages are expected to reduce the false negative call rate [27, 59]. Using the TE allele frequencies estimated based on this subset of our data to estimate  frequency revealed similar results of the age-adjusted SFS based on the whole dataset (Additional file 1: Fig. S9), indicating that our observation of retrotransposons evolving under purifying selection is not solely driven by a high false negative TE calling rate.” and in Additional file 1: Fig. S9.

The details of this analyses have been added to the materials and methods Line 493-498: “Mapping coverage is known to influence false discovery rate [27, 59]. To investigate the impact of false positive and false negative TE calls on our results, we down sampled the TE dataset to only include TEs that have been called in samples that had at least an average mapping coverage of 20x. The allele frequencies of TEs present in our high coverage dataset was recalculated only considering samples with at least an average mapping coverage of 20x. This second TE dataset was then used to check if using a dataset with a higher mapping coverage and presumably a lower false TE calling rate impacted our results.”

(2) If confirmed, the observation that retrotransposons located more than 5kb away from genes appear to be also affected by purifying selection (L209) is indeed surprising. The authors should add a comparison with SNPs at the same distance from genes to strengthen the claim and make sure it is not the result of mapping artifacts, such as alignment quality dropping far away from genes.

We added a comparison of the age-adjusted SFS of SNPs and retrotransposons more than 5 kb away from genes to evaluate if the observed shape of the age-adjusted SFS of retrotransposons more than 5 kb away from genes were due to artefacts. The results are included on line 383-389: “Finally, we tested whether TE polymorphisms located more than 5 kb away from genes are evolving under purifying selection could be due to mapping or other artefacts by comparing the shape of the age-adjusted SFS of retrotransposons and SNPs more than 5 kb away from genes. However, the age-adjusted SFS of SNPs 5 kb away from genes differs from the one of retrotransposons (Additional file 1: Fig. S10), indicating that the shape of the age-adjusted SFS of retrotransposons more than 5 kb away from genes is not likely to be the result of artefacts in regions of the genome far away from genes.” and Additional file 1: Fig. S10.

(3) The authors' claim that most TE polymorphisms are under weak to moderate purifying selection (L273) relies on the comparison of the age of polymorphisms in the oldest age bin with forward simulations. However, the conclusions from these comparisons cannot be extrapolated to the fitness effects of all TE polymorphisms as variants in the oldest age bin are de facto a biased sample of the variants of a category, a point the authors highlight.

We adjusted the mentioned paragraph to better highlight this point. Line 390-397: “To further ascertain the strength of purifying selection, we used forward simulation and showed that simulations assuming a moderately weak selection pressure (S = -5 or S = -8) against TE polymorphisms best fitted our observed data. In theory, no TE polymorphisms under strong purifying selection should be present in a natural population, as such mutations are expected to be quickly lost, especially in a predominantly selfing species where most loci are expected to be homozygous. Therefore, it is not surprising that TE polymorphisms which persist in B. distachyon are under weak to moderate selection, as also shown, for example, for the L1 retrotransposons in humans [27] or the BS retrotransposon family in Drosophila melanogaster [62].”

L220-228 for high-effect SNPs. Indeed, the most deleterious TE polymorphisms would be purged very quickly and never contribute to variants in the oldest age bin. Unless new arguments can be made to support this claim, this conclusion should be rephrased to claim instead that even the oldest TE polymorphisms are still mostly non-neutral and under weak to moderate purifying.

This has been adjusted. Line 231-232: “. Hence, even the oldest retrotransposon polymorphisms seem to be mostly non-neutral and are affected by purifying selection.”

L214: replace smaller with more negative for clarity.

Done.

L233: Given the discussion L220-228, the oldest age bin seems to be biased in its composition and thus not useful for comparisons. The sentence should therefore be rephrased to reflect that DNA transposon polymorphisms appear to be actually less deleterious than high-effect SNPs in S9A and B based on the penultimate age bin.

This has been fixed.

Reviewer #2:

• I wonder if false negative detection could artificially increase the evidence for purifying selection by increasing the amount of low-frequency variants. This could be easily checked if long-read data or genome assembly is available for any of the samples in the collection, by comparing the TIP/TAP prediction with the actual sequence.

We agree with this point from the reviewers that false negative calls can lead to misinterpretations of the observed low-frequencies of the TEs. (But see response to the first comment of reviewer #1). Unfortunately, long-read data from the sample used here are not available to estimate false negative call rates. However, to check if the observed results are manly driven by high false negative rates, we re-run the age-adjusted SFS based on samples with at least 20x mapping coverage, which should result in the reduction the false negative TE calling rate. The results and conclusions from this second analyses were included in the text Line 338-349: “One caveat of the approach used in this study is that TE calling pipelines based on short-reads tend to have higher false positive and false negative call rates than SNP calling pipelines, which is also the case for the TEPID TE calling pipeline used here [57, 59]. A high false negative TE calling rate however might bias our TE frequency estimates toward lower frequencies, which could drive the observed patterns in the age-adjusted SFS. To assess if the false negative TE calling rate in our study substantially affected our results, we re-run the age-adjusted SFS on a subset of our dataset only including samples with a genome-wide mapping coverage of at least 20x, as higher mapping coverages are expected to reduce the false negative call rate [27, 59]. Using the TE allele frequencies estimated based on this subset of our data to estimate  frequency revealed similar results of the age-adjusted SFS based on the whole dataset (Additional file 1: Fig. S9), indicating that our observation of retrotransposons evolving under purifying selection is not solely driven by a high false negative TE calling rate.” and in Additional file 1: Fig. S9.

• Supplementary Figure S1. DNA transposons are much worse at separating the samples in comparison to LTR-retrotransposons. Doesn´t this suggest that these two classes have very different dynamics in the population and maybe different intensities of the selection forces acting on them? Could this profile be explained as DNA transposons being older and likely more fixed in all the clades, whereas retrotransposons are more recent and more specific to some populations? Another possibility might be that some B. distachyon DNA transposons had an unusually high excision rate. In any case, in my opinion, this reinforces the need to study the different TE orders in more detail.

Indeed, different TE orders and superfamilies can have different excision rates, age distributions and be under different selective regimes. To investigate the possibility that different TE orders are affected by very different selective regimes, we split our TE dataset into the four different TE types: Copia, Ty3, Helitron and MITE. We than re-run the age-adjusted SFS analyses and added our results to the text Line 422-430: “To further examine our conclusion on purifying selection, we investigated the selective regime affecting different retrotransposons and DNA-transposons superfamilies. Thereby, we generated age-adjusted SFS for the four most common TE superfamilies Copia, Ty3 (also known under the name Gypsy, but we will avoid using this name because of its problematic nature see [71]), Helitron and MITE and found similar deviations of the  frequency from 0 in the four investigated TE superfamilies (Additional file 1: Fig. S12–S15). These results indicate that our conclusion on the broad effect of purifying selection is not driven by a single TE superfamily but is at least common among the four most numerous TE superfamilies.” and in Additional file 1: Fig. S12- S15.

• Line 112: "most TE polymorphisms in our dataset were young and only a few were very old". Does this change substantially among TE orders/superfamilies?

Indeed, there are some differences in the age distribution of the TEs depending on the superfamilies, However, the differences are no substantial as the age bins in the age-adjusted SFS of the different TE superfamilies are fairly similar. See Additional file 1: Fig. S12-S15.

• Figure 2. Is difficult to read, especially lower panels. I think the grey border of the boxplots makes visualization difficult.

The gray borders have been removed.

Author Response

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

eLife Assessment

This useful study could potentially represent a step forward towards personalized medicine by combining cell-based data and a prior-knowledge network to derive Boolean-based predictive logic models to uncover altered protein/signaling networks within cancer cells. However, the level of evidence supporting the conclusions is inadequate, and further validation of the reported approach is required. If properly validated, these findings could be of interest to medical biologists working in the field of cancer and would inform drug development and treatment choices in the field of oncology.

We thank the editor and the reviewer for their constructive comments, which helped us to improve our story. We have now performed new analyses and experiments to further support our proposed approach.

Public Reviews:

Reviewer #1 (Public Review):

(1) The authors deploy a combination of their own previously developed computational methods and databases (SIGNOR and CellNOptR) to model the FLT3 signaling landscape in AML and identify synergistic drug combinations that may overcome the resistance AML cells harboring ITD mutations in the TKI domain of FLT3 to FLT3 inhibitors. I did not closely evaluate the details of these computational models since they are outside of my area of expertise and have been previously published. The manuscript has significant issues with data interpretation and clarity, as detailed below, which, in my view, call into question the main conclusions of the paper.

The authors train the model by including perturbation data where TKI-resistant and TKIsensitive cells are treated with various inhibitors and the activity (i.e. phosphorylation levels) of the key downstream nodes are evaluated. Specifically, in the Results section (p. 6) they state "TKIs sensitive and resistant cells were subjected to 16 experimental conditions, including TNFa and IGF1 stimulation, the presence or absence of the FLT3 inhibitor, midostaurin, and in combination with six small-molecule inhibitors targeting crucial kinases in our PKN (p38, JNK, PI3K, mTOR, MEK1/2 and GSK3)". I would appreciate more details on which specific inhibitors and concentrations were used for this experiment. More importantly, I was very puzzled by the fact that this training dataset appears to contain, among other conditions, the combination of midostaurin with JNK inhibition, i.e. the very combination of drugs that the authors later present as being predicted by their model to have a synergistic effect. Unless my interpretation of this is incorrect, it appears to be a "self-fulfilling prophecy", i.e. an inappropriate use of the same data in training and verification/test datasets.

We thank the reviewer for this comment. We have now extensively revised the Figure 2B and edited the text to clarify and better describe the experimental conditions of our multiparametric analysis. As the reviewer stated, we have used different combinations of drugs, including midostaurin and JNK inhibitor to generate two cell-specific predictive models recapitulating the main signal transduction events, down-stream FLT3, occurring in resistant (FLT3ITD-TKD) and sensitive (FLT3ITD-JMD) cells. These experiments were performed by treating cells at very early time points to obtain a picture of the signaling response of FLT3-ITD positive cells. Indeed, we have measured the phosphorylation level of signaling proteins, because at these early time points (90 minutes) we do not expect a modulation of downstream crucial phenotypes, including apoptosis or proliferation. To infer perturbations impacting the apoptosis or proliferation phenotypes, we applied a computational two-steps strategy:

(1) We extracted key regulators of ‘apoptosis’ and ‘proliferation’ hallmarks from SIGNOR database.

(2) We applied our recently developed ProxPath algorithm to retrieve significant paths linking nodes of our two optimized models to ‘proliferation’ and ‘apoptosis’ phenotypes.

This allowed us to evaluate in silico the “proliferation” and “apoptosis” rate upon inactivation of each node of the network. With the proposed approach, we identified JNK as a potential drug target to use in combination with FLT3 to restore sensitivity (i.e. in silico inducing apoptosis and reducing proliferation) of FLT3 ITD-TKD cells. We here want to stress once more that although the first piece of information (the effect of JNK and FLT3 inhibition) on sentinel readouts was provided in the training dataset, the second piece of information (the effect on this treatment over the entire model and, as a consequence, on the cellular phenotype) was purely the results of our computational models. As such, we hope that the reviewer will agree that this could not represent a “self-fulfilling prophecy".

That said, we understand that this aspect was not clearly defined in the manuscript. For this reason, we have now 1) extensively revised the Figure 2B; 2) edited the text (pg. 6) to clarify the purpose and the results of our approach; and 3) described in further detail (pg. 16-18) the experimental conditions of our multiparametric analysis.

(2) My most significant criticism is that the proof-of-principle experiment evaluating the combination effects of midostaurin and SP600125 in FLT3-ITD-TKD cell line model does not appear to show any synergism, in my view. The authors' interpretation of the data is that the addition of SP600125 to midostaurin rescues midostaurin resistance and results in increased apoptosis and decreased viability of the midostaurin-resistant cells. Indeed, they write on p.9: "Strikingly, the combined treatment of JNK inhibitor (SP600125) and midostaurin (PKC412) significantly increased the percentage of FLT3ITD-TKD cells in apoptosis (Fig. 4D). Consistently, in these experimental conditions, we observed a significant reduction of proliferating FLT3ITD- TKD cells versus cells treated with midostaurin alone (Fig. 4E)." However, looking at Figs 4D and 4E, it appears that the effects of the midostaurin/SP600125 combination are virtually identical to SP600125 alone, and midostaurin provides no additional benefit. No p-values are provided to compare midostaurin+SP600125 to SP600125 alone but there seems to be no appreciable difference between the two by eye. In addition, the evaluation of synergism (versus additive effects) requires the use of specialized mathematical models (see for example Duarte and Vale, 2022). That said, I do not appreciate even an additive effect of midostaurin combined with SP600125 in the data presented.

We agree with the reviewer that the JNK inhibitor and midostaurin do not have neither a synergic nor additive effect and we have now revised the text accordingly. It is highly discussed in the scientific community whether FLT3ITD-TKD AML cells benefit from midostaurin treatments. In a recently published retroprospective study of K. Dohner et al. (Rücker et al., 2022), the authors investigated the prognostic and predictive impact of FLT3-ITD insertion site (IS) in 452 patients randomized within the RATIFY trial, which evaluated midostaurin additionally to intensive chemotherapy. Their study clearly showed that “Midostaurin exerted a significant benefit only for JMDsole” patients. In agreement with this result, we have demonstrated that midostaurin treatment had no effects on apoptosis of blasts derived from FLT3ITD-TKD patients (Massacci et al., 2023). On the other hand, we and others observed that midostaurin triggers apoptosis in FLT3ITD-TKD cells to a lesser extent as compared to FLT3ITDJMD cells (Arreba-Tutusaus et al., 2016). The data presented here (Fig. 4) and our previously published papers (Massacci et al., 2023; Pugliese et al., 2023) pinpoint that hitting cell cycle regulators (WEE1, CDK7, JNK) induce a significant apoptotic response of TKI resistant FLT3ITD-TKD cells. Prompted by the reviewer comment, we have now revised the text and discussion (pg.9; 14) highlighting the crucial role of JNK in apoptosis induction.

(3) In my view, there are significant issues with clarity and detail throughout the manuscript. For example, additional details and improved clarity are needed, in my view, with respect to the design and readouts of the signaling perturbation experiments (Methods, p. 15 and Fig 2B legend). For example, the Fig 2B legend states: "Schematic representation of the experimental design: FLT3 ITD-JMD and FLT3 ITD-JMD cells were cultured in starvation medium (w/o FBS) overnight and treated with selected kinase inhibitors for 90 minutes and IGF1 and TNFa for 10 minutes. Control cells are starved and treated with PKC412 for 90 minutes, while "untreated" cells are treated with IGF1 100ng/ml and TNFa 10ng/ml with PKC412 for 90 minutes.", which does not make sense to me. The "untreated" cells appear to be treated with more agents than the control cells. The logic behind cytokine stimulation is not adequately explained and it is not entirely clear to me whether the cytokines were used alone or in combination. Fig 2B is quite confusing overall, and it is not clear to me what the horizontal axis (i.e. columns of "experimental conditions", as opposed to "treatments") represents. The Method section states "Key cell signaling players were analyzed through the X-Map Luminex technology: we measured the analytes included in the MILLIPLEX assays" but the identities of the evaluated proteins are not given in the Methods. At the same time, the Results section states "TKIs sensitive and resistant cells were subjected to 16 experimental conditions" but these conditions do not appear to be listed (except in Supplementary data; and Fig 2B lists 9 conditions, not 16). In my subjective view, the manuscript would benefit from a clearer explanation and depiction of the experimental details and inhibitors used in the main text of the paper, as opposed to various Supplemental files/Figures. The lack of clarity on what exactly were the experimental conditions makes the interpretation of Fig 2 very challenging. In the same vein, in the PCA analysis (Fig 2C) there seems to be no reference to the cytokine stimulation status while the authors claim that PC2 stratifies cells according to IGF1 vs TNFalpha. There are numerous other examples of incomplete or confusing legends and descriptions which, in my view, need to be addressed to make the paper more accessible.

We thank the reviewer for his/her comment. We have now extensively revised the text of the manuscript (pg. 6), revised Fig. 2B (now Fig 2C) and methods (pg. 16-18) to improve the clarity of our manuscript, making the take-home messages more accessible. We believe that the revised versions of text and of Figure 2 better explain our strategy and clarify the experimental set up, we added details on the choices of the experimental conditions, and we proposed a better graphic representation of the analysis.

(4) I am not sure that I see significant value in the patient-specific logic models because they are not supported by empirical evidence. Treating primary cells from AML patients with relevant drug combinations would be a feasible and convincing way to validate the computational models and evaluate their potential benefit in the clinical setting.

We thank the reviewer for this comment. We have now performed additional experiments in a small cohort of FLT3-ITD positive patient-derived primary blasts. Specifically, we have treated blasts from 2 FLT3ITD-TKD patients and 3 FLT3ITD-JMD+TKD patients with PKC412 (100nM) 24h and/or 10μM SP600125 (JNK inhibitor). After 24h of treatment we have measured the apoptotic rate. As shown below and in the new Fig. 4F (see pg.10, main text), midostaurin triggers higher levels of apoptosis in FLT3ITD-JMD+TKD blasts as compared to FLT3ITD-TKD blasts. Importantly, treatment with the JNK inhibitor SP600125 alone triggers apoptosis in FLT3ITD-TKD blasts, validating the crucial role of JNK in FLT3ITD-TKD cell survival and TKI resistance. The combined treatment of midostaurin and SP600125 increases the percentage of apoptotic cells as compared to midostaurin treatment alone but to a lesser extent than single agent treatment. This result is in agreement with the current debate in the scientific community on the actual beneficial effect of midostaurin treatment in FLT3ITD-TKD AML patients.

Author response image 1.

Primary samples from AML patients with the FLT3ITD-TKD mutation (n=2, yellow bars) or the FLT3ITD-JMD/TKD mutation (n=3, blue bars) were exposed to Midostaurin (100nM, PKC412), and JNK inhibitor (10µM, SP600125) for 48 hours, or combinations thereof. The specific cell death of gated AML blasts was calculated to account for treatment-unrelated spontaneous cell death. The bars on the graph represent the mean values with standard errors.

Reviewer #2 (Public Review):

Summary:

This manuscript by Latini et al describes a methodology to develop Boolean-based predictive logic models that can be applied to uncover altered protein/signalling networks in cancer cells and discover potential new therapeutic targets. As a proof-of-concept, they have implemented their strategy on a hematopoietic cell line engineered to express one of two types of FLT3 internal tandem mutations (FLT3-ITD) found in patients, FLT3-ITD-TKD (which are less sensitive to tyrosine kinase inhibitors/TKIs) and FLT3-ITD-JMD (which are more sensitive to TKIs).

Strengths:

This useful work could potentially represent a step forward towards personalised targeted therapy, by describing a methodology using Boolean-based predictive logic models to uncover altered protein/signalling networks within cancer cells. However, the weaknesses highlighted below severely limit the extent of any conclusions that can be drawn from the results.

Weaknesses:

While the highly theoretical approach proposed by the authors is interesting, the potential relevance of their overall conclusions is severely undermined by a lack of validation of their predicted results in real-world data. Their predictive logic models are built upon a set of poorlyexplained initial conditions, drawn from data generated in vitro from an engineered cell line, and no attempt was made to validate the predictions in independent settings. This is compounded by a lack of sufficient experimental detail or clear explanations at different steps. These concerns considerably temper one's enthusiasm about the conclusions that could be drawn from the manuscript.

We thank the reviewer for the thorough review and kind comments about our manuscript. We hope the changes and new data we provide further strengthen it in his or her eyes.

Some specific concerns include:

(1) It remains unclear how robust the logic models are, or conversely, how affected they might be by specific initial conditions or priors that are chosen. The authors fail to explain the rationale underlying their input conditions at various points. For example: - at the start of the manuscript, they assert that they begin with a pre-PKN that contains "76 nodes and 193 edges", though this is then ostensibly refined with additional new edges (as outlined in Fig 2A). However, why these edges were added, nor model performance comparisons against the basal model are presented, precluding an evaluation of whether this model is better.

We understand the reviewer’s concern. We have now complemented the manuscript with an extended version of the proposed modelling strategy offering a detailed description of the pipeline and the rationale behind each choice (Supplementary material, pg.14-19). Furthermore, we also referenced the manuscript to a GitHub repository where users can follow and reproduce each step of the pipeline (https://github.com/SaccoPerfettoLab/FLT3ITD_driven_AML_Boolean_models).

• At a later step (relevant to Fig S4 and Fig 3), they develop separate PKNs, for each of the mutation models, that contain "206 [or] 208 nodes" and "756 [or] 782 edges", without explaining how these seemingly arbitrary initial conditions were arrived at. Their relation to the original parameters in the previous model is also not investigated, raising concerns about model over-fitting and calling into question the general applicability of their proposed approach. The authors need to provide a clearer explanation of the logic underlying some of these initial parameter selections, and also investigate the biological/functional overlap between these sets of genes (nodes).

We thank the reviewer for raising this question. Very briefly, the proposed optimization strategy falls in a branch of the modelling, where the predictive model is, indeed, driven by the data (Blinov and Moraru, 2012). From a certain point of view, the scope of optimization is the one of fitting the experimental data in the best way possible. To achieve this, we followed standard practices (Dorier et al., 2016; Traynard et al., 2017). To address the issue of “calling into question the general applicability of their proposed approach”, we have compared the activity status of nodes in the models with ‘real data’ extracted from cell lines and patients’ samples to reassure about the robustness and scalability of the strategy (please see below, response to point 3 pg. 9).

Finally, as mentioned in the previous point, we have now provided a detailed supplementary material, where we have described all the aspects mentioned by the reviewer: step-by-step changes in the PKN, the choice of the parameters and other details can be traced over the novel text and are also available in the GitHub repository (https://github.com/SaccoPerfettoLab/FLT3-ITD_driven_AML_Boolean_models).

(2) There is concern about the underlying experimental data underpinning the models that were generated, further compounded by the lack of a clear explanation of the logic. For example, data concerning the status of signalling changes as a result of perturbation appears to be generated from multiplex LUMINEX assays using phosphorylation-specific antibodies against just 14 "sentinel" proteins. However, very little detail is provided about the rationale underlying how these 14 were chosen to be "sentinels" (and why not just 13, or 15, or any other number, for that effect?). How reliable are the antibodies used to query the phosphorylation status? What are the signal thresholds and linear ranges for these assays, and how would these impact the performance/reliability of the logic models that are generated from them?

We thank the reviewer for this comment as it gives us the opportunity to clarify and better explain the criteria behind the experimental data generation.

Overall, we revised the main text at page 6 and the Figure 2B to improve the clarity of our experimental design. Specifically, the sentinels were chosen because they were considered indirect or direct downstream effectors of the perturbations and were conceived to serve as both a benchmarking system of the study and a readout of the global perturbation of the system. To clarify this aspect, we have added a small network (compressed PKN) in Figure 2B to show that the proteins (green nodes) we chose to measure in the LUMINEX multiplex assay are “sentinels” of the activity of almost all the pathways included in the Prior knowledge network. Moreover, we implemented the methods section “Multiparametric experiment of signaling perturbation” (pg. 16-18), where we added details about the antibodies used in the assay paired with the target phosphosites and their functional role (Table 3). We also better specified the filtering process based on the number of beads detected per each antibody used (pg. 18). About the reliability of the measurements, we can say that the quality of the perturbation data impacts greatly on the logic models’ performance. xMAP technology been already used by the scientific community to generate highly reproducible and reliable multiparametric dataset for model training (Terfve et al., 2012). Additionally, we checked that for each sentinel we could measure a fully active state, a fully inactive state and intermediate states. Modulation of individual analytes are displayed in Figure S3.

Author response image 2.

Partial Figure of normalization of analytes activity through Hill curves. Experimental data were normalized and scaled from 0 to 1 using analyte-specific Hill functions. Raw data are reported as triangles, normalized data and squares. Partial Figure representing three plots of the FLT3 ITD-JMD data (Complete Figure in Supplementary material Fig S3).

(3) In addition, there are publicly available quantitative proteomics datasets from FLT3-mutant cell lines and primary samples treated with TKIs. At the very least, these should have been used by the authors to independently validate their models, selection of initial parameters, and signal performance of their antibody-based assays, to name a few unvalidated, yet critical, parameters. There is an overwhelming reliance on theoretical predictions without taking advantage of real-world validation of their findings. For example, the authors identified a set of primary AML samples with relevant mutations (Fig 5) that could potentially have provided a valuable experimental validation platform for their predictions of effective drug combination. Yet, they have performed Boolean simulations of the predicted effects, a perplexing instance of adding theoretical predictions on top of a theoretical prediction!

Additionally, there are datasets of drug sensitivity on primary AML samples where mutational data is also known (for example, from the BEAT-AML consortia), that could be queried for independent validation of the authors' models.

We thank the reviewer for this comment that helped us to significantly strengthen our story. Prompted by his/her comment, we have now queried three different datasets for independent validation of our logic models. Specifically, we have taken advantage of quantitative phosphoproteomics datasets of FLT3-ITD cell lines treated with TKIs (Massacci et al., 2023), phosphoproteomic data of FLT3-ITD positive patients-derived primary blast (Kramer et al., 2022) and of drug sensitivity data on primary FLT3-ITD positive AML samples (BEAT-AML consortia)

• Comparison with phosphoproteomic data of FLT3-ITD cell lines treated with TKIs (Massacci et al., 2023)

Here, we compared the steady state of our model upon FLT3 inhibition with the phosphoproteomic data describing the modulation of 16,319 phosphosites in FLT3-ITD BaF3 cells (FLT3ITD-TKD and FLT3ITD-JMD) upon TKI treatment (i.e. quizartinib, a highly selective FLT3 inhibitor). As shown in the table below and new Figure S5A, the activation status of the nodes in the two generated models is highly comparable with the level of regulatory phosphorylations reported in the reference dataset. Briefly, to determine the agreement between each model and the independent dataset, we focused on the phosphorylation level of specific residues that (i) regulate the functional activity of sentinel proteins (denoted in the ‘Mode of regulation’ column) and (ii) that were measured in this work to train the model. So, we cross-referenced the sentinel protein status in FLT3 inhibition simulation (as denoted in the 'Model simulation of FLT3 inhibition' column) with the functional impact of phosphorylation measured in Massacci et. al dataset (as denoted in the 'Functional impact in quizartinib dataset' column). Points of congruence were summarized in the 'Consensus' column. As an example, if the phosphorylation level of an activating residue decreases (e.g., Y185 of Mapk1), we can conclude that the protein is inhibited (‘Down-reg’) and this is coherent with model simulation in which Mapk1 is ‘Inactive’.

Author response image 3.

• Comparison with phosphoproteomic data of FLT3-ITD patient-derived primary blasts (Kramer et al., 2022)

Using the same criteria, we extended our validation efforts by comparing the activity status of the proteins in the “untreated” simulation (i.e. reproducing the tumorigenic state where FLT3, IGF1R and TNFR are set to be active) with their phosphorylation levels in the dataset by Kramer et al. (Kramer et al., 2022). Briefly, this dataset gathers phosphoproteomic data from a cohort of 44 AML patients and we restricted the analysis to 11 FLT3-ITD-positive patients. Importantly, all patients carry the ITD mutation in the juxta membrane domain (JMD), thus allowing for the comparison with FLT3 ITD-JMD specific Boolean model, exclusively.

The results are shown in the heatmap below. Each cell in the heatmap reports the phosphorylation level of sentinel proteins’ residues in the indicated patient (red and blue indicate up- or- down-regulated phosphoresidues, respectively). Patients were clustered according to Pearson correlation. We observed a good level of agreement between the patients’ phosphoproteomics data and our model (reported in the column “Tumor simulation steady state”) for a subset of patients highlighted within the black rectangle. However, for the remaining patients, the level of agreement is poor. The main reason is that our work focuses on FLT3-ITD signaling and a systematic translation of the Boolean modeling approach to the entire cohort of AML patients would require the inclusion of the impact of other driver mutations in the network. This is actually a current and a future line of investigation of our group. We have revised the discussion, taking this result into consideration.

Author response image 4.

• Comparison with drug sensitivity data on primary FLT3-ITD positive AML samples (BEAT-AML consortia)

Here we took advantage of the Beat AML programme on a cohort of 672 tumour specimens collected from 562 patients. The BEAT AML consortium provides whole-exome sequencing, RNA sequencing and analyses of ex vivo drug sensitivity of this large cohort of patient-derived primary blasts. We focused on drug sensitivity screening on 134 patients carrying the typical FLT3-ITD mutation in the JMD region. Unfortunately, the ITD insertion in the TKD region is less characterized and additional in-depth sequencing studies are required to identify in this cohort FLT3ITD-TKD positive blasts. Next, we focused on those compounds hitting nodes present in the FLT3ITD-JMD Boolean model. Specifically, we selected drugs inhibiting FLT3, PI3K, mTOR, JNK and p38 and we calculated the average IC50 of FLT3ITD-JMD patient-derived primary blasts for each drug. These results are reported as a bar graph in the new Fig. S5B and below (upper panel) and were compared with the apoptotic and proliferation rate measured in silico simulation of the FLT3ITD-JMD Boolean model. Drug sensitivity screening on primary FLT3ITD-JMD blasts revealed that inhibition of FLT3, PI3K and mTOR induces cell death at low drug concentrations in contrast with JNK and p38 inhibitors showing higher IC50 values. These observations are consistent with our simulation results of the FLT3ITD-JMD model. As expected, in silico inhibition of FLT3 greatly impacts apoptosis and proliferation. Additionally, in silico suppression of mTOR and to a lesser extent PI3K and p38 affect apoptosis and proliferation. Of note, JNK inhibition neither in silico nor in vitro seems to affect viability of FLT3ITD-JMD cells.

Author response image 5.

Altogether these publicly available datasets independently validate our models, strengthening the reliability and robustness of our approach.

We have now revised the main text (pg. 8; 9) and added a new Figure (Fig. S5) in the supplementary material; we collected the results of the analysis in TableS6.

(4) There are additional examples of insufficient experimental detail that preclude a fuller appreciation of the relevance of the work. For example, it is alluded that RNA-sequencing was performed on a subset of patients, but the entire methodological section detailing the RNA-seq amounts to just 3 lines! It is unclear which samples were selected for sequencing nor where the data has been deposited (or might be available for the community - there are resources for restricted/controlled access to deidentified genomics/transcriptomics data).

We apologize for the lack of description regarding the RNA sequencing of patient samples. We have now added details of this approach in the method section (pg. 24), clearly explained in text how we selected the patients for the analysis. Additionally, data has now been deposited in the GEO database (accession number: GSE247483).

The sentences we have rephrased are below:

“We analyzed the mutational and expression profiles of 262 genes (Table S7), relevant to hematological malignancies in a cohort of 14 FLT3-ITD positive de novo AML patients (Fig. 5A, panel a). Since, follow-up clinical data were available for 10 out of 14 patients (Fig. 5B, Table S9), we focused on this subset of patients. Briefly, the classification of these 10 patients according to their ITD localization (see Methods) was as follows: 8 patients with FLT3ITD-JMD, 4 with FLT3ITD-JMD+TKD, and 2 with FLT3ITD-TKD (Fig. 5A, panel b). The specific insertion sites of the ITD in the patient cohort are shown in Table S8.

Similarly, in the "combinatory treatment inference" methods, it states "...we computed the steady state of each cell line best model....." and "Then we inferred the activity of "apoptosis" and "proliferation" phenotypes", without explaining the details of how these were done. The outcomes of these methods are directly relevant to Fig 4, but with such sparse methodological detail, it is difficult to independently assess the validity of the presented data.

Overall, the theoretical nature of the work is hampered by real-world validation, and insufficient methodological details limit a fuller appreciation of the overall relevance of this work.

We thank the reviewer for the insightful feedback regarding the methodology in our paper.<br /> About ‘real-world validation’ we have extensively replied to this issue in point 3 (pg. 9-14 of this document). For what concerns the ‘insufficient methodological details’, we have made substantial improvements to enhance clarity and reproducibility, that encompass: (i) revisions in the main text and in the Materials and Methods section; (ii) detailed explanation of each step and decisions taken that can be accessed either as an extended Materials and Methods section (Supplementary material, pg. 14-19) and through our GitHub repository (https://github.com/SaccoPerfettoLab/FLT3-ITD_driven_AML_Boolean_models). We sincerely hope this addition addresses concerns and facilitates a more thorough and independent assessment of our work.

Reviewer #3 (Public Review):

Summary:

The paper "Unveiling the signaling network of FLT3-ITD AML improves drug sensitivity prediction" reports the combination of prior knowledge signaling networks, multiparametric cell-based data on the activation status of 14 crucial proteins emblematic of the cell state downstream of FLT3 obtained under a variety of perturbation conditions and Boolean logic modeling, to gain mechanistic insight into drug resistance in acute myeloid leukemia patients carrying the internal tandem duplication in the FLT3 receptor tyrosine kinase and predict drug combinations that may reverse pharmacoresistant phenotypes. Interestingly, the utility of the approach was validated in vitro, and also using mutational and expression data from 14 patients with FLT3-ITD positive acute myeloid leukemia to generate patient-specific Boolean models.

Strengths:

The model predictions were positively validated in vitro: it was predicted that the combined inhibition of JNK and FLT3, may reverse resistance to tyrosine kinase inhibitors, which was confirmed in an appropriate FLT3 cell model by comparing the effects on apoptosis and proliferation of a JNK inhibitor and midostaurin vs. midostaurin alone.

Whereas the study does have some complexity, readability is enhanced by the inclusion of a section that summarizes the study design, plus a summary Figure. Availability of data as supplementary material is also a high point.

We thank the reviewer for his/her constructive comments about our manuscript. We believe that our story has been significantly strengthened by the changes and new data we provided.

Weaknesses:

(1) Some aspects of the methodology are not properly described (for instance, no methodological description has been provided regarding the clustering procedure that led to Figs. 2C and 2D).

We apologize for the lack of proper description of the methodology. We have extensively revised the methods section and worked to improve the clarity. We have now added a description of the clustering procedures in the methods section (pg. 19) of new Fig. S2D., Fig. S2E.

It is not clear in the manuscript whether the patients gave their consent to the use of their data in this study, or the approval from an ethical committee. These are very important points that should be made explicit in the main text of the paper.

We thank the reviewer for this comment. We have now added the following sentence (pg. 24): “Peripheral blood (PB) samples from 14 AML patients were obtained upon patient’s informed consent.”

The authors claim that some of the predictions of their models were later confirmed in the follow-up of some of the 14 patients, but it is not crystal clear whether the models helped the physicians to make any decisions on tailored therapeutic interventions, or if this has been just a retrospective exercise and the predictions of the models coincide with (some of) the clinical observations in a rather limited group of patients. Since the paper presents this as additional validation of the models' ability to guide personalized treatment decisions, it would be very important to clarify this point and expand the presentation of the results (comparison of observations vs. model predictions).

As described in the introduction section, this study was inspired by an urgent clinical problem in AML research: patients carrying the ITD in the TKD domain of the FLT3 receptor display poor prognosis and do not respond to current therapy: Midostaurin (which on the other hand is effective in patients with the ITD in the JMD domain).

To fill this gap, we gathered a team of 18 participants, of which 7 have a clinical background and have expertise in the diagnosis, treatment and management of AML patients and 5 are experts in Boolean modeling. The scope of the project is the development of a computational approach to identify possible alternative solutions for FLT3ITD-TKD AML patients, generating future lines of investigations. Drug combinations are currently under investigation as a potential means of avoiding drug resistance and achieving more effective and durable treatment responses. However, it is impractical to test for potential synergistic properties among all available drugs using empirical experiments alone. With our approach, we developed models that recreated in silico the main differences in the signaling of sensitive and resistant cells to support the prioritization of novel therapies. Prompted by the reviewer suggestions, we have now extended the validation of our models, through the comparison with publicly available cell lines and patient-derived dataset. We have also confirmed our results by performing in vitro experiments in patient-derived primary blasts treated with midostaurin and/or JNK inhibitor. Importantly, we have already demonstrated that hitting cell cycle regulators in FLT3ITD-TKD cells can be an effective approach to kill resistant leukemia cells (Massacci et al., 2023; Pugliese et al., 2023). We are aware that changing the clinical practice and the therapies for patients require a proper clinical study which goes far beyond the scope of this manuscript.

However, we hope that our results can be translated soon from “bench-to-bed”. Importantly, we believe that our study can open lines of investigations aimed at the application of our approach to identify promising therapeutic strategies in other clinical settings.

Recommendations for the authors

The reviewers have highlighted significant issues regarding the inadequate level of evidence to support some of the conclusions, plus lack of an exhaustive methodological description that may jeopardize reproducibility.

We hope that the editor and the reviewers will appreciate the extensive revision we made and new data and analysis we provided to strengthen our story.

Reviewer #1 (Recommendations For The Authors):

(1) In Fig 2D the hierarchical tree is off-set in relation to the treatment symbols and names in the middle of the Figure. In addition, I do not see FLT3i combination with JNKi in the JMD cells (perhaps, a coloring error?).

We thank the reviewer for this observation. We have now revised the hierarchical tree, which is now in Figure S2D, we have aligned the tree with the symbols and names and corrected the colouring error for the sample FLT3i+JNKi in JMD cells.

(2) Midostaurin and PKC412 refer to the same drug and are used interchangeably in the manuscript. Using one name consistently would improve readability.

We have now improved the readability of the text and the Figures by choosing “Midostaurin” when we refer to the FLT3 inhibitor.

(3) It is not clear to me why the FLT3-ITD-JMD cells are not presented in Fig. 4B. Perhaps their values are 0? In that case, the readability would be improved by including a thin blue line representing zero values. Additionally, on p.8 the authors state "Interestingly, in the FLT3ITDTKD model, the combined inhibition of JNK and FLT3, exclusively, in silico restores the TKI sensitivity, as revealed by the evaluation of the apoptosis and proliferation levels (Fig. 4B-C)." but Fig. 4C shows no differential effects of JNK inhibition in sensitive versus resistant cells.

To address the reviewer's point, we’ve added a thin blue line representing the zero values of the FLT3ITD-JMD in the results of the simulations in Figure 4B. Regarding the Figure 4C, the reviewer is right in saying that there is no difference in terms of proliferation between sensitive and resistant cells upon JNKi and FLT3i co-inhibition. However, we can see lower proliferation levels in both cell lines as compared to the “untreated” condition. Indeed, the simulation suggests that by combining JNK and FLT3 inhibition we restore the resistant phenotype lowering the proliferation rate of the resistant cells to the TKI-sensitive levels.

Reviewer #2 (Recommendations For The Authors):

I have addressed a number of concerns in the public review. Much better effort needs to be made to provide sufficient methodological detail (to permit independent validation by a sufficiently capable and motivated party) and explain the rationale of important parameter selections. Furthermore, I urge the authors to take advantage of the plethora of publicly available real-world data to validate their predicted outcomes.

We are grateful to the reviewer for the careful revisions. All the aspects raised have been discussed in the specific sections of the public review. In summary, we have provided more methodological details, by revising the text, the methods session, by adding a new step-by-step description of the modelling strategy, the parameters and the criteria adopted in each phase (supplementary methods) and by referring to the entire code developed. Prompted by the reviewer suggestions, we have performed a novel and extensive comparison of our model with three different publicly available datasets. This analysis significantly strengthens our story, and a new supplementary Figure (Fig. S5) summarizes our findings (pg. 9-14 of this document).

Reviewer #3 (Recommendations For The Authors):

(1) At first sight, the distribution of the data points in the PCA space does not really seem to speak of nice clustering. Have the authors computed any clustering validation metric to assess if their clustering strategy is adequate and how informative the results are? Further analysis of this point of the article is precluded by the absence of a clear methodological description.

Here we have used the PCA analysis to obtain a global view of our complex multiparametric data. We have now worked on the PCA to improve its readability. As shown in the new Figure 2D, PCA analysis showed that the activity level of sentinel proteins stratifies cells according to FLT3 activation status (component 1: presence vs absence of FLT3i) and cytokine stimulation (component 2: IGF1 vs TNF⍺). We have now added new experimental details on this part in the methods section (pg. 19) and we deposited the code used for the clustering strategy on the GitHub repository (https://github.com/SaccoPerfettoLab/FLT3ITD_driven_AML_Boolean_models).

(2) Whereas scientists and medical professionals who work in the field of oncology may be familiar with some of the abbreviations used here, it would be good for improved readability by a more general audience to make sure that all the abbreviations (e.g., TKI) are properly defined the first time that they appear in the text.

We thank the reviewer for this observation. To improve the readability of the text, we properly defined all the abbreviations in their first appearance, and we added the “Abbreviation” paragraph at page 15 of the manuscript to summarize them all.

(3) How were the concentrations of the combined treatments chosen in the cell assays used as validation?

We thank the reviewer for giving us the chance to clarify this point. We implemented the Methods with additional information about the treatments used in the validations. We detailed the SP600125 IC50 evaluation and usage in our cell lines (pg.22): IC50 values are approximately 1.5 µM in FLT3-ITD mutant cell lines; the SP600125 treatment affects cell viability, reaching a plateau phase of cell death and at about 2 µM. I used the minimal dose of SP600125 (10µM) to properly inhibit JNK. (Kim et al., 2010; Moon et al., 2009).

We also specified (pg.22) that the concentration of Midostaurin was chosen based on the previously published work (Massacci et al., 2022): FLT3 ITD-TKD cells treated with Midostaurin 100nM show lower apoptotic rate and higher cell viability compared to FLT3 ITD-JMD cells.

The concentration of SB203580 and UO126 was chosen based on previous data available in the lab and set up experiments (pg.22).

(4) The authors say that "we were able to derive patient-specific signaling features and enable the identification of potential tailored treatments restoring TKI resistance" and that "our predictions were confirmed by follow-up clinical data for some patients". However, the results section on this part of the manuscript is rather scarce (the main text should be much more descriptive about the results summarized in Fig. 5, which are not self-explanatory).

We thank the reviewer for this observation. We have now expanded the text to provide a more comprehensive description of the results about personalized Boolean model generation and usage and the content presented in Fig. 5 (pg.10-12).

(5) I do not really agree with the final conclusion about this paper being "the proof of concept that our personalized informatics approach described here is clinically valid and will enable us to propose novel patient-centered targeted drug solutions". First, the clinical data used here belongs to a rather low number of patients. Second, as mentioned before, it is not clear if the models have been used to make any prospective decision or if this conclusion is drawn from an in vitro assay plus a retrospective analysis on a limited number of patients. Moreover, a description of the results and the discussion of the part of the manuscript dealing with patientspecific models is rather scarce, and it is difficult to see how the authors support their conclusions. Also, the statement " In principle, the generalization of our strategy will enable to obtain a systemic perspective of signaling rewiring in different cancer types, driving novel personalized approaches" may be a bit overoptimistic if one considers that so far, the approach has only been applied to a single type of drug-resistant cancer.

We thank the reviewer for this comment. We agree with the referees that the clinical data we used belongs to a rather low number of patients. However, during the revision we have extensively worked to support the clinical relevance of our models and our discoveries. Specifically, we have compared our Boolean logic models with two different publicly available datasets on phosphoproteomics and drug sensitivity of FLT3ITD-JMD and FLT3ITD-TKD cell lines and blasts (FigS5 and answer to reviewer 2, point 3). Importantly, these datasets independently validated our models, highlighting that our approach has a translational value. Additionally, we have performed novel experiments by measuring the apoptotic rate of patient-derived primary blasts upon pharmacological suppression of JNK (Fig. 4H, pg. 10 of main text). Our data highlights that our approach has the potential to suggest novel effective treatments.

That said, we have now revised the discussion to avoid overstatements.

References

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Author Response

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

Reviewer #1 (Recommendations For The Authors):

Many of my specific issues have been addressed in the revision. However, the data shown in Reviewer Fig. 1 and 2 is not sufficiently described to assess it's reliability and these new data do not appear to have been integrated into the paper. A response that more clearly states how the manuscript has been revised to address the comments is necessary.

We appreciate the opportunity to respond to your updated comments on our manuscript. We carefully considered the feedback and made changes to address the specific issues raised.

In response to your question of insufficient description of the data shown in Reviewer Fig. 1 and 2, we would like to confirm that we have taken this feedback seriously. Supplementary data, including the information provided in Reviewer Figures 1 and 2, have been fully described and integrated into the body of the manuscript according to your request. We ensured that the reliability and significance of new data were clearly presented to enhance the overall synthesis of the manuscript.

We are grateful to your valuable feedback, which undoubtedly contributed to the refinement of our manuscript. We hope that the revised version meets the standards of the journal and look forward to the opportunity for further deliberation.

Reviewer #2 (Recommendations For The Authors):

Additional feedback from the reviewer:

"I think the authors have been responsive to my previous comments. However, I cannot find this new data in the main text but rather only in the response to reviewers. New data should be incorporated into the main text not the supplement as the controls are important to consider alongside the treatment groups. Lastly, while the authors include BODIPY in their approaches, their results are not quantitative. My suggestion was to include this data in a quantitative manner not just the images. Lastly, I am still somewhat puzzled about the connection with GABA. The rationale for its selection other than it was significantly changed is not strong."

Thank you for providing us with the latest feedback. We appreciate the opportunity to address the specific concerns raised and provide a detailed response to each point.

(1) Incorporation of New Data into the Main Text:

We acknowledge the reviewer's comment regarding the incorporation of new data into the main text rather than solely in the response to reviewers. In response to this feedback, we have diligently revised the manuscript to ensure that the new data, including controls, is now seamlessly integrated into the main body of the text. This modification allows for a more comprehensive and contextual presentation of the data, as recommended by the reviewer.

(2) Quantitative Presentation of BODIPY Results:

We understand the importance of presenting quantitative data for the BODIPY results, and we appreciate the reviewer's suggestion to include this information in a quantitative manner, not just as images. In line with this valuable feedback, we have revised the relevant sections to incorporate quantitative data alongside the images, providing a more robust and comprehensive presentation of the results.

(3) Rationale for the Selection of GABA:

In the present study, in order to elucidate the molecular mechanisms through which pathway participates metformin-treated IR injury, we analysed gene expression profiles of each group mice, showing that similar mRNA changes are mainly concentrated in the three top pathways: lipid metabolism, carbohydrate metabolism, and amino acid metabolism. Given the close relevance between lipid metabolism and ferroptosis, and the fact of carbohydrate metabolism is a primary way to metabolize amino acids, 22 species of amino acid were detected in liver tissues using HPLC-MS/MS for further identification of key metabolites involved in the role of metformin against HIRI-induced ferroptosis. It was found that only GABA level is significantly increased by metformin treatment and FMT treatment, further verifying by the data of ELISA detection. Consequently, we identified GABA was the main metabolism of metformin protecting from HIRI and focus on the source of GABA generation.

We would like to express our gratitude to your thorough evaluation and constructive feedback, which has undoubtedly contributed to the improvement of our manuscript.

Author Response

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

eLife assessment

This is an important study that provides new insights into the development and function of medullary thymus epithelial cells (mTEC). The authors provide compelling evidence to support their claims as to the differentiation and lineage outcomes of CCL21+ mTEC progenitors, which further our understanding of how central tolerance of T cells is enforced within the thymus.

Public Reviews:

Reviewer #1 (Public Review):

The work by Ohigashi and colleagues addresses the developmental and lineage relationship of a newly characterized thymus epithelial cell (TEC) progenitor subset. The authors take advantage of an elegant and powerful set of experimental approaches to demonstrate that CCL21-expressing TECs appear early in thymus organogenesis and that these cells, which are centrally located, go on to give rise to medullary (m)TECs. What makes the findings intriguing is that these CCL21-expressing mTECs are a distinct subset, which do not express RANK or AIRE, and transcriptomic and lineage tracing approaches point to these cells as potential mTEC progenitor-like cells. Of note, using in vitro and in vivo precursor-product cell transfer experiments, the authors show that this subset has a developmental potential to give rise to AIRE+ self-antigen-displaying mTECs, revealing that CCL21-expressing mTECs can give rise to distinct mTEC subsets. This functional duality provides an attractive rationale for the necessary function of mTECs, which is to attract CCR7+ thymocytes that have just undergone positive selection in the thymus cortex to enter the medulla to undergo tolerance-induction against self-antigen-displaying mTECs. Overall, the work is well supported and offers new insights into the diverse functions of the medullary compartment, and how two distinct subsets of mTECs can achieve it.

Reviewer #2 (Public Review):

Summary:

The authors set out to discover a developmental pathway leading to functionally diverse mTEC subsets. They show that Ccl21 is expressed early during thymus ontogeny in the medullary area. Fate-mapping gives evidence for the Ccl21 positive history of Aire positive mTECs as well as of thymic tuft cells and postnatally of a certain percentage of cTECs. Therefore, the differentiation potential of Ccl21+ TECs is tested in reaggregate thymus experiments - using embryonic or postnatal Ccl21+ TECs. From these experiments, the authors conclude that at least embryonic mTECs in large part pass through a Ccl21 positive stage prior to differentiation towards an Aire expressing or tuft cell stage.

The authors are using Ccl21a as a marker for a bipotent progenitor that is detectable in the embryonic thymus and is still present at the adult stage mainly giving rise to mTECs. The choice of this marker gene is very interesting since Ccl21 expression can directly be linked to an important aspect in thymus biology: the expression of Ccl21 by cells in the thymic medulla allows trafficking of T cells into the medulla in order to undergo T cell selection.

Making use of the Ccl21 detection, the authors can nicely show that cells actively expressing Ccl21 are localized throughout the medulla at an embryonic stage but also in adult thymus tissue. This suggests, that this progenitor is not accumulating at a specific area inside the medulla. This is a new finding.

Moreover, the finding that a Ccl21+ progenitor population plays a functional role in thymocyte trafficking towards the medulla has not been described. Thus, Ccl21 expression may be used to localize a late bipotent progenitor in the thymic lobes.

In addition, in Fig.8, the authors provide evidence that these progenitor cells have the potential to self-maintain as well as to differentiate in reaggregate experiments at E17 (not at 4 weeks of age). The first point is of great interest and importance since these cells in theory can be of therapeutic use.

Overall assessment:

The authors highlight a developmental pathway starting from a Ccl21-expressing TEC progenitor that contributes to a functionally diverse mTEC repertoire. This is a welcome addition to current knowledge of TEC differentiation.

Reviewer #3 (Public Review):

In this manuscript, the authors define the developmental trajectory resulting in a diverse mTEC compartment. Using a variety of approaches, including a novel CCL21-fate mapping model, data is presented to argue that embryonic CCL21-expressing thymocyte attracting mTECs naturally convert to into self-antigen displaying mTEC subsets, including Aire+ mTECs and thymic tuft cells. Perhaps somewhat surprisingly, a large fraction of cTECs were also marked for having expressed CCL21, suggesting that there exists some conversion of mTEC (progenitors) into cTEC, a developmentally interesting observation that could be followed up later. Overall, the experimental setup, writing, and conclusions, are all outstanding.

Provisional author response

We thank the editors and the reviewers for their supportive comments on our manuscript. We will revise the manuscript according to their helpful recommendations.

Author response to recommendations

We thank the editors and the reviewers for their supportive comments on our manuscript. We also thank the three reviewers for their helpful recommendations. We have revised the manuscript accordingly, as detailed below.

Reviewer #1 (Recommendations For The Authors):

There are several unanswered questions, which the authors themselves acknowledge, a principal one being whether CCL21+ mTECs represent a progenitor for yet another distinct subset of cortical (c)TECs, or whether they represent an intermediary or unique population of mTECs derived from a bipotent (cTEC/mTEC) progenitor. These questions will need to be addressed in future work as they go beyond the initial characterization of this intriguing mTEC subset.

Indeed, our findings reported in this manuscript have stimulated many interesting questions, including those pointed out by the reviewer. We would like to address them one by one in our future work.

The presence of GFP+ cTECs, which are lineage-traced as having expressed CCL21, begs the question as to whether these cells are generated as a consequence of later steps in mTEC differentiation or derived from earlier bipotent cells, which again the authors point out. The authors could discuss this further or perhaps experimentally address this by using a model system whereby mTEC differentiation is absent or halted (e.g., Relb ko, or TCRa/TCRd ko) and test whether GFP+ cTECs are still present.

According to the suggestion, we have revised the manuscript by adding a statement that it is interesting to examine whether GFP+ cTEC development in Ccl21a-Cre x CAG-loxP-EGFP mice is mediated through RelB-dependent mTEC developmental progression or developing thymocyte-dependent mTEC-nurturing ‘crosstalk’ signals.

Reviewer #2 (Recommendations For The Authors):

Even though the manuscript highlights the functional aspect of a postnatal bipotent progenitor, there are several aspects that need further discussion.

(1) The title is somewhat misleading since the identified TEC subset can not only be detected in embryonic, but also in postnatal thymus. Only the RTOC experiments indicate a higher developmental potential of TECs isolated from embryos, but this might as well be due to experimental difficulties as discussed in the text. Furthermore, Ccl21+ TECs are shown to differentiate postnatally into mTECs and cTECs, therefore this subset presumably belongs to a bipotent progenitor population described earlier (their ref. 22, 39).

We are fully aware of previous studies showing that mTEC progenitors include cells that transcribe Ccl21a, and have cited them in the manuscript. The manuscript title describes our finding that thymocyte-attracting CCL21-expressing functional mTECs isolated from embryonic thymus show the capability to give rise to self-antigen-displaying mTECs. We thank the reviewer for further pointing out the possibility that postnatal CCLl21+ TECs include cells that retain the capability to differentiate into mTECs and cTECs.

(2) In the introduction the authors claim that the "developmental progression of the self-antigen-displaying mTEC subset occurs in a single stream as mTEClow progenitors -> mTEChigh Aire-expressing cells -> mTEClow mimetic cells." line 79. So far it only could be shown that some mimetic cell types undergo an Aire+ stage; whether this is true for all mimetic cells remains to be shown. Therefore, this statement should be toned down.

Following the suggestion, this sentence has been toned down in the revised manuscript.

(3) In line 86, the reference to another paper, describing Ccl21a expression in a postnatal mTEC biased progenitor should be added: Nusser et al. Nature. 2022 PMID: 35614226, in which the developmental potential of the Ccl21 positive so-called postnatal progenitor is analysed by barcoding and results give evidence for differentiation into mature mTECs (see lines 94-96).

As suggested, the Introduction of the revised manuscript now cites Nusser, et al. study showing that postnatal mTEC-biased progenitors include cells that transcribe Ccl21a.

(4) Have a look at Extended Data Figure 2b of PMID: 35614226, wherein the population-specific gene expression pattern of the progenitor population at different time points is depicted. Ccl21a belongs to a group of genes, which identifies the postnatal progenitor, and indicates that its functionality and/or developmental potential is age-dependent. Therefore, it would be important to specify the age of the analysed mice throughout the text of the results part instead of describing them as "postnatal" only.

As recommended, mouse age has been added to the revised manuscript and figures.

(5) Line 113: "embryonic" needs to be replaced since the results of Fig. 1 are referring to 5-week-old mice.

The manuscript has been revised per the reviewer’s suggestion.

(6) Referring to Fig. 3g, line 173: It is interesting to see that, at 3 weeks of age, 95% of mTECs have a Ccl21-history but only approx. 70% of cTECs. Therefore, the earliest progenitor giving rise to the first cTECs might still be productive and feed into the cTEC lineage. This reporter would allow for the analysis of progenitor activity over time. The same could be done for mTECs since at E15 the tdTomato signal is still low compared to the assigned medullary area in Fig. 2c in order to detect when the Ccl21-expressing progenitor becomes the main source of mTECs. The finding in Fig. 4e (line196) also argues for the timed replacement of cTECs by a progenitor which locates to the medulla, thus, leading to a decline in Ccl21-history signal towards the subcapsular region at 2 weeks of age. This should be better explained/discussed.

We appreciate the work of Nusser, et al. showing that postnatal mTEC-biased, but not embryonic cTEC-biased, TEC progenitors include cells that transcribe a detectable amount of Ccl21a (cited in the Introduction as ref. 23). It is important to clarify whether and how those postnatal TEC progenitors (23) overlap with the embryonic and postnatal CCL21-protein-expressing mTECs reported in this study. It is also interesting to shed light on how Ccl21a+ progenitors contribute to cTECs and mTECs over the ontogeny and whether the enrichment of Ccl21a+ progenitor-derived cTECs in the perimedullary area reflects a temporal replacement of cTECs derived from Ccl21a+ progenitors localized in the medulla. We would like to clarify these issues in our future work. The revised manuscript includes a discussion of these issues.

(7) Line 304 and 355: Note that the "unstable" age-dependent gene expression profiles were already reported in Nusser et al. Nature. 2022. Not only Ccl21 expression, but other progenitor-specific genes also change their expression levels with age. The entirety of changes in gene expression during aging likely impacts the developmental potential of progenitor populations. These changes might be reflected in the negative results of the RTOC experiment using TECs of 4-week-old mice. The manuscript would benefit from a discussion in light of this "unstable" age-dependent gene expression.

It is interesting to point out that the age-dependent difference in gene expression profiles, which was reported in TEC progenitors by Nusser, et al. (23), is also detected in CCL21-expressing mTECs in this study. Similarly to the recommendation no. 6 by reviewer 2, and as described in the revised manuscript, it is interesting to clarify whether and how embryonic and postnatal CCL21-expressing mTECs overlap with the previously reported TEC progenitors.

(8) Line 321: as discussed above, the exact time point should be added to the text since the proportion of cTECs derived from a Ccl21+ progenitor is associated with a certain time point, "2/3 of cTECs" refers to 3 weeks of age.

The manuscript has been revised following the reviewer’s suggestion.

Reviewer #3 (Recommendations For The Authors):

The one question I have, which may be more of a curiosity of this reviewer than a requirement for the manuscript, is whether thymocytes themselves are required for the conversion/maturation of attracting TECs to mTECs? For example, in CD3e-/- (or Rag-/-) mice, are mTECs arrested at the thymocyte attracting stage, or is the conversion process 'pre-programed'? In the same vein, do cTECs (or the immature cTECs) maintain CCL21 expression in the absence of mature thymocytes? These are not critical studies but are fairly straightforward (effort- and time-wise) that would aid in placing this process in the overall scope of thymus development.

We previously showed that Aire+ mTECs are detectable in the thymus of RAG2-deficient mice, in which thymocyte development is arrested beyond the CD4/CD8 double-negative 3 stage (Hikosaka, et al. 2006; PMID: 18799150). In another work, we also showed that Aire+ mTECs and CCL21+ mTECs are detectable in the thymus of TCR-alpha-KO mice, which lack mature CD4/CD8 single-positive TCR-alpha/beta-expressing thymocytes (Lkhagvasuren, et al. 2013; PMID: 23585674). These results indicate that thymocyte maturation beyond the Rag-dependent stage is not essential for the development of Aire+ mTECs. Nonetheless, we agree with the reviewer pointing out that it is important to clarify how developing thymocytes contribute to the growth and differentiation of diverse TEC subpopulations, including GFP+ cTEC development in Ccl21a-Cre x CAG-loxP-EGFP mice. The revised manuscript includes a discussion of these issues.

Author Response

We thank eLife Senior Editor and reviewers for the comprehensive evaluation and constructive comment on our manuscript. We are grateful that all 3 reviewers recognize the value of the large pharmacological and proteomics screen of 51 cancer cell lines in relation to vitamin C IC50 values. As reviewer 1 points out, our findings are of interest as high dose vitamin C is in clinical trials. Most importantly, we show that all 51 cell lines tested can be killed at a dose range that is achievable by intravenous administration in the clinic. These pharmacological findings underscore high-dose vitamin C as a potent anti-cancer agent. Moreover, we provide an elaborate description of functional terms associated with the vitamin C IC50 values in the different cell panels (Figs 1-5) and the common denominators across panels (Figs 6, 7 and 8), thereby enhancing our biological insights of sensitivity to vitamin C treatment. This study indeed is of descriptive nature and our large scale pharmacological and proteomics scale dataset should be seen as a resource for further research. The raw and processed data will be available in the ProteomeXchange repository (accession number and reviewer password were provided before) and the resubmission will include all processed proteome and phosphoproteome data as a supplementary file.

It is beyond the scope of our study to do mechanistic studies with knock-downs to see if we can further sensitize cancer cell lines that are less sensitive. We do not call these cell lines resistant as cell growth can be inhibited at a clinically achievable dose.

In our detailed rebuttal we will follow up on the suggestion of reviewer 1 to put our data also in the context of NCI-60 growth inhibition data for other cytotoxic agents. This will expand our comparative analysis to cisplatin in the lung cancer panel (Fig 5A) where we show that vitamin C IC50 values and cisplatin IC50 values are not one-on-one correlated as one of the most cisplatin resistant NSCLC cell lines in our panel was very sensitive to high dose vitamin C. Furthermore, we will clarify method details and annotate mutational status in our panels and explore potential genomic associations to high-dose vitamin C sensitivity as presented in previous studies (e.g. mutant BRAF and/or KRAS tumors, https://doi.org/10.1126/science.aaa5004).

Finally, we will critically read the manuscript and add references where needed.

Author Response

Reviewer #1 (Public Review):

Summary:

Heer and Sheffield used 2 photon imaging to dissect the functional contributions of convergent dopamine and noradrenaline inputs to the dorsal hippocampus CA1 in head-restrained mice running down a virtual linear path. Mice were trained to collect water rewards at the end of the track and on test days, calcium activity was recorded from dopamine (DA) axons originating in the ventral tegmental area (VTA, n=7) and noradrenaline axons from the locus coeruleus (LC, n=87) under several conditions. When mice ran laps in a familiar environment, VTA DA axons exhibited ramping activity along the track that correlated with distance to reward and velocity to some extent, while LC input activity remained constant across the track, but correlated invariantly with velocity and time to motion onset. A subset of recordings taken when the reward was removed showed diminished ramping activity in VTA DA axons, but no changes in the LC axons, confirming that DA axon activity is locked to reward availability. When mice were subsequently introduced to a new environment, the ramping to reward activity in the DA axons disappeared, while LC axons showed a dramatic increase in activity lasting 90 s (6 laps) following the environment switch. In the final analysis, the authors sought to disentangle LC axon activity induced by novelty vs. behavioral changes induced by novelty by removing periods in which animals were immobile and established that the activity observed in the first 2 laps reflected novelty-induced signal in LC axons.

Strengths:

The results presented in this manuscript provide insights into the specific contributions of catecholaminergic input to the dorsal hippocampus CA1 during spatial navigation in a rewarded virtual environment, offering a detailed analysis of the resolution of single axons. The data analysis is thorough and possible confounding variables and data interpretation are carefully considered.

Weaknesses:

Aspects of the methodology, data analysis, and interpretation diminish the overall significance of the findings, as detailed below.

The LC axonal recordings are well-powered, but the DA axonal recordings are severely underpowered, with recordings taken from a mere 7 axons (compared to 87 LC axons). Additionally, 2 different calcium indicators with differential kinetics and sensitivity to calcium changes (GCaMP6S and GCaMP7b) were used (n=3, n=4 respectively) and the data pooled. This makes it very challenging to draw any valid conclusions from the data, particularly in the novelty experiment. The surprising lack of novelty-induced DA axon activity may be a false negative. Indeed, at least 1 axon (axon 2) appears to be showing a novelty-induced rise in activity in Figure 3C. Changes in activity in 4/7 axons are also referred to as a 'majority' occurrence in the manuscript, which again is not an accurate representation of the observed data.

The reviewer points out a weakness in the analysis of VTA axons in our dataset. The relatively low n (currently 7) comes from the fact that VTA axons in the CA1 region of the hippocampus are very sparse and very difficult to record from (due to their sparsity and the low level of baseline fluorescence inherent in long range axon segments). This is the reason they have not been recorded from in any other lab outside of our lab. LC axons, on the other hand, are more abundant in CA1. In the paper when comparing VTA versus LC axons we deal with the mismatch in n by downsampling the LC axons to match the VTA axons and repeated this 1000 times to create a distribution. However, because the VTA axon n is relatively low, it is possible that we have not sampled the VTA axon population sufficiently and therefore have a biased population in our dataset. The issue is that it takes months for the baseline expression of GCaMP to reach sufficient levels to be able to record from VTA axons, and it is typical to find only a single axon in a FOV per animal. There are additional reasons why mice and/or axon recordings do not reach criteria and cannot be included in the dataset (these exclusion criteria are reported in the Methods section). For instance, out of the 54 DAT-Cre mice injected, images were never conducted in 36 for lack of expression or because mice failed to reach behavioral criteria. Another 11 mice were excluded for heat bubbles that developed during imaging, z-drift of the FOV, or bleaching of the GCaMP signal.

However, we do have n=2 additional VTA axon recordings that we will add to the dataset to bring the n up from 7 to 9. We plan on re-analyzing the data with n=9 VTA axons and making comparisons to down-sampled LC axons as described above. This boost in n will increase the power of our VTA axon analysis. To more formally test whether this is sufficient for statistical tests, we plan to utilize the G*power power-analysis tool to compute statistical power for each of the different tests we use. We will report this in the next version of the paper. However, the n=2 additional axons were nor recorded in the novel environment, so the next version will remain at n=7 for the novel environment analysis. We agree with the reviewer that the lack of the novelty induced DA axon activity may be a false negative, and so we will adjust the description of our results and discussion accordingly.

During the data collection of VTA axon activity we tried two variants of GCaMP: 6s and 7b, to see if one would increase the success rate of finding and recording from VTA axons. Given the long time-course of these experiments and the low yield in success, we pooled the GCaMP variants together to increase statistical power. Because the 2 additional VTA DA axons that were recorded from expressed GCaMP6s, the next version of the paper will have n=5 GCaMP6s, and n=4 GCaMP7b VTA DA axons, which will allow us to compare the activity of the two sensors in the familiar environment. The reviewer correctly pointed out that the sensors themselves could confound our results, and so they should not be pooled unless we can show they do not produce different signals in the axons. We will make this comparison and report the findings in the next version of the paper. If we find no significant differences, we will pool the data. If differences are detected, we will keep these axons separate for subsequent analysis and comparisons to LC axons.

The authors conducted analysis on recording data exclusively from periods of running in the novelty experiment to isolate the effects of novelty from novelty-induced changes in behavior. However, if the goal is to distinguish between changes in locus coeruleus (LC) axon activity induced by novelty and those induced by motion, analyzing LC axon activity during periods of immobility would enhance the robustness of the results.

This is indeed true, and this suggested analysis could further support our conclusions regarding the LC novelty signal. For the next version of the paper, we will use the periods of immobility to analyze and isolate any novelty induced activity in LC axons. However, following exposure to the novel environment, mice spend much less time immobile, therefore there may not be sufficient periods of immobility close in time to the exposure to the novel environment (which is when the novelty signal occurs). We plan to analyze mouse behavior during the early exposure to the novel environment for immobility and check whether we have enough of this behavior to perform the suggested analysis.

The authors attribute the ramping activity of the DA axons to the encoding of the animals' position relative to reward. However, given the extensive data implicating the dorsal CA1 in timing, and the remarkable periodicity of the behavior, the fact that DA axons could be signalling temporal information should be considered.

This is a very good point. We agree that the VTA DA axons could be signaling temporal information, as we have previously shown that these axons also exhibit ramping activity when you average their activity by time to reward (Krishnan et. al., 2022). We will conduct this analysis on this dataset. We have not, however, conducted any experiments designed to separate out time from distance, such as the experiments conducted in Kim et. al., 2020. Therefore, we cannot determine whether this is due to proximity in space to reward or time to reward. We will clarify in our text that by proximity, we mean either place or time, and cannot conclude which feature of the experience drives the VTA axon signal.

Krishnan, L.S., Heer, C., Cherian, C., Sheffield, M.E. Reward expectation extinction restructures and degrades CA1 spatial maps through loss of a dopaminergic reward proximity signal. Nat Commun 13, 6662 (2022).

Kim, HyungGoo R., Athar N. Malik, John G. Mikhael, Pol Bech, Iku Tsutsui-Kimura, Fangmiao Sun, Yajun Zhang, et al. A Unified Framework for Dopamine Signals across Timescales. Cell 183, no. 6 (2020).

The authors should explain and justify the use of a longer linear track (3m, as opposed to 2m in the DAT-cre mice) in the LC axon recording experiments.

LC axon activity was recorded on a 3m track to match the track length from an experiment we recently published (Dong et al., 2021) in which mice were exposed to a novel 3m track while populations of CA1 pyramidal cells were recorded. In that paper we described the time course of place field formation on the novel track. We wanted to test if LC axons signaled novelty (as we hypothesized) and whether the time course of LC axon activity matched the time course of place field formation. We briefly discuss this in the Discussion section of this paper and hypothesize that LC axons in CA1 could open a window of plasticity in which new place fields can form.

VTA axons were recorded on a 2m track (same VR tracks as LC axons were recorded on) to match another recent paper from our lab in which reward expectation was manipulated (Krishnan et al, 2022). In that study CA1 populations of pyramidal cells were recorded during the reward expectation experiment. To match the experience during recordings of VTA axons in CA1 to test how reward expectation may influence axon signaling along the track, we also used a 2m track. The idea was to check how VTA dopaminergic inputs to CA1 may influence CA1 population dynamics along the track.

Although the tracks were identical for LC and VTA recordings for both the familiar and novel tracks in terms of visual cues and design, the track lengths are different (simply modulated by gain control of the rotary encoder). To account for this we normalized the lengths for our comparison analysis. This normalization allows for a direct comparison of the patterns of activity across the two types of axons, controlling for the potential confound introduced by the different track lengths. By adjusting the data to a common scale, we could assess the relative changes in activity levels at matched spatial bins, ensuring that any observed differences or similarities are due to the intrinsic properties of the axons rather than differences in track lengths. However, the different lengths do make the animal’s experience slightly different. This is somewhat offset by the observations in our study that none of the LC or VTA axon signals would be expected to be majorly influenced by variations in track length. For instance, LC axons are associated with velocity and a pre-motion initiation signal, neither of which would be influenced by track length. VTA axons are also associated with velocity, which would not influence a direct comparison to LC axon velocity signals as mice reach maximal velocity very rapidly along the track. VTA axons do ramp up in activity as they approach the reward zone, and this signal could be modulated by track length (or maybe not if the signal is encoding time to reward rather than distance). However, LC axons show no ramping to reward signals, so a comparison across axons recorded on different track lengths for this analysis is justified.

However, to add rigor to comparisons of axon dynamics recorded along 2m and 3m tracks, we plan to plot axon activity of both sets of axons by time to reward, and actual (un-normalized) distance from reward.

Krishnan, L.S., Heer, C., Cherian, C., Sheffield, M.E. Reward expectation extinction restructures and degrades CA1 spatial maps through loss of a dopaminergic reward proximity signal. Nat Commun 13, 6662 (2022).

Dong, C., Madar, A. D. & Sheffield, M.E. Distinct place cell dynamics in CA1 and CA3 encode experience in new environments. Nat Commun 12, 2977 (2021).

Reviewer #2 (Public Review):

Summary:

The authors used 2-photon Ca2+-imaging to study the activity of ventral tegmental area (VTA) and locus coeruleus (LC) axons in the CA1 region of the dorsal hippocampus in head-fixed male mice moving on linear paths in virtual reality (VR) environments.

The main findings were as follows:

• In a familiar environment, the activity of both VTA axons and LC axons increased with the mice's running speed on the Styrofoam wheel, with which they could move along a linear track through a VR environment.
• VTA, but not LC, axons showed marked reward position-related activity, showing a ramping-up of activity when mice approached a learned reward position.
• In contrast, the activity of LC axons ramped up before the initiation of movement on the Styrofoam wheel.
• In addition, exposure to a novel VR environment increased LC axon activity, but not VTA axon activity.

Overall, the study shows that the activity of catecholaminergic axons from VTA and LC to dorsal hippocampal CA1 can partly reflect distinct environmental, behavioral, and cognitive factors. Whereas both VTA and LC activity reflected running speed, VTA, but not LC axon activity reflected the approach of a learned reward, and LC, but not VTA, axon activity reflected initiation of running and novelty of the VR environment.

I have no specific expertise with respect to 2-photon imaging, so cannot evaluate the validity of the specific methods used to collect and analyse 2-photon calcium imaging data of axonal activity.

Strengths:

(1) Using a state-of-the-art approach to record separately the activity of VTA and LC axons with high temporal resolution in awake mice moving through virtual environments, the authors provide convincing evidence that the activity of VTA and LC axons projecting to dorsal CA1 reflect partly distinct environmental, behavioral and cognitive factors.

(2) The study will help a) to interpret previous findings on how hippocampal dopamine and norepinephrine or selective manipulations of hippocampal LC or VTA inputs modulate behavior and b) to generate specific hypotheses on the impact of selective manipulations of hippocampal LC or VTA inputs on behavior.

Weaknesses:

(1)The findings are correlational and do not allow strong conclusions on how VTA or LC inputs to dorsal CA1 affect cognition and behavior. However, as indicated above under Strengths, the findings will aid the interpretation of previous findings and help to generate new hypotheses as to how VTA or LC inputs to dorsal CA1 affect distinct cognitive and behavioral functions.

(2) Some aspects of the methodology would benefit from clarification.<br /> First, to help others to better scrutinize, evaluate, and potentially to reproduce the research, the authors may wish to check if their reporting follows the ARRIVE (Animal Research: Reporting of In Vivo Experiments) guidelines for the full and transparent reporting of research involving animals (https://arriveguidelines.org/). For example, I think it would be important to include a sample size justification (e.g., based on previous studies, considerations of statistical power, practical considerations, or a combination of these factors). The authors should also include the provenance of the mice. Moreover, although I am not an expert in 2-photon imaging, I think it would be useful to provide a clearer description of exclusion criteria for imaging data.

We thank the reviewer for helping us formalize the scientific rigor of our study. There are ten ARRIVE Guidelines and we have addressed most of them in our study already. However, there is an opportunity to add detail. We have listed below all ten points and how we have or will address each one.

(1) Experimental design - we go into great depth explaining the experimental set-up, how we used the autofluorescent blebs as imaging controls, how we controlled for different sample sizes between the two populations, and the statistical tests used for comparisons. We also carefully accounted for animal behavior when quantifying and describing axon dynamics both in the familiar and novel environments.

(2)Sample size - We state both the number of ROIs and mice for each analysis. Wherever we state how many axons had a certain kind of activity, we will also state the number of mice we saw this activity in. For the next version of the paper, we plan to conduct a power analysis using G*power to assess the power of our sample sizes for statistical analysis.

(3) Inclusion/exclusion criteria - Out of the 36 NET-Cre mice injected, 15 were never recorded for either failing to reach behavioral criteria, or a lack of visible expression in axons. Out of the 54 DAT-Cre mice injected, images were never conducted in 36 for lack of expression or failing to reach behavioral criteria. Out of the remaining 21 NET-CRE, 5 were excluded for heat bubbles, z-drift, or bleaching, while 11 DAT-Cre were excluded for the same reasons. This was determined by visually assessing imaging sessions, followed by using the registration metrics output by suite2p. This registration metric conducted a PCA on the motion-corrected ROIs and plotted the first PC. If the PC drifted largely, to the point where no activity was apparent, the video was excluded from analysis.

(4) Randomization - Already included in the paper is a description of random down sampling of LC axons to make statistical comparisons with VTA axons. LC axons were selected pseudo-randomly (only one axon per imaging session) to match VTA sampling statistics. This randomization was repeated 1000 times and comparisons were made against this random distribution.

(5) Blinding-masking - no blinding/masking was conducted as no treatments were given that would require this. We will include this statement in the next version.

(6) Outcomes - We defined all outcomes measured, such as those related to animal behavior and related axon signaling.

(7) Statistical methods - None of the reviewers had any issues regarding our description of statistical methods, which we described in detail in this version of the paper.

(8) Experimental animals - We described that DAT- Cre mice were obtained through JAX labs, and NET-Cre mice were obtained from the Tonegawa lab (Wagatsuma et al. 2017)

(9) Experimental procedure - Already listed in detail in Methods section.

(10) Results - Rigorously described in detail for behaviors and related axon dynamics.

Wagatsuma, Akiko, Teruhiro Okuyama, Chen Sun, Lillian M. Smith, Kuniya Abe, and Susumu Tonegawa. “Locus Coeruleus Input to Hippocampal CA3 Drives Single-Trial Learning of a Novel Context.” Proceedings of the National Academy of Sciences 115, no. 2 (January 9, 2018): E310–16. https://doi.org/10.1073/pnas.1714082115.

Second, why were different linear tracks used for studies of VTA and LC axon activity (from line 362)? Could this potentially contribute to the partly distinct activity correlates that were found for VTA and LC axons?

A detailed response to this is written above for a similar comment from reviewer 1.

Third, the authors seem to have used two different criteria for defining immobility. Immobility was defined as moving at <5 cm/s for the behavioral analysis in Figure 3a, but as <0.2 cm/s for the imaging data analysis in Figure 4 (see legends to these figures and also see Methods, from line 447, line 469, line 498)? I do not understand why, and it would be good if the authors explained this.

This is an error leftover from before we converted velocity from rotational units of the treadmill to cm/s. This will be corrected in the next version of the paper.

(3) In the Results section (from line 182) the authors convincingly addressed the possibility that less time spent immobile in the novel environment may have contributed to the novelty-induced increase of LC axon activity in dorsal CA1 (Figure 4). In addition, initially (for the first 2-4 laps), the mice also ran more slowly in the novel environment (Figure 3aIII, top panel). Given that LC and VTA axon activity were both increasing with velocity (Figure 1F), reduced velocity in the novel environment may have reduced LC and VTA axon activity, but this possibility was not addressed. Reduced LC axon activity in the novel environment could have blunted the noveltyinduced increase. More importantly, any potential novelty-induced increase in VTA axon activity could have been masked by decreases in VTA axon activity due to reduced velocity. The latter may help to explain the discrepancy between the present study and previous findings that VTA neuron firing was increased by novelty (see Discussion, from line 243). It may be useful for the authors to address these possibilities based on their data in the Results section, or to consider them in their Discussion.

This is a great point. The decreased velocity in the novel environment could lead to a diminished novelty response in LC axons. We will add a discussion point on this in the next version. This could also be the case for VTA axons, so will add a discussion point that the lack of novelty signaling seen in VTA axons could be due to reduced velocity masking this signal.

(4) Sensory properties of the water reward, which the mice may be able to detect, could account for reward-related activity of VTA axons (instead of an expectation of reward). Do the authors have evidence that this is not the case? Occasional probe trials, intermixed with rewarded trials, could be used to test for this possibility.

Mice receive their water reward through a waterspout that is immobile and positioned directly in front of their mouth (which is also immobile as they are head fixed) and water delivery is triggered by a solenoid when the mice reach the end of the virtual track. Therefore, because the waterspout remains in the same place relative to the mouse, and the water reward is not delivered until they reach the end of the virtual track, there is nothing for the mice to detect. We will update the paper to make this clearer.

Additionally, on the initial laps with no reward, the ramping activity is still present (Krishnan et al, 2022) indicating this activity is not directly related to the presence/absence of water but is instead caused by reward expectation.

Reviewer #3 (Public Review):

Summary:

Heer and Sheffield provide a well-written manuscript that clearly articulates the theoretical motivation to investigate specific catecholaminergic projections to dorsal CA1 of the hippocampus during a reward-based behavior. Using 2-photon calcium imaging in two groups of cre transgenic mice, the authors examine the activity of VTA-CA1 dopamine and LC-CA1 noradrenergic axons during reward seeking in a linear track virtual reality (VR) task. The authors provide a descriptive account of VTA and LC activities during walking, approach to reward, and environment change. Their results demonstrate LC-CA1 axons are activated by walking onset, modulated by walking velocity, and heighten their activity during environment change. In contrast, VTA-CA1 axons were most activated during the approach to reward locations. Together the authors provide a functional dissociation between these catecholamine projections to CA1. A major strength of their approach is the methodological rigor of 2-photon recording, data processing, and analysis approaches. These important systems neuroscience studies provide solid evidence that will contribute to the broader field of learning and memory. The conclusions of this manuscript are mostly well supported by the data, but some additional analysis and/or experiments may be required to fully support the author's conclusions.

Weaknesses:

(1) During teleportation between familiar to novel environments the authors report a decrease in the freezing ratio when combining the mice in the two experimental groups (Figure 3aiii). A major conclusion from the manuscript is the difference in VTA and LC activity following environment change, given VTA and LC activity were recorded in separate groups of mice, did the authors observe a similar significant reduction in freezing ratio when analyzing the behavior in LC and VTA groups separately?

In response to this comment, we will analyze the freezing ratios in DAT-Cre and NET-Cre mice separately. However, other members of the lab have seen the same result in other mouse strains (See Dong et al. 2021), so we do not expect to see a difference (but it is certainly worth checking).

(2) The authors satisfactorily apply control analyses to account for the unequal axon numbers recorded in the LC and VTA groups (e.g. Figure 1). However, given the heterogeneity of responses observed in Figures 3c, 4b and the relatively low number of VTA axons recorded (compared to LC), there are some possible limitations to the author's conclusions. A conclusion that LC-CA1 axons, as a general principle, heighten their activity during novel environment presentation, would require this activity profile to be observed in some of the axons recorded in most all LC-CA1 mice.

We agree with the reviewer’s point here. To help avoid this problem, when downsampling LC axons to compare to VTA axons, we matched the sampling statistics of the VTA axons/mice (i.e. only one LC axon was taken from each mouse to match the VTA dataset).

However, in the next version of the paper we will also report the number of mice that we see a significant novel response in. We will also add the number of mice with significant activity for each of the measures in the familiar environment (e.g. how many mice had axons positively correlated with velocity).

Additionally, if the general conclusion is that VTA-CA1 axons ramp activity during the approach to reward, it would be expected that this activity profile was recorded in the axons of most all VTA-CA1 mice. Can the authors include an analysis to demonstrate that each LC-CA1 mouse contained axons that were activated during novel environments and that each VTA-CA1 mouse contained axons that ramped during the approach to reward?

As stated above, we will add the number of mice that had each activity type we reported here.

(3) A primary claim is that LC axons projecting to CA1 become activated during novel VR environment presentation. However, the experimental design did not control for the presentation of a familiar environment. As I understand, the presentation order of environments was always familiar, then novel. For this reason, it is unknown whether LC axons are responding to novel environments or environmental change. Did the authors re-present the familiar environment after the novel environment while recording LC-CA1 activity?

This is an important point to address. While we never varied the presentation order of the familiar vs novel environments, we did record the activity of LC axons in some of the mice in a dark environment (no VR cues) prior to exposure to the familiar environment. We will look at these axons to address whether they respond to initial exposure to the familiar environment. This will allow us to check whether they are responding to environmental change or novelty. We will add this analysis to the next version of the paper.

Author Response

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

eLife assessment

This important study assesses anatomical, behavioral, physiological, and neurochemical effects of early-life seizures in rats, describing a striking astrogliosis and deficits in cognition and electrophysiological parameters. The convincing aspects of the paper are the wide range of convergent techniques used to understand the effects of early-life seizures on behavior as well as hippocampal prefrontal cortical dynamics. While reviewers thought that the scope was impressive, there was criticism of the statistical robustness and number of animals used per study arm, as well as the lack of causal manipulations to determine cause-and-effect relationships. This paper will be of interest to neurobiologists, epileptologists, and behavioral scientists.

We thank Joseph Gleeson as the Reviewing Editor and Laura Colgin as the Senior Editor for considering this revision of our manuscript for publication in eLife. We appreciate the positive acknowledgment of the study and the critical points raised by the reviewers. We have addressed all the excellent comments of the two reviewers, providing a detailed response for each comment. We believe that these revisions have significantly improved the quality and rigor of our study.

We want to assure you that our experimental design was meticulously crafted, incorporating adequate control groups, and is grounded in prominent studies in systems neurophysiology focusing into early-life seizures effects, especially for capturing mild effects. We conducted statistical tests adhering to established norms and recommendations, ensuring a thorough and transparent description of the employed statistical methods. We welcome any specific suggestions to further improve this aspect.

In fact, the concerns raised by the reviewers regarding statistical robustness may stem from a misunderstanding of the rat cohorts used in each experiment. Criticism was directed at the use of only 5 animals without a control group for acute electrophysiological recording. It is essential to clarify that this group served the sole purpose of confirming that the injection of lithium-pilocarpine would induce both behavioral and electrographic seizures. Importantly, this was a descriptive result, and no statistical test or further analysis was conducted with these data. In the revised manuscript, we have made adjustments to this description, aiming to eliminate any ambiguity, particularly addressing the issue of sample size in each experiment.

Regarding the lack of causal manipulations, we fully agree that this approach would provide a deeper mechanistic understanding of our findings and is an essential next step. Still, developmental brain disturbances are linked to manifold intricate outcomes, so an initial observational exploration would offer insights about particular and nuanced relationships for following studies aimed at targeted interventions. In this context, our objective was to provide a comprehensive characterization of ELS effects to serve as a foundation for future research. While recognizing the relevance of causal manipulations, only a more sophisticated data analyses were able to reveal more complex aspects like specific multivariate associations and non-linear relationships that would not have been revealed by causally perturbing one or another factor at first. In the revised manuscript, we emphasized the limitation of lacking causal manipulations as well as the advantages of our approach. Also, we mentioned some possible targets for following perturbational investigations based on our findings.

For a more detailed discussion on these matters, we invite you to review our response to reviewers.

Reviewer 1

In this paper, Ruggiero, Leite, and colleagues assess the effects of early-life seizures on a large number of anatomical, physiological, behavioral, and neurochemical measures. They find that prolonged early-life seizures do not lead to obvious cell loss, but lead to astrogliosis, working memory deficits on the radial arm maze, increased startle response, decreased paired pulse inhibition, and increased hippocampal-PFC LTP. There was a U-shape relationship between LTP and cognitive deficits. There is increased theta power during the awake state in ELS animals but reduced PFC theta-gamma coupling and reduced theta HPC-PFC coherence. Theta coherence seems to be similar in ACT and REM states in ELS animals while in decreases in active relative REM in controls.

Strengths:

The main strength of the paper is the number of convergent techniques used to understand how hippocampal PFC neural dynamics and behavior change after early-life seizures. The sheer scale, breadth, and reach of the experiments are praiseworthy. It is clear that the paper is a major contribution to the field as far as understanding the impact of early-life seizures. The LTP findings are robust and provide an important avenue for future study. The experiments are performed carefully and the analysis is appropriate. The paper is well-written and the figures are clear.

We express our gratitude to Reviewer #1 for conducting a thoughtful and comprehensive review of our manuscript. We sincerely value both the constructive criticisms provided and your acknowledgment of the manuscript's strengths.

Weaknesses:

The main weakness of the paper is the lack of causal manipulations to determine whether prevention or augmentation of any of the findings has any impact on behavior or cognition. Alternatively, if other manipulations would enhance working memory in ELS animals, it would be interesting to see the effects on any of these parameters measured in the paper.

We sincerely appreciate the insightful comments from Reviewer #1 regarding the potential benefits of including causal manipulations in our study. We wholeheartedly agree that such manipulations can provide a deeper understanding of the mechanistic underpinnings of the observed relationships and represent a crucial next step in our research trajectory.

Our primary objective in this study was to establish a comprehensive framework through observational examinations, exploring intricate relationships across various neurobiological and behavioral variables in the aftermath of early-life seizures (ELS). By identifying these associations, our work aims to provide a foundation for future investigations that can delve into targeted interventions.

While we acknowledge the importance of causal manipulations, we would like to underscore the advantages of our initial multivariate correlational study. Importantly, developmental brain disturbances have lasting impacts affecting multiple biological outcomes that may have intricate relationships between themselves. Firstly, although some neurobiological variables stood out from the comparisons of group means, this did not reveal some nuanced relationships within the data. The complexity of the relationships we uncovered, involving behavior, cognition, immunohistochemistry, plasticity, neurochemistry, and network dynamics, required a more elaborate analytical approach. Only through sophisticated data analysis techniques, we were able to dissect important peculiarities, such as the robust multivariate association between brain-wide astrogliosis and sensorimotor impairments, as well as non-linear relationships, such as the inverted-U relationship between plasticity and working memory. These nuances might not have been fully revealed through causal manipulations, since several variables are strongly related and consequently can affect several outcomes, leading to a false conclusion of direct causality.

Nevertheless, we acknowledge the understatement of the limitation of lacking causal manipulations in our manuscript. To address this, we have included a dedicated section in the discussion highlighting this limitation. We emphasize the advantages of this exploratory phase, supported by a review of the literature on cause-and-effect studies that align with our findings. Additionally, we speculate on promising targets for future cause-and-effect studies based on our findings. For instance, we hypothesize that enhancing plasticity may improve working memory in control subjects, while attenuating plasticity might have a similar effect in ELS subjects. Furthermore, we propose that reactive astrogliosis and concurrent neuroinflammatory processes likely underlie sensorimotor changes in the ELS group. Lastly, we suggest that dopaminergic antagonism in the ELS group could normalize behavioral deficits, prevent the exaggerated LTP induction of the HPC-PFC pathway, reestablish the state-dependent network dynamics, and desensitize the dopaminergic response.

[...]Also, I find the sections where correlations and dimensionality reduction techniques are used to compare all possible variables to each other less compelling than the rest of the paper (with the exception of the findings of U-shaped relationship of cognition to LTP). In fact, I think these sections take away from the impact of the actual findings.

We appreciate the reviewer's feedback and would like to emphasize the significance of the multivariate analysis conducted in our study. Multivariate analysis extends beyond bivariate correlations and is the only type of analysis capable of comprehending the relation of data in a multidimensional way, offering a comprehensive approach to understanding complex relationships among multiple variables. By employing techniques such as principal component analysis (PCA), generalized linear models (GLM), and canonical correlation analysis (CCA), we aimed to unravel intricate patterns of covariance that explore how different variables collectively contribute to the observed outcomes and assess the impact of each independent variable (predictor) on the dependent variable (the variable to be predicted or explained). Importantly, it enables us to control for potential confounding factors by keeping all other variables constant.

While we acknowledge that these sections may appear intricate, their inclusion is indispensable for a comprehensive understanding of the diverse variables associated with SE outcomes. We believe that these analyses offer valuable insights into the intricate dynamics of our study, providing a more holistic perspective on the altered spectrum induced by early-life seizures (ELS).

Regarding the reviewer's observations about the impact of the U-shaped relationship between cognition and LTP, we have made graphical and textual adjustments to emphasize the significance of these findings, aiming to enhance their clarity and impact within the broader context of our research. We trust that these modifications contribute to a more compelling presentation of our results.

[…]Finally, the apomorphine section seemed to hang separately from the rest of the paper and did not seem to fit well.

We appreciate the Reviewer #1 feedback on the apomorphine section. In order to address this point, we carefully rewrote our rationale before the results to clarify our hypothesis and chosen methodology. In our work, we performed the apomorphine experiment as a logical next step of previous data. We showed that ELS rats display REM-like oscillatory dynamics during active behavior, similar to genetically and pharmacologically hyperdopaminergic mice (Dzirasa et al., 2006). Furthermore, other results also indicated possible dopamine neurotransmission alterations, such as working memory deficits, hyperlocomotion, PPI deficits, aberrant HPC-PFC LTP, and abnormal PFC gamma coordination. Therefore, we hypothesized that ELS animals would present a state of hyperdopaminergic activity. Among the possible methodologies to investigate the hyperdopaminergic state, we choose the apomorphine sensitivity test, which is classically used and induces unambiguous behavior and neurochemical alterations in hyperdopaminergic rodents (Duval, 2023; Ellenbroek & Cools, 2002).

Reviewer 1 (Recommendations For The Authors):

(1) It would be useful to stain for other GABAergic interneuron markers such as somatostatin, VIP, CCK.

(2) The authors refer to neuroinflammation but they are really referring to reactive astrogliosis. I would also suggest staining for microglial markers.

(3) The duration of chronic electrographic seizures in ELS animals should also be calculated and presented.

(4) Word usage: the authors frequently use the word "presents" when "demonstrates" would be more appropriate

(1) We appreciate your insight into staining for other GABAergic interneuron markers such as somatostatin, VIP, CCK. While investigating additional interneuron types is indeed relevant, it was not the primary focus of this study for several reasons: 1) The overall neuron density, assessed through NeuN immunostaining, revealed no differences between controls and early life seizure (ELS) groups, even in brain regions susceptible to neuron death after SE (i.e., CA1). Therefore, differences in interneurons, which are more resistant to death in SE and constitute approximately 20% of the cells, are unlikely. 2) Among all interneuron subtypes, Parvalbumin-positive (PV+) interneurons represent a substantial population and are susceptible to various stressors. In the hippocampus, 24% of GABAergic neurons are PV+, whereas 14% are SST+, 10% are CCK+, and VIP+ are less than 10% (Freund and Buzsaki, 1996). Consequently, we considered PV+ interneurons to be a more sensitive subpopulation for evaluating the effects of SE. As they showed no significant difference, we do not believe that assessing smaller subtypes, such as VIP+ or CCK+ cells, would yield significant differences.

(2) While we often see activated microglia in hippocampal sclerosis, these cells are only slightly increased in cases without hippocampal sclerosis (which are similar to our animals), as we previously published (Peixoto-Santos et al., 2012). Astrocytes are a better marker for the epileptogenic zone, as are increased in epileptogenic zones without neuron loss and are also important for controlling neuronal activity by neurotransmitter recycling and ion buffering. In fact, our present model is very similar to the mesial temporal lobe epilepsy patients with gliosis-only, which are characterized by only presenting increased reactive astrogliosis in the hippocampus, without cell loss, and also present changes in innate inflammatory response related to the presence of reactive astrocytes (Grote et al., 2023).

(3) We have performed these calculations and added this information to the revised manuscript.

(4) We thank the reviewer for the word usage recommendation. Indeed, we frequently used “present” throughout the manuscript to describe the observations and patterns the groups “exhibited” or “showed”. However, we believe this is truly not the most appropriate usage in the Discussion when we describe the multivariate latent factors, as we did not “present” them, but rather, we “demonstrated” their existence and significance through our analysis. We rewrote these sentences and hope this is the point the reviewer was referring to.

References:

Duval F. Systematic review of the apomorphine challenge test in the assessment of dopaminergic activity in schizophrenia. Healthcare. 2023 11 (1487): 1-11. doi: 10.3390/healthcare11101487.

Dzirasa K, Ribeiro S, Costa R, Santos LM, Lin SC, Grosmark A, Sotnikova TD, Gainetdinov RR, Caron MG, Nicolelis MAL. Dopaminergic control of sleep-wake states. Journal of Neuroscience. 2006 26:10577–10589. doi:10.1523/JNEUROSCI.1767-06.2006.

Freund TF, Buzsáki G. Interneurons of the hippocampus. Hippocampus. 1996;6(4):347-470. doi: 10.1002/(SICI)1098-1063(1996)6:4<347::AID-HIPO1>3.0.CO;2-I. PMID: 8915675.

Ellenbroek BA & Cools AR. Apomorphine susceptibility and animal models for psychopathology: genes and environment. Behavior Genetics. 2002 32 (5): 349-361. doi: 10.1023/a:1020214322065.

Grote A, Heiland DH, Taube J, Helmstaedter C, Ravi VM, Will P, Hattingen E, Schüre JR, Witt JA, Reimers A, Elger C, Schramm J, Becker AJ, Delev D. 'Hippocampal innate inflammatory gliosis only' in pharmacoresistant temporal lobe epilepsy. Brain. 2023 Feb 13;146(2):549-560. doi: 10.1093/brain/awac293. PMID: 35978480; PMCID: PMC9924906.

Peixoto-Santos JE, Galvis-Alonso OY, Velasco TR, Kandratavicius L, Assirati JA, Carlotti CG, Scandiuzzi RC, Serafini LN, Leite JP. Increased metallothionein I/II expression in patients with temporal lobe epilepsy. PLoS One. 2012;7(9):e44709. doi: 10.1371/journal.pone.0044709. Epub 2012 Sep 18. Erratum in: PLoS One. 2016;11(7):e0159122. PMID: 23028585; PMCID: PMC3445538.

Reviewer 2

In this manuscript, the authors employ a multilevel approach to investigate the relationship between the hippocampal-prefrontal (HPC-PFC) network and long-term phenotypes resulting from early-life seizures (ELS). Their research begins by establishing an ELS rat model and conducting behavioral and neuropathological studies in adulthood. Subsequently, the manuscript delves into testing hypotheses concerning HPC-PFC network dysfunction. While the results are intriguing, my enthusiasm is tempered by concerns related to the logical flow

We thank the reviewer for bringing attention to the logical flow of the manuscript. Given the diverse array of behavioral and neurobiological variables examined in our study obtained through various methods and measures, we utterly recognize the utmost importance of a clear and coherent logical flow to provide a comprehensive understanding of the overall narrative.

Our goal was to articulate the neurobiological findings in a manner that underscores their convergence of mechanisms, revealing a cohesive relationship between early-life seizure, cognitive deficits, sensorimotor impairments, abnormal network dynamics, aberrant plasticity, neuroinflammation and dysfunctional dopaminergic transmission.

Briefly, an outline of our narrative could be summarized in the highlights:

(1) ELS induces sensorimotor alterations and working memory deficits.

(2) ELS does not induce neuronal loss, so neurobiological underpinnings may be molecular and functional.

(3) ELS induces brain-wide astrogliosis and exaggerated HPC-PFC long-term plasticity.

(4) ELS does not induce neuronal loss, so neurobiological underpinnings may be molecular and functional.

(5) Sensorimotor alterations are more correlated to astrogliosis, while cognitive deficits to altered HPC-PFC plasticity.

(6) ELS-induced functional alterations may also be observable in freely moving subjects. ELS induces state-dependent alterations in the HPC-PFC network dynamics, such as increased hippocampal theta and abnormal PFC gamma coordination during behavioral activity.

(7) ELS leads to REM-ACT similarity, previously reported in hyperdopaminergic mice, indicating dopaminergic dysfunction.

(8) ELS exhibits altered dopaminergic transmission and behavioral sensitivity that mirror the initial sensorimotor findings.

(9) The literature establishes an inverted-U relationship between dopamine and cognition and PFC plasticity, which may explain our finding of an inverted-U relationship between working memory and HPC-PFC LTP across CTRL and ELS rats.

To address this concern, we have made revisions to enhance the logical flow, ensuring a more seamless transition between the different sections of the Results by presenting clearer links between observations and following investigations. We hope these changes contribute to a more straightforward rationale and easily understandable presentation of our hypotheses and results.

Focus on Correlations: The manuscript primarily highlights correlations as the most significant findings. For instance, it demonstrates that ELS induces cognitive and sensorimotor impairments. However, it falls short of elucidating why these deficits are specifically linked to HPC-PFC synaptic plasticity/network. Furthermore, the manuscript mentions the involvement of other brain regions like the thalamus in the long-term outcomes of ELS based on immunohistochemistry data.

Thank you for your insightful comments, which allowed us to provide further clarification on our study's focus and findings. Our primary goal was to delve into the electrophysiological alterations within the HPC-PFC pathway. The rationale behind this choice lies in the hypothesis that, even in the absence of significant neuronal loss, functional changes in circuits closely linked to the cognitive and behavioral aspects under investigation could be identified.

While we concentrated our electrophysiological investigation on the HPC-PFC pathway due to its well-established functional correlates in existing literature, it is essential to highlight that our data reveal broader alterations in neural circuitry. Notably, we observed an increase in GFAP in the entorhinal cortex and thalamic reticular nucleus, along with changes in the dopaminergic release within the VTA-NAc pathway. These findings suggest that the impact of early-life seizures extends beyond the HPC-PFC circuit.

While we recognize the relevance of other brain circuits in the outcomes of ELS, we argue for a specific role of the HPC-PFC circuit in the outcomes of ELS. We will detail the supporting evidence and arguments that specifically link the HPC-PFC function to our ELS-related observations in a later comment regarding the "overinterpretation" of the HPC-PFC role. To better convey these important nuances, we have made specific modifications to the results and in the discussion section to underscore the broader implications of our findings, providing a more comprehensive understanding of the study's scope and outcomes.

[…]This raises questions about the subjective nature and persuasiveness of the statistical studies presented.

All statistical analyses were carefully applied based on the literature and following well-established precepts and precautions. Specifically, we constructed the experimental design for univariate inferential statistics for the data related to behavioral tests, synaptic plasticity, immunohistochemistry, oscillatory activity, and dopaminergic sensitization. However, we also submitted our data to multivariate statistical analysis, which is recommended in cases with a considerable amount of data, and intend to investigate possible hidden effects. In this situation, multivariate analyses are inherently exploratory due to the possibility of using multiple measurements for each phenomenon investigated. Nevertheless, their application is not subjective and follows the same statistical rigor as univariate analyses. We firmly believe that abstaining from exploring these data, would not reach the full potential of this analytical method in dissecting the multidimensional associations within our dataset. In order to eliminate any doubt regarding the objectivity in the choice and application of statistics, we carefully rewrote the methods, highlighting the details of statistical rigor even more.

Sample Size Concerns: The manuscript raises concerns about the adequacy of sample sizes in the study. The initial cohort for acute electrophysiology during ELS induction comprised only 5 rats, without a control group. Moreover, the behavioral tests involved 11 control and 14 ELS rats, but these same cohorts were used for over four different experiments. Subsequent electrophysiology and immunohistochemistry experiments used varying numbers of rats (7 to 11). Clarification is needed regarding whether these experiments utilized the same cohort and why the sample sizes differed. A power analysis should have been performed to justify sample sizes, especially given the complexity of the statistical analyses conducted.

We appreciate the reviewer's thoroughness and considerations regarding the sample sizes used in our study. The concerns raised about statistical robustness seem to stem from a lack of clarity in delineating the rat cohorts used in each experiment. It is encouraging to note that several studies in the field of neurophysiology, employing similar analyses, utilize a sample size similar to what was used in our research. The choice of the sample size was based on a thorough analysis of the existing literature, considering specific experimental demands, the complexity of employed techniques, and the need to achieve statistically robust results. In response to these concerns and to enhance clarity on the sample sizes, we have made several modifications (highlighted in red) in the text. Below, we provide details for each animal cohort utilized:

Cohort 1 - Acute Electrophysiology

The decision to use only 5 animals without a control group for acute electrophysiological recording aimed specifically to confirm that the injection of lithium-pilocarpine would induce both behavioral and electrographic seizures. It is crucial to note that this was a descriptive result and a methodological control of the ELS model. Besides, no statistical test or further analysis was conducted on these data. We maintain the belief that a group of 5 animals is sufficient to demonstrate that the protocol induces electrographic seizures, and introducing a control group was considered unnecessary to show that saline injection does not induce electrographic seizures.

Cohort 2 - Behavior, LTP Recording, and Immunohistochemistry

Initially, 14 (ELS) and 11 (CTRL) rats were used for behavior assessment. The reduction in sample size for LTP and immunohistochemistry experiments was influenced by practical challenges, including mortality during LTP surgery and issues with immunohistochemical staining that hindered a proper analysis for some animals.

Cohort 3 - Chronic Freely-Moving Electrophysiology

A new cohort of animals (n=6 and 9 for CTRL and ELS, respectively) was used specifically for freely-moving electrophysiological data.

Cohort 4 - Behavioral Sensitization to Psychostimulants

A fourth cohort was utilized for assessing behavioral sensitization to psychostimulants (CTRL n=15 and ELS n=14). The reduced sample size for neurotransmitter analysis (CTRL n=8 and ELS n=9) was a deliberate selection of a subsample to ensure a sufficient sample for quantification while maintaining statistical validity

Overinterpretation of HPC-PFC Network Dysfunction: The manuscript potentially overinterprets the role of HPC-PFC network dysfunction based on the results.

We appreciate the insight from Reviewer #2 regarding the potential overinterpretation of the role of the hippocampal-prefrontal cortex (HPC-PFC) network dysfunction in the various alterations observed after ELS.

The significance of HPC-PFC plasticity and network function has been extensively documented concerning cognitive, affective, and sensorimotor functions, as well as in models of neuropsychiatric diseases. Our recent review (Ruggiero et al., 2021) compiles these findings. Specifically, the HPC-PFC network has been linked to spatial working memory through a series of causal and correlational studies conducted by Floresco et al. and Gordon et al. These findings make the HPC-PFC pathway a plausible candidate for underlying alterations associated with working memory, consistent with our observation of exaggerated HPC-PFC LTP associated with poorer performance in the ELS group. Regarding the immunohistochemical observations, we concur with Reviewer #2 that these findings suggest broader-scale brain alterations related to sensorimotor dysfunction beyond the HPC-PFC circuitry. Surely, we acknowledge that these large-scale alterations may underlie brain-wide network functional changes.

In our network dynamics study arm, we investigated HPC-PFC oscillatory activity, allowing us to discuss potential relationships between abnormal plasticity (verified in the second study arm) and network dynamics. It is important to note that while there is some anatomical specificity to the LFPs recorded in the HPC and PFC, these activities may represent larger-scale limbic-cortical dynamics. The intermediate HPC exhibits a significant influence from both dorsal and ventral HPC, and the prelimbic PFC is intricately related to both hippocampal and thalamic oscillations exhibiting under-demand state-dependent synchrony. Additionally, the state maps used in our study were initially described to distinguish states at a global forebrain network level. Even in our past studies, we have described HPC-PFC patterns of network activity (Marques et al., 2022a) that later were found to represent a part of a brain-wide synchrony pattern (Marques et al., 2022b). However, most of our findings on oscillatory dynamics were centered around theta oscillations, a well-established brain-wide activity that originates and spreads from the hippocampus and are present in the HPC-PFC circuit during activity.

In conclusion, we believe the correlations between HPC-PFC LTP and working memory, as well as the specific alterations of theta coordinated activity, support a particular role of the HPC-PFC network dysfunction in the effects of ELS. However, the brain-wide immunochemical alterations are plausible indications of larger-scale dysfunctional networks. To address this issue, we emphasized in the discussion of network findings that the immunohistochemical and neurochemical findings endorse the need to investigate ELS effects on larger networks.

Notably, cognitive deficits are described as subtle, with no evidence of learning deficits and only faint working memory impairments. However, sensorimotor deficits show promise. Consequently, it's essential to justify the emphasis on the HPC-PFC network as the primary mechanism underlying ELS-associated outcomes, especially when enhanced LTP is observed. Additionally, the manuscript seems to sideline neuropathological changes in the thalamus and the thalamus-to-PFC connection. The analysis lacks a direct assessment of the causal relationship between HPC-PFC dysfunction and ELS-associated outcomes, leaving a multitude of multilevel analyses yielding potential correlations without easily interpretable results.

We thank Reviewer #2 for the thorough review and insightful comments. To better grasp the context, it is crucial to consider this characterization within the scope of our experimental design and expected outcomes. Unlike epilepsy models involving adult animals or interventions causing pronounced neuronal loss and structural modifications, our study was intentionally designed to explore moderate behavioral alterations. In fact, the mild behavioral alterations observed in ELS models and the lack of neuronal loss guided our focus on investigating changes in HPC-PFC communication.

While our observed cognitive deficits may be milder compared to certain models, it is imperative to underscore their robustness and clinical relevance. These findings have been consistently replicated globally across various experimental models, encompassing ELS induced by hyperthermia (Chang et al., 2003; Kloc et al., 2022), kainic acid (Statsfrom et al. 1993), flurothyl (Karnam et al., 2009a; 2009b), and hypoxia (Najafian et al., 2021; Hajipour et al., 2023). Mild cognitive deficits were also evident by other research groups using the pilocarpine model in P12 (Mikulecká et al., 2019; Kubová et al., 2013; Kubová et al., 2002). Furthermore, our group replicated the working memory deficit results using an alternative paradigm (the T-maze) and a different rat strain (Sprague Dawley), enhancing the reliability of our observations (D’Agosta et al., 2023).

The clinical perspective gains importance, considering that cognitive effects of ELS may be less severe than those in patients with long-term epilepsy. In fact, the majority of patients with childhood epilepsy exhibit mild cognitive impairment as the most common grade of severity - more than two times the rate of severe cognitive impairment (Sorg et al., 2022). Investigating the mechanisms underlying these mild cognitive changes is crucial for shedding light on neurobiological aspects not fully understood, thereby expanding our comprehension of the consequences of ELS.

We recognize the challenges associated with conducting causal experiments in neuroscience, especially in long-term and chronic alterations as seen in our model. Isolating modifications of specific activities is indeed intricate. However, it's essential to acknowledge that neuroscience progress has not solely relied on causal experiments but has significantly advanced through correlational observations. Our findings serve as a foundational step in comprehending the repercussions of ELS, proposing mechanisms and circuits that necessitate further in-depth dissection and study in the future. We have integrated these considerations into the discussion section of the manuscript to enhance clarity.

Overall, while the manuscript presents intriguing findings related to the HPC-PFC network and ELS outcomes, it requires a more rigorous experimental design[…]

We thank the reviewer for acknowledging our intriguing findings. Regarding the experimental design, we are confident that all the manuscript hypotheses, design, and execution of experiments were rigorously based on the literature and carried out with all necessary controls. As stated earlier, we constructed the experimental design for univariate inferential statistics and explored associations between variables using multivariate statistics. Specifically, we achieved a rigorously experimental design following a series of guidelines. First, the planning of the sample size in each experiment and their respective controls were based on mild effects from the ELS literature. As previously indicated, the only experiment with one group was just the description of the behavioral effects and electrographic seizures after the acute injection of lithium-pilocarpine. Given the exhaustive replication of these data in the ELS literature, this result was presented descriptively as a methodological control. Second, detailed descriptions of statistics were made in both methods and results, always indicating positive and negative results. Notably, the experimental designs used in the work do not correspond to any novelty or radicalization, strictly following the literature of the field. However, new indications and references about the experimental accuracy were added to the manuscript to resolve any doubts regarding objectivity.

References:

Chang YC, Huang AM, Kuo YM, Wang ST, Chang YY, Huang CC. Febrile seizures impair memory and cAMP response-element binding protein activation. Ann Neurol. 2003 Dec;54(6):706-18. doi: 10.1002/ana.10789. PMID: 14681880.

D'Agosta R, Prizon T, Zacharias LR, Marques DB, Leite JP, Ruggiero RN. Alterations in hippocampal-prefrontal cortex connectivity are associated with working memory impairments in rats subjected to early-life status epilepticus. In: NEWROSCIENCE INTERNATIONAL SYMPOSIUM, 2023, Ribeirão Preto. Poster.

Hajipour S, Khombi Shooshtari M, Farbood Y, Ali Mard S, Sarkaki A, Moradi Chameh H, Sistani Karampour N, Ghafouri S. Fingolimod Administration Following Hypoxia Induced Neonatal Seizure Can Restore Impaired Long-term Potentiation and Memory Performance in Adult Rats. Neuroscience. 2023 May 21;519:107-119. doi: 10.1016/j.neuroscience.2023.03.023. Epub 2023 Mar 28. PMID: 36990271.

Karnam HB, Zhou JL, Huang LT, Zhao Q, Shatskikh T, Holmes GL. Early life seizures cause long-standing impairment of the hippocampal map. Exp Neurol. 2009 Jun;217(2):378-87. doi: 10.1016/j.expneurol.2009.03.028. Epub 2009 Apr 2. PMID: 19345685; PMCID: PMC2791529.

Karnam HB, Zhao Q, Shatskikh T, Holmes GL. Effect of age on cognitive sequelae following early life seizures in rats. Epilepsy Res. 2009 Aug;85(2-3):221-30. doi: 10.1016/j.eplepsyres.2009.03.008. Epub 2009 Apr 22. PMID: 19395239; PMCID: PMC2795326.

Kubová H, Mareš P. Are morphologic and functional consequences of status epilepticus in infant rats progressive? Neuroscience. 2013 Apr 3;235:232-49. doi: 10.1016/j.neuroscience.2012.12.055. Epub 2013 Jan 7. PMID: 23305765.

Kloc ML, Marchand DH, Holmes GL, Pressman RD, Barry JM. Cognitive impairment following experimental febrile seizures is determined by sex and seizure duration. Epilepsy Behav. 2022 Jan;126:108430. doi: 10.1016/j.yebeh.2021.108430. Epub 2021 Dec 10. PMID: 34902661; PMCID: PMC8748413.

Kubová H, Mares P, Suchomelová L, Brozek G, Druga R, Pitkänen A. Status epilepticus in immature rats leads to behavioural and cognitive impairment and epileptogenesis. Eur J Neurosci. 2004 Jun;19(12):3255-65. doi: 10.1111/j.0953-816X.2004.03410.x. PMID: 15217382.

Marques DB, Ruggiero RN, Bueno-Junior LS, Rossignoli MT, and Leite JP. Prediction of Learned Resistance or Helplessness by Hippocampal-Prefrontal Cortical Network Activity during Stress. The Journal of Neuroscience. 2022a 42 (1): 81-96.. https://doi.org/10.1523/jneurosci.0128-21.2021.

Marques DB, Rossignoli MT, Mesquita BDA, Prizon T, Zacharias LR, Ruggiero RN and Leite JP. Decoding fear or safety and approach or avoidance by brain-wide network dynamics abbreviated. bioRxiv. 2022b https://doi.org/10.1101/2022.10.13.511989.

Mikulecká A, Druga R, Stuchlík A, Mareš P, Kubová H. Comorbidities of early-onset temporal epilepsy: Cognitive, social, emotional, and morphologic dimensions. Exp Neurol. 2019 Oct;320:113005. doi: 10.1016/j.expneurol.2019.113005. Epub 2019 Jul 3. PMID: 31278943.

Najafian SA, Farbood Y, Sarkaki A, Ghafouri S. FTY720 administration following hypoxia-induced neonatal seizure reverse cognitive impairments and severity of seizures in male and female adult rats: The role of inflammation. Neurosci Lett. 2021 Mar 23;748:135675. doi: 10.1016/j.neulet.2021.135675. Epub 2021 Jan 28. PMID: 33516800.

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Author Response

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

Reviewer #1

This is a short but important study. Basically, the authors show that α-synuclein overexpression's negative impact on synaptic vesicle recycling is mediated by its interaction with E-domain containing synapsins. This finding is highly relevant for synuclein function as well as for the pathophysiology of synucleinopathies. While the data is clear, functional analysis is somewhat incomplete.

(1) The authors should present a clearer dissociation of endocytosis and exocytosis under the various conditions they study. They should quantify the rate of rise and decay of pHluorin signals. 2. In addition, I strongly recommend a few additional experiments with and without a vATPase inhibitor such as bafilomycin to estimate the relative effects on exo- vs. endocytosis. As the authors are aware bafilomycin will mask the re-acidification /endocytosis component, thus revealing pure exocytosis and thus enabling quantification of endocytosis with minimal contamination from exocytosis.

In the revised version, we analyzed and quantified exocytosis and endocytosis separately, with bafilomycin experiments, as the reviewer suggested (new data, Fig. 1- Fig. Supp. 1A-B). Overexpression of human alpha-synuclein only attenuated exocytosis in neurons that also expressed synapsins (WT neurons and synapsin TKO neurons transduced with synapsin Ia). In parallel, we also examined endocytosis by calculating the time-constant of the decay in the fluorescence of sypHy during the endocytotic phase (Fig. 1- Fig. Supp. 1C-E). Previous studies have shown that after brief stimulus-trains – like those used in our study (20Hz/300AP) – most endocytosis occurs after the cessation of stimulation 1. Expression of human alpha-synuclein did not alter the endocytosis time-constant in any of our experiments. To summarize, the interaction of alpha-synuclein with the synapsin E domain was required for alpha-synuclein induced attenuation of exocytosis, but not endocytosis.

Reviewer #2

...The paper will be improved significantly if additional experiments are added to expand and provide a more mechanistic understanding of the effect of α-syn and the intricate interplay between synapsin, α-syn, and the SV. For an enthusiastic reader, the manuscript as it looks now with only 3 figures, ends prematurely. Some of the experiments above or others could complement, expand and strengthen the current manuscript, moving it from a short communication describing the phenomenon to a coherent textbook topic. Nevertheless, this work provides new and exciting evidence for the regulation of neurotransmitter release and its regulation by synapsin and α-syn.

(1) Did the authors try to attach E-domain for example to synapsin Ib and restore α-syn inhibition with synapsin Ib-E?

This is an interesting idea, but in previous studies, we found that synapsin Ib does not associate with synaptic vesicles2, so it will not be present at the right location to be able to restore alpha-synuclein induced synaptic attenuation. We have also seen that this mis-localization alters synaptic properties (unpublished).

(2) Was the expression level of Synapsin-IaScrE examined and compared to WT Synapsin-Ia in Fig 3?

Yes, this data is now shown in Fig. 3-Fig. Supp. 1.

(3) Were SVs dispersed in α-syn overexpression as predicted?

We interpret the reviewer’s question and reasoning as follows. If alpha-synuclein binds to the E-domain of synapsin, a prediction in the alpha-synuclein over-expression scenario is that the overabundance of alpha-synuclein molecules would bind to and sequester the E-domain synapsins away from synaptic vesicles. In the absence of E-domain synapsins, the synaptic-vesicle clustering effects of synapsins would be lost, and there would be dispersion of synaptic vesicles. We tested this prediction, which is now shown in an additional figure (new data, Fig. 4). Indeed, the AAV-mediated over-expression of alpha-synuclein leads to a dispersion of synaptic vesicles, and this dispersion is dependent on synapsins Ia and Ib, but not IIa and IIb (please see Fig. 4D-E in the revised manuscript). Appropriate text is also added, starting with “Previous studies have shown that loss of all synapsins...” presents this data and interprets it.

(4) How does this study coincide with the effects of α-syn on fusion pore and endocytosis? This should be at least discussed. It is also possible that the effects of α-syn on endocytosis might affect the results as if endocytosis is affected, SVs number and distribution will be also affected.

It is difficult to reconcile our data with the idea that alpha-synuclein facilitates fusion-pore opening, as proposed by the Edwards lab 3. In fact, its difficult to reconcile this concept with their own previous data, showing that alpha-synuclein over-expression attenuates SV-recycling 4. As mentioned above, modulation of endocytosis does not seem to be a major factor in our experiments, though this does not rule out a physiologic role for alpha-synuclein in endocytosis, since all our experiments are based on over-expression paradigms. Future experiments looking at phenotypes after acute alpha-synuclein knockdown may provide more clarity. In any case, there are many purported roles of alpha-synuclein, and this is now mentioned in the last paragraph (starting with Additionally, -syn has been implicated…”

(5) What happened after stimulation when synapsin is detached from SV, does α-syn continues to be linked to it?

The fate of alpha-synuclein after stimulation is unclear in our experiments. Previous experiments suggest that while both synapsin and alpha-synuclein detach from the SV cluster during stimulation, synapsin returns to synapses while alpha-synuclein does not 5. However, our more recent experiments (unpublished) suggest that the activity-induced dispersion of alpha-synuclein might be phosphorylation-dependent, and that over-expression of alpha-synuclein may not be the best setting to evaluate protein dispersion. We hope to answer this question more rigorously using alpha-synuclein knock-in constructs.

(6) The experiment with E-domain fused to syPhy assumes that α-syn will still be bound to the SV. So how does α-syn inhibit ST?

The goal of this experiment was to force the synapsin E-domain to be in a location where it would normally be present – i.e. surface of the synaptic vesicle – by tagging it to sypHy (sypHy-E), and ask if this forced-retention would be sufficient to reinstate the alpha-synuclein mediated attenuation of SV-recycling (as shown in Fig. 3F, it does). Please note that the sypHy-E in these experiments does target to the synapses (new data, Fig. 3-Fig. Supp. 2D). In this context, we are not sure what the reviewer means by “So how does a-syn inhibit synaptic transmission?” We don’t think that alpha-synuclein needs to unbind from the SVs in order to inhibit synaptic transmission. Overall, we think that alpha-synuclein needs to cooperate with synapsins to perform its function, but as mentioned above and in the manuscript, the precise role of alpha-synuclein in this process is still unclear.

(7) An interesting experiment will be the expression of the isolated E-domain and examining blockage of α-syn inhibition and disruption of synapsin- α-syn interaction. Have the authors examined it as was done in other models?

We did do the experiment where we only over-expressed the isolated synapsin E-domain in neurons. We were thinking that perhaps the E-domain would have a dominant-negative effect on SV-clustering, as it did in the lamprey and other model-systems, where the E-peptide was directly injected into the axon. However, we found that in cultured hippocampal neurons, the over-expressed E-domain behaves like a soluble protein and is not enriched in synapses (see new data, Fig. 3-Fig. Supp. 2B). Also, the over-expressed E-domain cannot reinstate the synaptic attenuation induced by alpha-synuclein (new data, Fig. 3-Fig. Supp. 2C), likely because the E-domain does not target to synapses. Actually, this is why we did the syPhy-E domain experiment in the first place, to ensure that the E-domain was in the right location to have an effect.

(8) A schematic model/scheme providing a mechanistic view of the interplay between the proteins is essential and can improve the paper.

The only model we can confidently make right now would be stick-figures showing the site where alpha-synuclein C-terminus binds to synapsin, which is obviously not very insightful. As noted above (and in the revised version), several different functions have been attributed to alpha-synuclein, and the precise role of alpha-synuclein/synapsin interactions in regulating the SV-cycle is unclear. We hope to create a better model after getting some more data from us and our colleagues working on this challenging problem.

References

(1) Kononenko NL & Haucke V. (2015) Molecular mechanisms of presynaptic membrane retrieval and synaptic vesicle reformation. Neuron 85, 484-496.

(2) Gitler D, Xu Y, Kao H-T, Lin D, Lim S, Feng J, Greengard P & Augustine GJ. (2004) Molecular Determinants of Synapsin Targeting to Presynaptic Terminals. J. Neurosci. 24, 3711-3720.

(3) Logan T, Bendor J, Toupin C, Thorn K & Edwards RH. (2017) α-Synuclein promotes dilation of the exocytotic fusion pore. Nat Neurosci 20, 681-689.

(4) Nemani VM, Lu W, Berge V, Nakamura K, Onoa B, Lee MK, Chaudhry FA, Nicoll RA & Edwards RH. (2010) Increased expression of alpha-synuclein reduces neurotransmitter release by inhibiting synaptic vesicle reclustering after endocytosis. Neuron 65, 66-79.

(5) Fortin DL, Nemani VM, Voglmaier SM, Anthony MD, Ryan TA & Edwards RH. (2005) Neural activity controls the synaptic accumulation of alpha-synuclein. J Neurosci 25, 10913-10921.

Author Response

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

Reviewer 1: I would have preferred to see more figures with brain images showing the cellular abundance maps and the atrophy maps. Without being able to see these figures, it's difficult for the reader to 1) validate the atrophy patterns or 2) gain intuition about how the cellular abundance maps vary across the brain. The images in Figure 1C give a small preview, but I'd like to see these maps in their entirety on the brain surface or axial image slices.

(1) We added brain surface visualization plots of the voxel-wise cellular abundance maps to Figure 1 (lateral, dorsal, and ventral views of both hemispheres). To illustrate how their spatial distributions are associated with brain tissue damage, in Figure 2, we have also added brain surface visualizations of regional values from the atrophy t-statistic maps for the thirteen neurodegenerative conditions and the cell-type map most strongly associated with each condition. These plots allow us to observe variability across the cell-type density and atrophy maps, as well as to visually validate and compare how the patterns vary across the brain.

Reviewer 1: FTD is an umbrella category for a family of distinct clinical syndromes with different atrophy patterns. It doesn't seem a good idea to take the average of all subjects in this group to form a single atrophy map. Instead, different average maps for each syndrome should be provided.

(2) Considering the heterogeneity of clinical FTD syndromes, we addressed the reviewers' concerns about using the averaged atrophy map across all patients with an FTD diagnosis. As suggested, we accessed different atrophy maps for each major variant of clinical FTD, including behavioral FTD (n = 70), as well as the semantic (n = 36) and nonfluent variants of primary progressive aphasia (n = 30). These maps are based on data from the participants from the same dataset of the Frontotemporal Lobar Degeneration Neuroimaging Initiative (FTLDNI) that we originally used. Similar to our previous results using the atrophy map averaged over all FTD patients, the analysis showed significant associations of atrophy patterns with cell type densities in all three major variants (see Figure 3A). Notably, these new findings offer insights into specific differences in spatial vulnerability of different cell-types across the variants of FTD, each characterized by unique symptoms, clinical manifestations, and atrophy patterns. In response to these additions, we have updated all figures, results, and interpretations accordingly.

Reviewer 2: In the abstract, the list of neurodegenerative disorders should be edited: frontotemporal dementia is an umbrella clinical syndrome, not a neurodegenerative disorder. Frontotemporal lobar degeneration (FTLD) is a neurodegenerative disorder, and many tauopathies are FTLDs. While the authors grab their definitional classes from various sources (i.e., published cohort, and other studies), the reader fatigues to understand the population that is being assessed.

(3) To address potential confusion arising from the inclusion of atrophy maps from FTLD patients across two different studies, stratified based on both clinical and pathological criteria, we added clarifications regarding the assessed population and the used definitions. We used the term FTD when addressing the clinical syndromes, and the term FTLD was employed when referencing the histologically confirmed neurodegenerative pathologies. In addition, we added details on the diagnostic criteria employed for participant recruitment in the FTLDNI cohort, which data we used for atrophy maps in clinical subtypes of FTD. Lastly, throughout the text and within the figures, we systematically refined the nomenclature for FTLD pathological types, categorizing them based on their known definitions used in literature and type of proteinaceous inclusions (FTLD- 3-repeat and 4-repeat tauopathies and FTLD-TDP types A and C).

Reviewer 1: The results section contains perhaps too much interpretation. While the information that's provided serves as an interesting review (e.g., the discussion of the blood-brain barrier), the discussion may be a better place for this.

(4) We removed sentences with excessive interpretation but insisted on including those outlining the fundamental functions of cell types and their literature-based relevance to neurodegenerative diseases in the Results section, clarifying the significance of our findings to the readers.

Reviewer 2: The authors based their methodology on the use of a deconvolutional cell classifier; however, do not extensively recognize that their data on gene expression are based on normal brain levels rather than on diseased ones.

(5) We acknowledged that the gene expression data is based on normal human brain levels in figure titles and all sections of the paper (Introduction, Results, Discussion, Methods) to remind the readers that the analysis shows how changes in gray matter tissue in diseased brains correlates with healthy reference levels of cellular density.

Reviewer 2: More information in the text needs to be provided regarding the method used to infer gene expression levels at non-sampled brain locations. The reader should not be forced to read reference 40 or investigate the methods section. Figure 1 schematics do not sufficiently explain the used method.

(6) We added clarifications/references about the used Gaussian progress regression for imputing gene expression (Results and figure titles).

Reviewer 2: Also, while predicted levels are uniquely based on patterns of brain atrophy, it is not possible to know whether this strategy is generalizable to all diseases (for instance, it is known that pure DLB, PD and ALS are not associated with extensive brain atrophy), or even adequately comparable between subtypes of diseases within the same class (e.g., different forms of FTLD). The authors do not acknowledge that only data based on true neuropathological assessment may prove whether their findings are true.

(7) Although diagnoses of most dementia conditions used in our study were histologically confirmed, we added acknowledgement about the importance of neuropathological assessment (Discussion section).

Author Response

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

eLife assessment

This important work identifies a previously uncharacterized capacity for songbirds to recover vocal targets even without sensory experience. While the evidence supporting this claim is solid, with innovative experiments exploring vocal plasticity in deafened birds, additional behavioral controls and analyses are necessary to shore up the main claims. If improved, this work has the potential for broad relevance to the fields of vocal and motor learning.

We were able to address the requests for additional behavioral controls about the balancing of the groups (reviewer 1) and the few individual birds that showed a different behavior (reviewer 2) without collecting any further data. See our detailed replies below.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

Zai et al test if songbirds can recover the capacity to sing auditory targets without singing experience or sensory feedback. Past work showed that after the pitch of targeted song syllables is driven outside of birds' preferred target range with external reinforcement, birds revert to baseline (i.e. restore their song to their target). Here the authors tested the extent to which this restoration occurs in muted or deafened birds. If these birds can restore, this would suggest an internal model that allows for sensory-to-motor mapping. If they cannot, this would suggest that learning relies entirely on feedback-dependent mechanisms, e.g. reinforcement learning (RL). The authors find that deafened birds exhibit moderate but significant restoration, consistent with the existence of a previously under-appreciated internal model in songbirds.

Strengths:

The experimental approach of studying vocal plasticity in deafened or muted birds is innovative, technically difficult, and perfectly suited for the question of feedback-independent learning. The finding in Figure 4 that deafened birds exhibit subtle but significant plasticity toward restoration of their pre-deafening target is surprising and important for the songbird and vocal learning fields, in general.

Weaknesses:

The evidence and analyses related to the directed plasticity in deafened birds are confusing, and the magnitude of the plasticity is far less than the plasticity observed in control birds with intact feedback. The authors acknowledge this difference in a two-system model of vocal plasticity, but one wonders why the feedback-independent model, which could powerfully enhance learning speed, is weak in this songbird system.

We fully agree with the reviewer. This surprising weakness applies to birds’ inability rather than our approach for characterizing it.

There remains some confusion about the precise pitch-change methods used to study the deafened birds, including the possibility that a critical cohort of birds was not suitably balanced in a way where deafened birds were tested on their ability to implement both pitch increases and decreases toward target restoration.

Both deaf groups were balanced: (dLO and WNd) were balanced in that half of the birds (5/10 WNm and 4/8 dLO) shifted their pitch up (thus target restoration corresponded to decreasing pitch) and half of the birds (5/10 WNd and 4/8 dLO) shifted their pitch down (thus target restoration corresponded to increasing pitch), see Methods.

To clarify the precise pitch-change method used, we added to the methods an explanation about why we used the sensitivity index 𝒅′ in Fig. 4:

We used sensitivity 𝒅′ relative to the last 2 h of WN/LO instead of NRP because we wanted to detect a pitch change, which is the realm of detection theory, i.e. 𝒅′. Furthermore, by measuring local changes in pitch relative to the last 2 h of WN/LO reinforcement, our measurements are only minimally affected by the amount of reinforcement learning that might have occurred during this 2 h time window — choosing an earlier or longer window would have blended reinforced pitch changes into our estimates. Last but not least, changes in the way in which we normalized 𝒅’ values — dividing by 𝑺𝑩, — or using the NRP relative to the last 2 h of WN/LO did not qualitatively change the results shown in Fig. 4D.

Reviewer #2 (Public Review):

Summary:

This paper investigates the role of motor practice and sensory feedback when a motor action returns to a learned or established baseline. Adult male zebra finches perform a stereotyped, learned vocalization (song). It is possible to shift the pitch of particular syllables away from the learned baseline pitch using contingent white noise reinforcement. When the reinforcement is stopped, birds will return to their baseline over time. During the return, they often sing hundreds of renditions of the song. However, whether motor action, sensory feedback, or both during singing is necessary to return to baseline is unknown.

Previous work has shown that there is covert learning of the pitch shift. If the output of a song plasticity pathway is blocked during learning, there is no change in pitch during the training. However, as soon as the pathway is unblocked, the pitch immediately shifts to the target location, implying that there is learning of the shift even without performance. Here, they ask whether the return to baseline from such a pitch shift also involves covert or overt learning processes. They perform a series of studies to address these questions, using muting and deafening of birds at different time points. learning.

Strengths:

The overall premise is interesting and the use of muting and deafening to manipulate different aspects of motor practice vs. sensory feedback is a solid approach.

Weaknesses:

One of the main conclusions, which stems primarily from birds deafened after being pitch-shifted using white noise (WNd) birds in comparison to birds deafened before being pitchshifted with light as a reinforcer (LOd), is that recent auditory experience can drive motor plasticity even when an individual is deprived of such experience. While the lack of shift back to baseline pitch in the LOd birds is convincing, the main conclusion hinges on the responses of just a few WNd individuals who are closer to baseline in the early period. Moreover, only 2 WNd individuals reached baseline in the late period, though neither of these were individuals who were closer to baseline in the early phase. Most individuals remain or return toward the reinforced pitch. These data highlight that while it may be possible for previous auditory experience during reinforcement to drive motor plasticity, the effect is very limited. Importantly, it's not clear if there are other explanations for the changes in these birds, for example, whether there are differences in the number of renditions performed or changes to other aspects of syllable structure that could influence measurements of pitch.

We thank the reviewer for these detailed observations. We looked into the reviewer’s claim that our main conclusion of revertive pitch changes in deaf birds with target mismatch experience hinges on only few WNd birds in the early period.

When we remove the three birds that were close to baseline (NRP=0) in the early period, we still get the same trend that WNd birds show revertive changes towards baseline: Early 𝒅’ = −𝟎. 𝟏𝟑, 𝒑 = 𝟎. 𝟐𝟒, tstat = −𝟎.𝟕𝟒, 𝒅𝒇 = 𝟔, 𝑵 = 𝟕 birds, one-sided t-test of H0: 𝒅′ = 𝟎; Late 𝒅’ = −𝟏. 𝟐𝟔, 𝒑 = 𝟎. 𝟎𝟖, tstat = −𝟏.𝟔𝟑, 𝒅𝒇 = 𝟔, 𝑵 = 𝟕 birds, one-sided t-test of H0: 𝒅′ = 𝟎. Furthermore, even without these three birds, bootstrapping the difference between WNd and dC birds shows the same trend in the early period (p=0.22) and a significant reversion in the late period (p<0.001). Thus, the effect of reversion towards baseline in the late period is robustly observed on a population level, even when discounting for three individual birds that the reviewer suspected would be responsible for the effect.

Moreover, note that there are not two but three WNd individuals that reached baseline in the late period (see Figure 2C, D). One of them was already close to baseline in the early period and another one was already relatively close, too.

Also, the considerable variability among birds is not surprising, it is to be expected that the variability across deaf birds is large because of their ongoing song degradation that might lead to a drift of pitch over time since deafening.

Last but not least, see also our multivariate model (below).

With regards to the “differences in the number of renditions” that could explain pitch changes: Deaf birds sing less after deafening than hearing birds: they sing less during the first 2 hours (early): 87±59 renditions (WNd) and 410±330 renditions (dLO) compared to 616±272 renditions (control birds). Also, WN deaf birds sing only 4300±2300 motif renditions between the early and late period compared to the average of 11000±3400 renditions that hearing control birds produce in the same time period. However, despite these differences, when we provide WNd birds more time to recover, namely 9 days after the early period, they sung on average 12000±6000 renditions, yet their NRP was still significantly different from zero (NRP = 0.37, p=0.007, tstat=3.47, df=9). Thus, even after producing more practice songs, deaf birds do not recover baseline pitch and so the number of songs alone cannot explain why deaf birds do not fully recover pitch. We conclude that auditory experience seems to be necessary to recover song.

We added this information to the Results.

In this context, note that the interesting part of our work is not that deaf birds do not fully recover, but that they recover anything at all (“main conclusion”, Fig. 4). The number of songs does not explain why deaf birds with mismatch experience (WNd, singing the least and singing significantly less than control birds, p=2.3*10-6, two-tailed t-test) partially revert song towards baseline, unlike deaf birds without mismatch experience (dLO, singing significantly more than WNd birds, p=0.008, and indistinguishable from control birds, p=0.1). We added this information to the Results section.

With regards to ‘other aspects of syllable structure’: We did not look into this. Regardless of the outcome of such a hypothetical analysis, whether other syllable features change is irrelevant for our finding that deaf birds do not recover their target song. Nevertheless, note that in Zai et al. 2020 (supplementary Figure 1), we analyzed features other than pitch change in deaf birds. Absolute change in entropy variance was larger in deaf birds than in hearing birds, consistent with the literature on song degradation after deafening (Lombardino and Nottebohm, 2000, Nordeen and Nordeen 2010 and many others). In that paper, we found that only pitch changes consistently along the LO direction. All other features that we looked at (duration, AM, FM and entropy) did not change consistently with the LO contingency. We expect that a similar result would apply for the changes across the recovery period in WNd and dLO birds, i.e., that song degradation can be seen in many features and that pitch is the sole feature that changes consistently with reinforcement (LO/WN) direction.

While there are examples where the authors perform direct comparisons between particular manipulations and the controls, many of the statistical analyses test whether each group is above or below a threshold (e.g. baseline) separately and then make qualitative comparisons between those groups. Given the variation within the manipulated groups, it seems especially important to determine not just whether these are different from the threshold, but how they compare to the controls. In particular, a full model with time (early, late), treatment (deafened, muted, etc), and individual ID (random variable) would substantially strengthen the analysis.

We performed a full model of the NRP as the reviewer suggests and it supports our conclusions: Neither muting, deafening nor time without practice between R and E windows have a significant effect on pitch in the E window, but the interaction between deafening and time (late, L) results in a significant pitch change (fixed effect 0.67, p=2*10-6), demonstrating that deaf birds are significantly further away from baseline (NRP=0) than hearing birds in late windows, thereby confirming that birds require auditory feedback to recover a distant pitch target. Importantly, we find a significant fixed effect on pitch in the direction of the target with mismatch experience (fixed effect -0.37, p=0.006), supporting our finding that limited vocal plasticity towards a target is possible even without auditory feedback.

We included this model as additional analysis to our manuscript.

The muted birds seem to take longer to return to baseline than controls even after they are unmuted. Presumably, there is some time required to recover from surgery, however, it's unclear whether muting has longer-term effects on syrinx function or the ability to pass air. In particular, it's possible that the birds still haven't recovered by 4 days after unmuting as a consequence of the muting and unmuting procedure or that the lack of recovery is indicative of an additional effect that muting has on pitch recovery. For example, the methods state that muted birds perform some quiet vocalizations. However, if birds also attempt to sing, but just do so silently, perhaps the aberrant somatosensory or other input from singing while muted has additional effects on the ability to regain pitch. It would also be useful to know if there is a relationship between how long they are muted and how quickly they return to baseline.

We agree, it might be the case that muting has some longer-term effects that could explain why WNm birds did not recover pitch 4 days after unmuting. However, if such an effect exists, it is only weak. Arguing against the idea that a longer muting requires longer recovery, we did not find a correlation between the difference in NRP between early and late and 1. the duration the birds were muted (correlation coefficient = -0.50, p=0.20), and 2. the number of renditions the birds sung between early and late (correlation coefficient = 0.03, p=0.95), and 3. the time since they last sung the target song (last rendition of baseline, correlation coefficient = -0.43, p=0.29). Neither did we find a correlation between the early NRP and the time since the muting surgery (correlation coefficient = 0.26, p=0.53), suggesting that the lack of pitch recovery while muted was not due to a lingering burden of the muting surgery. We added these results to the results section.

In summary, we used the WNm group to assess whether birds can recover their target pitch in the absence of practice, i.e. whether they recovered pitch in the early time period. Whether or not some long-term effect of the muting/unmuting procedure affects recovery does not impair the main finding we obtained from WNm birds in Figure 1 (that birds do not recover without practice).

Reviewer #3 (Public Review):

Summary:

Zai et al. test whether birds can modify their vocal behavior in a manner consistent with planning. They point out that while some animals are known to be capable of volitional control of vocalizations, it has been unclear if animals are capable of planning vocalizations -that is, modifying vocalizations towards a desired target without the need to learn this modification by practicing and comparing sensory feedback of practiced behavior to the behavioral target. They study zebra finches that have been trained to shift the pitch of song syllables away from their baseline values. It is known that once this training ends, zebra finches have a drive to modify pitch so that it is restored back to its baseline value. They take advantage of this drive to ask whether birds can implement this targeted pitch modification in a manner that looks like planning, by comparing the time course and magnitude of pitch modification in separate groups of birds who have undergone different manipulations of sensory and motor capabilities. A key finding is that birds who are deafened immediately before the onset of this pitch restoration paradigm, but after they have been shifted away from baseline, are able to shift pitch partially back towards their baseline target. In other words, this targeted pitch shift occurs even when birds don't have access to auditory feedback, which argues that this shift is not due to reinforcement-learning-guided practice, but is instead planned based on the difference between an internal representation of the target (baseline pitch) and current behavior (pitch the bird was singing immediately before deafening).

The authors present additional behavioral studies arguing that this pitch shift requires auditory experience of the song in its state after it has been shifted away from baseline (birds deafened early on, before the initial pitch shift away from baseline, do not exhibit any shift back towards baseline), and that a full shift back to baseline requires auditory feedback. The authors synthesize these results to argue that different mechanisms operate for small shifts (planning, does not need auditory feedback) and large shifts (reinforcement learning, requires auditory feedback).

We thank the reviewer for this concise summary of our paper. To clarify, we want to point out that we do not make any statement about the learning mechanism birds use to make large shifts to recover their target pitch, i.e. we do not say that large shifts are learned by reinforcement learning requiring auditory feedback. We only show that large shifts require auditory feedback.

The authors also make a distinction between two kinds of planning: covert-not requiring any motor practice and overt-requiring motor practice but without access to auditory experience from which target mismatch could be computed. They argue that birds plan overtly, based on these deafening experiments as well as an analogous experiment involving temporary muting, which suggests that indeed motor practice is required for pitch shifts.

Strengths:

The primary finding (that partially restorative pitch shift occurs even after deafening) rests on strong behavioral evidence. It is less clear to what extent this shift requires practice, since their analysis of pitch after deafening takes the average over within the first two hours of singing. If this shift is already evident in the first few renditions then this would be evidence for covert planning. This analysis might not be feasible without a larger dataset. Similarly, the authors could test whether the first few renditions after recovery from muting already exhibit a shift back toward baseline.

This work will be a valuable addition to others studying birdsong learning and its neural mechanisms. It documents features of birdsong plasticity that are unexpected in standard models of birdsong learning based on reinforcement and are consistent with an additional, perhaps more cognitive, mechanism involving planning. As the authors point out, perhaps this framework offers a reinterpretation of the neural mechanisms underlying a prior finding of covert pitch learning in songbirds (Charlesworth et al., 2012).

A strength of this work is the variety and detail in its behavioral studies, combined with sensory and motor manipulations, which on their own form a rich set of observations that are useful behavioral constraints on future studies.

Weaknesses:

The argument that pitch modification in deafened birds requires some experience hearing their song in its shifted state prior to deafening (Fig. 4) is solid but has an important caveat. Their argument rests on comparing two experimental conditions: one with and one without auditory experience of shifted pitch. However, these conditions also differ in the pitch training paradigm: the "with experience" condition was performed using white noise training, while the "without experience" condition used "lights off" training (Fig. 4A). It is possible that the differences in the ability for these two groups to restore pitch to baseline reflect the training paradigm, not whether subjects had auditory experience of the pitch shift. Ideally, a control study would use one of the training paradigms for both conditions, which would be "lights off" or electrical stimulation (McGregor et al. 2022), since WN training cannot be performed in deafened birds. This is difficult, in part because the authors previously showed that "lights off" training has different valences for deafened vs. hearing birds (Zai et al. 2020). Realistically, this would be a point to add to in discussion rather than a new experiment.

We added the following statement to our manuscript:

It is unlikely that dLO birds’ inability to recover baseline pitch is somehow due to our use of a reinforcer of a non-auditory (visual) modality, since somatosensory stimuli do not prevent reliable target pitch recovery in hearing birds (McGregor et al 2022).

A minor caveat, perhaps worth noting in the discussion, is that this partial pitch shift after deafening could potentially be attributed to the birds "gaining access to some pitch information via somatosensory stretch and vibration receptors and/or air pressure sensing", as the authors acknowledge earlier in the paper. This does not strongly detract from their findings as it does not explain why they found a difference between the "mismatch experience" and "no mismatch experience groups" (Fig. 4).

We added the following statement: Our insights were gained in deaf birds and we cannot rule out that deaf birds could gain access to pitch information via somatosensoryproprioceptive sensory modalities. However, such information, even if available, cannot explain the difference between the "mismatch experience” (WNd) and the "no mismatch experience" (dLO) groups, which strengthens our claim that the pitch reversion we observe is a planned change and not merely a rigid motor response (as in simple usedependent forgetting).

More broadly, it is not clear to me what kind of planning these birds are doing, or even whether the "overt planning" here is consistent with "planning" as usually implied in the literature, which in many cases really means covert planning. The idea of using internal models to compute motor output indeed is planning, but why would this not occur immediately (or in a few renditions), instead of taking tens to hundreds of renditions?

Indeed, what we call ‘covert planning’ refers to what usually is called ‘planning’ in the literature. Also, there seems to be currently no evidence for spontaneous overt planning in songbirds (which we elicited with deafening). Replay of song-like syringeal muscle activity can be induced by auditory stimuli during sleep (Bush, A., Doppler, J. F., Goller, F., and Mindlin, G. B. (2018), but to our knowledge there are no reports of similar replay in awake, non-singing birds, which would constitute evidence for overt planning.

We cannot ascertain how fast birds can plan their song changes, but our findings are not in disagreement with fast planning. The smallest time window of analysis we chose is 2h, which sets a lower bound of the time frame within which we can measure pitch changes. Our approach is probably not ideally suited for determining the minimal planning time, because the deafening and muting procedures cause an increase in song variability, which calls for larger pitch sample sizes for statistical testing, and the surgeries themselves cause a prolonged period without singing during which we have no access to the birds’ planned motor output. Note that fast planning is demonstrated by the recent finding of instant imitation in nightingales (Costalunga, Giacomo, et al. 2023) and is evidenced by fast re-pitching upon context changes in Bengalese finches (Veit, L., Tian, L. Y., Monroy Hernandez, C. J., & Brainard, M. S., 2021).

To resolve confusion, it would be useful to discuss and add references relating "overt" planning to the broader literature on planning, including in the introduction when the concept is introduced.

Overt and covert planning are terms used in the literature on child development and on adult learning, see (Zajic, Matthew Carl, et al., Overt planning behaviors during writing in school-age children with autism spectrum disorder and attention-deficit/hyperactivity disorder, 2020) and (Abbas zare-ee, Researching Aptitude in a Process-Based Approach to Foreign Language Writing Instruction. Advances in Language and Literary Studies, 2014), and references therein.

Indeed, muddying the interpretation of this behavior as planning is that there are other explanations for the findings, such as use-dependent forgetting, which the authors acknowledge in the introduction, but don't clearly revisit as a possible explanation of their results. Perhaps this is because the authors equate use-dependent forgetting and overt planning, in which case this could be stated more clearly in the introduction or discussion.

We do not mean to strictly equate use-dependent forgetting and overt planning, although they can be related, namely when ‘use’ refers to ‘altered use’ as is the case when something about the behavior is missing (e.g. auditory feedback in our study), and the dependence is not just on ‘use’ but also on ‘experience’.

We added the following sentence to the discussion: We cannot distinguish the overt planning we find from more complex use-and-experience dependent forgetting, since we only probed for recovery of pitch and did not attempt to push birds into planning pitch shifts further away from baseline.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

(1) The single main issue with this paper is in the section related to Figure 4, and the Figure itself - this is the most important part of the paper essential to buttress the claim of covert learning. However, there are several sources of confusion in the text, analyses, and figures. The key result is in Figure 4B, C - and, in the context of Figs 1-3, the data are significant but subtle. That is, as the authors state, the birds are mostly dependent on slow sensory feedback-dependent (possibly RL) mechanisms but there is a small component of target matching that evidences an internal model. One wonders why this capacity is so small - if they had a good internal model they'd be much faster and better at recovering target pitches after distortion-driven deviations even without sensory feedback.

(1a) The analysis of the WNd and DLO reversions of pitch (related to Fig. 4) uses a d' analysis which is a pivot from the NRP analysis used in the rest of the paper. It is not clear why different analyses are being used here to compute essentially the same measure, i.e. how much did the pitch revert. It's also odd that different results are now obtained - Fig. 4 has a small but significant reversion of pitch in WNd birds but Fig. 2 shows no significant return to baseline.

We did not test for reversion towards baseline in Fig. 2 and made no statement about whether there is a significant reversion or not. But when we do such a test, we find a significant reversion for WNd birds in the ‘late’ window (NRP=0.5, p=0.02, N=10, tstat=-1.77, two-tailed t-test), which agrees with Figure 4. In the ‘early’ window in Fig. 2, we find only a trend but no reversion (NRP = 0.76, p=0.11, n=10, tstat=-1.76), which contrasts with our findings in Figure 4. However, the discrepancy can be simply explained by the difference in time alignment that we detail in the Materials and Methods. Namely, in Figure 2, we measure pitch relative to the pitch in the morning on the day before, which is not a good measure of ‘reversion’ (since pitch had been reinforced further away during the day), which is why we do not present this analysis in the paper and dedicate a separate analysis in Figure 4 to reversion.

(1b) Also in Fig. 4 is it the case that, as in the schematic of 4a, ALL birds in these experiments had their pitch pushed up - so that the return to baseline was all down? If this is the case the analysis may be contaminated by a pitch-down bias in deafened birds. This would ideally be tested with a balance of pitch-up and pitch-down birds in the pre-deafening period, and/or analysis of non-targeted harmonic stacks to examine their pitch changes. If non-targeted stacks exhibit pitch-down changes after deafening, then the reversion that forms the key discovery of this paper will be undermined. Please address.

Both groups in Figure 4 were balanced (same number of birds were shifted their pitch up and down), see response to public review and Methods.

(1c) After multiple re-reads and consultations with the Methods section I still do not understand the motivation or result for Figure 4E. Please provide clarification of the hypothesis/control being assessed and the outcome.

Figure 4E does not add an additional result but strengthens our previous findings because we obtain the same result with a different method. The pitch of deaf birds tends to drift after deafening. To discount for this drift and the effect of time elapsed since deafening, we bootstrapped the magnitude of the pitch change in WNd and dLO birds by comparing them to dC birds in matched time windows. We modified the sentence in the results section to clarify this point:

To discount for the effect of time elapsed since deafening and quantify the change in pitch specifically due to reinforcement, we bootstrapped the difference in 𝒅′ between dLO/WNd birds and a new group of dC birds that were deafened but experienced no prior reinforcement (see methods).

(1d) Line 215. It's not clear in the text here how the WNd birds experience a pitch mismatch. Please clarify the text that this mismatch was experienced before deafening. This is a critical paragraph to set up the main claims of the paper. Also, it's not clear what is meant by 'fuel their plan'? I can imagine this would simply be a DA-dependent plasticity process in Area X that does not fuel a plan but rather re-wires and HVC timestep to medium spiny neurons whose outputs drive pitch changes - i.e. not a fueled plan but simply an RL-dependent re-mapping in the motor system. Alternatively, a change could result in plasticity in pallial circuits (e.g. auditory to HVC mappings) that are RL independent and invoke an inverse model along the lines of the author's past work (e.g. Ganguli and Hahnlsoer). This issue is taken up in the discussion but the setup here in the results is very confusing about the possible outcomes. This paragraph is vague with respect to the key hypotheses. It's possible that the WNd and DLO groups enable dissection of the two hypotheses above - because the DLO groups would presumably have RL signals but without recovery - but there remains a real lack of clarity over exactly how the authors are interpreting Fig 4 at the mechanistic level.

WNd birds experience a pitch mismatch because while singing they hear that their pitch differs from baseline pitch, but the same is not true for dLO birds. We simply tested whether this experience makes a difference for reversion and it does. We added ‘before deafening’ to the paragraph and changed the wording of our hypothesis to make it clearer (we reworded ‘fuel their plan’). Mechanistic interpretations we left in the discussion. Without going to details, all we are saying is that birds can only plan to revert motor changes they are aware of in the first place.

Minor issues

The songs of deafened birds degrade, at a rate that depends on the bird's age. Younger crystalized birds degrade much faster, presumably because of lower testosterone levels that are associated with increased plasticity and LMAN function. Some background is needed on deafened birds to set up the WNd experiments.

Despite deafening leading to the degradation of song (Lombardino and Nottebohm, 2000), syllable detection and pitch calculation were still possible in all deaf birds (up to 13-50 days after deafening surgery, age range 90-300 dph, n=44 birds).

Since pitch shifting was balanced in both deaf bird groups (the same number of birds were up- and down-shifted), systematic changes in pitch post deafening (Lombardino and Nottebohm, 2000) will average out and so would not affect our findings.

Lines 97-103. The paragraph is unclear and perhaps a call to a SupFig to show the lack of recovery would help. If I understand correctly, the first two birds did not exhibit the normal recovery to baseline if they did not have an opportunity to hear themselves sing without the WN. I am failing to understand this.

In the early window (first 2 hours after unmuting) birds have not changed their pitch compared to their pitch in the corresponding window at the end of reinforcement (with matching time-of-day). We added ‘immediately after unmuting (early)’ to clarify this statement.

Lines 68-69. What is the difference between (2) and (3)? Both require sensory representation/target to be mapped to vocal motor output. Please clarify or fuse these concepts.

We fused the concept and changed the figure and explanation accordingly.

Line 100. Please name the figure to support the claim.

We marked the two birds in the Fig. 1H and added a reference in the text.

Line 109. Is there a way to confirm / test if muted birds attempted to sing?

Unfortunately, we do not have video recordings to check if there are any signs of singing attempts in muted birds.

Line 296: Why 'hierarchically 'lower'?

Lower because without it there is nothing to consolidate, i.e. the higher process can only be effective after the lower but not before. We clarified this point in the text.

Past work on temporal - CAF (tcaf) by the Olveczky group showed that syllable durations and gaps could be reinforced in a way that does not depend on Area X and, therefore, related to the authors' discussion on the possible mechanisms of sensory-feedback independent recovery, may rely on the same neural substrates that Fig. 4 WNd group uses to recover. Yet the authors find in this paper that tCAF birds did not recover. There seems to be an oddity here - if covert recovery relies on circuits outside the basal ganglia and RL mechanisms, wouldn't t-CAF birds be more likely to recover? This is not a major issue but is a source of confusion related to the authors' interpretations that could be fleshed out.

This is a good point, we reinvestigated the tCAF birds in the context of Fig 4 where we looked for pitch reversions towards baseline. tCAF birds do also revert towards baseline. We added this information to the supplement. We cannot say anything about the mechanistic reasons for lack of recovery, especially given that we did not look at brain-level mechanisms.

Reviewer #2 (Recommendations For The Authors):

The data presentation could be improved. It is difficult to distinguish between the early and late symbols and to distinguish between the colors for the individual lines on the plots or to match them with the points on the group data plots. In addition, because presumably, the points in plots like 2D are for the same individuals, lines connecting those points would be useful rather than trying to figure out which points are the same color.

We added lines in Fig. 2D connecting the birds in early and late.

The model illustrations (Fig 1A, Fig 5) are not intuitive and do not help to clarify the different hypotheses or ideas. I think these need to be reworked.

We revised the model illustrations and hope they improved to clarify the different hypothesis.

Some of the phrasing is confusing. Especially lines 157-158 and 256-257.

Lines 157-158: we removed an instance of ‘WNd’, which was out of place.

Lines 256-257: we rephrased to ‘showing that prior experience of a target mismatch is necessary for pitch reversion independently of auditory feedback’

Reviewer #3 (Recommendations For The Authors):

For Fig. 1, the conclusion in the text "Overall, these findings suggest that either motor practice, sensory feedback, or both, are necessary for the recovery of baseline song" is not aligned with the figure header "Recovery of pitch target requires practice".

We rephrased the conclusion to: Overall, these findings rule out covert planning in muted birds and suggest that motor practice is necessary for recovery of baseline song.

The use of the term "song experience" can be confusing as to whether it means motor or auditory experience. Perhaps replace it with "singing experience" or "auditory experience" where appropriate.

We did the requested changes.

Fig. 1A, and related text, reads as three hypotheses that the authors will test in the paper, but I don't think this turns out to the be the main goal (and if it is, it is not clear their results differentiate between hypotheses 1, 2, and 3). Perhaps reframe as discussion points and have this panel not be so prominent at the start, just to avoid this confusion.

We modified the illustration in Fig 1A and simplified it. We now only show the 2 hypotheses that we test in the paper.

Line 275-276, "preceding few hours necessitates auditory feedback, which sets a limit to zebra finches' covert planning ability". Did the authors mean "overt", not covert? Since their study focuses on overt planning.

Our study focuses on covert planning in figure 1 and overt planning in subsequent figures.

The purpose of the paragraph starting on line 278 could be more clear. Is the goal to say that overt planning and what has previously been described as use-dependent forgetting are actually the same thing? If not, what is the relationship between overt planning and forgetting? In other words, why should I care about prior work on use-dependent forgetting?

We moved the paragraph further down where it does not interrupt the narrative. See also our reply to reviewer 3 on use-dependent forgetting.

Line 294, "...a dependent process enabled by experience of the former...", was not clear what "former" is referring to. In general, this paragraph was difficult to understand. Line 296: Which is the "lower" process?

We added explanatory parentheses in the text to clarify. We rephrased the sentence to ‘the hierarchically lower process of acquisition or planning as we find is independent of immediate sensory experience.’

Line 295, the reference to "acquisition" vs. "retention". It is not clear how these two concepts relate to the behavior in this study, and/or the hierarchical processes referenced in the previous sentence. Overall, it is not clear how consolidation is related to the paper's findings.

We added explanatory parentheses in the text and changed figure 5 to better explain the links.

Line 305, add a reference to Warren et al. 2011, which I believe was the first study (or one of them) that showed that AFP bias is required for restoring pitch to baseline.

We are citing Warren et al. 2011 in the sentence:

Such separation also applies to songbirds. Both reinforcement learning of pitch and recovery of the original pitch baseline depend on the anterior forebrain pathway and its output, the lateral magnocellular nucleus of the anterior nidopallium (LMAN)(1).

Line 310, "Because LMAN seems capable of executing a motor plan without sensory feedback", is this inferred from this paper (in which case this is an overreach) or is this referencing prior work (if so, which one, and please cite)?

We changed the wording to ‘It remains to be seen whether LMAN is capable of executing a motor plans without sensory feedback’.

Line 326, "which makes them well suited for planning song in a manner congruent with experience." I don't fully understand the logic. Can this sentence be clarified?

We rephrased the sentence and added an explanation as follows: …which makes them well suited for executing song plans within the range of recent experience (i.e., if the song is outside recent experience, it elicits no LMAN response and so does not gain access to planning circuits).

Author Response

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

Reviewer 1

One criticism the authors have made of previous studies was that they have not distinguished between 'tonic' and 'phasic' LC activity and could not demonstrate 'time- locked phasic firing'. This has not been achieved in the present report, as an examination of Fig 1 C,D and 2 C,D shows. Previous reports in rats and monkeys, using unit recording in rats and monkeys clearly show that the latency of LC 'phasic' responses to salient or behaviorally relevant stimuli are in the range of tens of milliseconds, with a very short duration, often followed by a long-lasting inhibition. This kind of temporal precision concerning the phasic response cannot be gleaned from the time scale shown in the Figures (assuming the time scale is in seconds). We can discern a long-lasting increase in tonic firing level for the more salient stimuli (Fig 1C) (although the authors state in the discussion that "we did not observe obvious changes in tonic LC-HPC activity). This calcium imaging methodology as used in the present experiments can give us a general idea of the temporal relation of LC response to the stimulus, but apparently does not afford the millisecond resolution necessary to capture a phasic response, at least as the data are presented in the Figures.

While we understand the reviewer’s concern with our use of the terms phasic and tonic, we believe we have represented them as accurately as possible given our data. Unfortunately, the distinction between tonic and phasic activity is somewhat arbitrary, in that there is no strict definition, to our knowledge, of the exact parameters that activity must fall into to be categorized as tonic or phasic. While it is true that phasic LC activity has typically been studied with electrophysiological approaches that afford millisecond resolution and that observed phasic responses are often extremely short, there are numerous differences between those studies and this one. Most prominently, the stimuli used to elicit a phasic response are generally extremely short (often 1ms or less) and therefore generate extremely short phasic responses (Aston-Jones and Bloom, 1981a; Aston-Jones and Cohen, 2005), but this is not to say that phasic responses might not be longer in response to a longer lasting stimulus. Moreover, tonic activity is reported to track with behavioral state on the order of dozens of seconds to minutes and is not reported in response to specific stimuli (Aston-Jones and Bloom, 1981b). The “phasic” responses we report generally decay in less than 5 seconds in our fluorescence signals. Given the slow time course of decay for GcAMP6s (a single action potential can generate a response that lasts 3 or more seconds (Chen et al., 2013)) and the GRAB sensors (GRAB-DA2h τoff = 7.2s (Sun et al., 2020)), the underlying neural responses would have lasted for a significantly shorter period. Therefore, we believe the responses we observed are much more consistent with phasic responses to long-lasting sensory stimuli (20-second tone, 1-2 second shock), than with increases in tonic activity associated with a change in behavioral state. Finally, regardless of whether these responses are exactly the same as previously reported phasic responses, our photometry and optogenetics studies provide insight about a form of LC activity that is fundamentally different than what can be gleaned from much slower dialysis, lesion, and pharmacology studies. Nonetheless, we added the following to the discussion section to clarify the limitations of our interpretation:

“…given their relatively short duration and the fact that they are elicited specifically by salient sensory stimuli, we refer to these responses as “phasic responses.” However, because of the comparatively slow dynamics of fluorescent sensors relative to electrophysiology, we cannot rule out the possibility that these responses are somehow different in nature to previously reported phasic LC responses. Thus, some care must be taken in conflating the characteristics and/or function of the relatively short-lasting responses presented here and the extremely fast phasic responses to very brief (μs to ms) sensory stimuli reported previously.”

Much of the data presented here can be regarded as 'proof of concept' i.e. demonstrating that Photometric imaging of calcium signalling yields similar results concerning LC responses to salient or behaviorally relevant stimuli as has been previously reported using electrophysiological unit recording. The role of dopamine as the principal player in hippocampaldependent learning also corroborates previous reports.

Although some of the data presented in this study could be seen as “proof of concept” or “confirmatory” of previous results, we believe this work extends previous results by showing 1) the importance of hippocampal dopamine to aversive hippocampus-dependent learning and trace fear conditioning specifically, 2) that LC responses are important at the specific times of learning (i.e. CS/US onset/termination), and 3) that dopamine in the hippocampus is likely important for learning in a way that is not tied to prediction error or memory consolidation.

No attempt was made to address the important current question of the modular organisation of Locus Coeruleus, although the authors recognize the importance of this question and propose future experiments using their methodology to record simultaneously in several LC projection sites.

While we do recognize the importance of this modular organization, which is addressed in the discussion as the reviewer mentions, experiments addressing this organization are beyond the scope of the present study. Future work will address the possibility that LC projections to different regions show differential responses during learning.

The phasic-tonic issue has not been resolved by these experiments. Phasic responses of LC single units are short-latency, short-lived (just 3-4 action potentials), and followed by a relatively long refraction period. Multiunit responses will have a more jittery latency and longer-lasting response (but still only tens to hundreds of milliseconds). Your figures clearly show long-lasting increases in tonic firing levels, even though you state the contrary in the discussion. Therefore, I strongly recommend removing the word 'phasic' from the title.

Addressed above.

Yohimbine, the Alpha 2 antagonist, administered systemically, induces a massive increase in the rate of firing of LC cells (through blockade of autoinhibition at the cell body level at terminals). I guess its effect on the receptor 'backbones' overrides the massive release of NE and/or DA, but you might want to mention this; also include the dose of all drug treatments.

Yes, yohimbine’s effect on the GRAB-NE signal is somewhat counter-intuitive given the known effect of yohimbine on norepinephrine levels. However, our result is consistent with previous reports (Feng et al., 2019). We have added the following to the results section to clarify:

“Thus, even though yohimbine is known to increase NE levels in the hippocampus (Abercrombie et al., 1988), its blockade effect on the GRAB-NE sensor should result in a decrease in fluorescence after administration.”

Include time scale units on all figures (I assume it is seconds in Figs 1 &2).

Thank you for pointing out this issue, we have added units on all figures.

• Is it possible to have a better quality example of staining? Fig 1 B in particular is very blurry. Is the yellow double staining? Please indicate. Most of the GCaMP seems to be outside the main area of TH staining. Fig 4 B is much nicer--and it looks morphologically, like LC.

Unfortunately, the GcAMP6s staining was very dim in our hands and resulted in relatively blurry images. Yes, in this case, yellow is double staining. Regarding the morphology, the GCaMP image is taken from a sagittal section and the shape of expression is consistent with images of LC in the sagittal plane. However, given the quality of our ChR2 images, we are confident in the specificity of expression in these mice.

Reviewer 2

The claim that dopamine release in dHPC is caused by LC neurons is not directly tested. Unfortunately, the most critical experiment for the claims that dopamine release comes from LC during conditioning is not tested. A lack of dopamine signal in dHPC caused by inhibition of LC during TFC would show this. It is indeed an interesting observation that chemoegenetic activation of LC causes dopamine release in the dHPC. However, in the absence of concurrent VTA inhibition or lesion, it remains a possibility that the dopamine release is mediated through indirect actions on other dopamine-expressing neurons. The authors do a good job of arguing against this interpretation in the discussion, and the literature seems appropriate for this. However, the title is still an overstatement of the data presented in this study.

We agree with the reviewer’s comments. As indicated in the discussion, it is possible that hippocampal dopamine is increased indirectly via LC projections to dopaminergic midbrain regions. We believe that our title is consistent with this possibility. When phasic stimulation was delivered to the LC, dopamine levels increased in the hippocampus and trace fear conditioning was enhanced. The observed increase in dopamine could be direct or indirect. As the reviewer notes, we argue for the former in the discussion section. A number of experiments would be needed to show this directly (record dopamine while: inhibiting the LC, inhibiting the VTA, stimulating LC while simultaneously inhibiting the VTA etc.) and we are planning to do these in the future.

The primary alternative interpretations of the phasic activation experiment are whether only stimulation to the cue events (both on and off), or whether only stimulation to the shock. Thus this experiment would benefit from additional data showing either a no shock control, to show that enhanced activity of the LC to the tone is not inherently aversive, or manipulations to the tone but not to the shock.

Future work will explore whether the contribution of LC to learning is primarily due to its activation during the CS or the US. However, this is beyond the scope of this manuscript.

Specificity of the GRAB-NE and GRAB-DA sensors should be either justified through additional experiments testing the alternative antagonist (i.e. GRAB-NE CNO+eticloprode / GRAB-DA CNO+yohimbine) or additional citations that have tested this already. It is critical for the claims of the paper to show that these sensors are specific to dopamine or norepinephrine.<br /> Although sensitivity is a potential concern, these sensors have been thoroughly vetted and used by many groups since their generation. In particular, the creators of these sensors provided extensive data showing their specificity. The GRAB-DA sensor is ~10 fold more sensitive to DA than to NE (Sun et al., 2020, cited 239 times) and the GRAB-NE sensor is ~37 fold more sensitive to NE than to DA (Feng et al., 2019, cited 371 times).

The role of dopamine in prediction error was tested through a series of conditions whereby the shock was presented either signaled (i.e. predicted), or not. However, another way that prediction error is signaled is through the absence of an expected outcome. Admittedly it might not be possible to observe a decrease in dopamine signaling with this methodology.

Although this is a strong point, given that the study is not primarily focused on error prediction and the low likelihood of observing the typically small decrease in signaling during expected outcome omission, we feel that additional error prediction studies are beyond the scope of this manuscript. However, further experiments as suggested by the reviewer could prove interesting in future studies.

The difference between Fig. 6E and 6H needs to be clarified. What is shown in Fig. 6E is that the response to the shock decreases through experience (i.e. by the 10th trial). However in Fig 6H, there is no difference between signaled and signaled shock, but this is during conditioning, and not after learning (based on my understanding of the methods, line 482).

We are not sure we fully understand what point of clarification the reviewer is asking for. However, we have clarified in the methods that the signaled vs unsignaled shock experiment took place in animals that had already been trained on TFC. Thus, all of the trials took place after the animals had learned the tone-shock association. Therefore, although the drop in shock-response could be taken as an indicator of a prediction-error like signal, all the other data points to this not being the case (no change in tone response over training, no difference in signaled vs. unsignaled responses after training).

Unless I missed it, at no point in the manuscript is the number of subjects described. Please add the n per experiment within each section describing each experiment in the methods (Behavioral procedures). Some more details in the photometry statistical analysis would be helpful. For example, what is the n per group for every data set that is presented? How many trials per analysis?

We thank the reviewer for pointing this out. Animal numbers have been added in the methods section in the Behavioral Procedures, Optogenetics, and Drugs sub-sections and in the figure legends. Trial numbers are included in these sections and all trials were used for analysis.

What is the difference in experimental procedure between Fig. 2D and Fig. 3B? It seems that they are the same, and yet the LC response to the conditioned CS is not.

Fig. 3B is simply the Day 1 data from Fig 2D presented at a different scale because the shock response is included in Fig. 3B which necessitates a larger scale on both axes. Close inspection of the figures will show that the shapes of these two curves and the error around them is the same, but the different scaling obfuscates this slightly.

Typo in the legend of Figure 2 - D should be E.

Thank you, we have corrected this.

• Anatomical localization of the virus injections, and more importantly the fiber placements, is not shown. Including this information helps with replication and understanding where exactly the observations were made in dHPC to contrast with prior studies.

Representative examples are included in the manuscript in figure 1B, 3F, 4B, and 5B.

Reviewer 3

While the optogenetic study was lovely, a control using the same stimulation but delivered at different time points would have been a good addition to show how critical the neural signal at tone onset, tone offset, and shock is.

We agree that it would be interesting in future studies to delineate the specific times when LC stimulation produces a learning enhancement. It could be that LC activity is most important during one specific time period (eg. just during shock) or that all three periods of activation are required. It would also be useful to know whether stimulation at other times during learning can produce an enhancement given the potentially long-lasting effects of dopamine on HPC plasticity and learning.

Justification for the focus on D1 receptors was lacking.

We chose to focus on D1 receptors because previous studies have shown that these receptors are critical for memory formation or consolidation in the hippocampus. We have added a sentence justifying this in the results section.

“To test whether dopamine is required for trace fear memory formation, we administered the dopamine D1 receptor antagonist SCH23390 (0.1mg/kg) 30 minutes before training, as D1/D5 receptors have previously been shown to be critical for other types of hippocampus dependent memory and plasticity (Frey et al., 1990; Huang and Kandel, 1995; O’Carroll et al., 2006; Wagatsuma et al., 2018).”

The manuscript provides convincing evidence that the neural signal is not an error- correcting one by including a predicted (by a tone) and unpredicted shock. One possibility is that perhaps the unpredicted shock could be predicted by the context. Some clarification on the behavioural procedures would help understand if indeed the unsignaled shock could be predicted by the context or not.

Mice always exhibit freezing in the training environment, so the context is definitely a predictor of shock. However, the tone is a much better predictor because it is always followed by shock while the mice spend a large amount of time in the context without being shocked. This is demonstrated by the fact that the same procedure used in the current experiments consistently produces more tone fear than context fear (Wilmot et al., 2019). While we did not do long-term memory tests here, we assume the same dissociation occurred as it has been observed very consistently across studies (Chowdhury et al., 2005; Kitamura et al., 2014; Wilmot et al., 2019). Nonetheless, it is possible that a difference between signaled and unsignaled groups was obscured by the context. We should note however, that differences between dopaminergic responses to cued and uncued rewards and aversive outcomes has been observed and these animals were also trained in the same context (Eshel et al., 2016; Matsumoto and Hikosaka, 2009; Pan et al., 2005; Schultz, 1998). Therefore, we believe this experiment does differentiate the observed dopamine response in the hippocampus from previously reported VTA dopamine prediction error signaling.

Figure 2 - tone termination in Tone only group - no change? Stats?

Thank you for pointing out this omission. We have added the stats to the figure legend. Although the response to tone termination decreased numerically, it did not change significantly across days. This is one point we may seek to clarify in future studies, as the difference between tone onset and termination responses is unexpected. Given the relatively small responses, it’s possible future studies with stronger signal (eg. GcAMP8) may find differences in the tone termination response across training days. This is one of the reasons we focused primarily on the responses to tone onset and shock in the rest of the manuscript.

Fig 4 data - stimulation at time incongruent with the signal as a control for the timing of stim.

This is addressed above.

Fig 5 - GRAB-NE - yohimbine seems to suppress the signal below the vehicle. Not the case for GRAB-DA. Is this sig? post-hoc stats?

Yes, this does appear to be the case for GRAB-NE, and would not be entirely surprising given that there is likely a baseline level of NE (and dopamine) in the hippocampus that produces some degree of baseline fluorescence in the vehicle group. This signal could be reduced/abolished by blocking the sensor and preventing this baseline level of NE from binding and producing fluorescence. This may not be the same for the GRAB-DA for a variety of reasons – different sensor binding affinities, different baseline neurotransmitter levels, potentially non-equivalent drug doses, etc. Because of the large number of pairwise comparisons in this data (18), we did not make post-hoc pairwise comparisons.

Shock response curve - lines 466-474 - some explanation of what the pseudorandom order of shock presentation means.

We have added the following explanation to this section:

“…pseudorandom order, such that the shocks did not occur in ascending or descending order or follow the same pattern in each block,…”

Line 126 - the extinction came out of the blue, it needs some introduction such as a statement that the animals were exposed to extinction training following conditioning.

We have added the following earlier in that same paragraph:

“On the second and third days, mice underwent extinction trials in which no shocks were administered.”

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Author Response

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

The authors conducted two tasks at 300 days of separation. First, a social perception task, where Ps responded whether a pictured person either deserved or needed help. Second, an altruism task, where Ps are offered monetary allocations for themselves and a partner. Ps decide whether to accept, or a default allocation of 20 dollars each. The partners differed in perceived merit, such that they were highly deserving, undeserving, or unknown. This categorisation was decided on the basis of a prisoner's dilemma game the partner played beforehand. "Need" was also manipulated, by altering the probability that the partner must have their hand in cold water at the end of the experiment and this partner can use the money to buy themselves out. These two tasks were conducted to assess the perception of need/merit in the first instance, and how this relates to social behaviour in the second. fMRI data were collected alongside behavioural.

The authors present many analyses of behaviour (including DDM results) and fMRI. E.g., they demonstrate that they could decode across the mentalising network whether someone was making a need or deserving judgement vs control judgement but couldn't decode need vs deserving. And that brain responses during merit inferences (merit - control) systematically covaried with participants' merit sensitivity scores in the rTPJ. They also found relationships between behaviour and rTPJ in the altruism task. And that merit sensitivity in the perception task predicted the influence of merit on social behaviour in the altruism task.

Strengths:

This manuscript represents a sensible model to predict social perceptions and behaviours, and a tidy study design with interesting findings. The introduction introduced the field especially brilliantly for a general audience.

Response: We are pleased that the reviewer found the model sensible and the findings interesting! Below, we respond to each of the reviewer’s comments/critiques.

Weaknesses: (1) The authors do acknowledge right at the end that these are small samples. This is especially the case for the correlational questions. While the limitation is acknowledged at the end, it is not truly acknowledged in the way that the data are interpreted. I.e. much is concluded from absent relationships, where the likelihood of Type II error is high in this scenario. I suggest that throughout the manuscript, authors play down their conclusions about absence of effects.

Response: We agree with the reviewer that the limitation of small samples should be adequately reflected in the interpretation of the data. We have therefore added cautionary language to the interpretation of the correlational effects in several places of the revised manuscript. For example, we now state: “However, this absence of effects for need ought to be interpreted with caution, given the comparatively small sample size.” (pg. 33) and “As mentioned above, we cannot rule out the possibility that null findings may be due to the comparatively small sample size and should be interpreted cautiously (also see discussion)” (pg. 34-35).

(2) I found the results section quite a marathon, and due to its length I started to lose the thread concerning the overarching aims - which had been established so neatly in the introduction. I am unsure whether all of these analyses were necessary for addressing the key questions or whether some were more exploratory. E.g. it's unclear to me what one would have predicted upfront about the decoding analyses.

Response: We acknowledge and share the reviewer’s concern about the length of the results section and potential loss of clarity. Regarding the decoding analyses, we want to clarify that they were conducted as a sanity check to compare against the results of the univariate analysis. We didn’t have apriori hypotheses regarding these supplemental decoding analysis. We have clarified this issue in the revised version of the manuscript and moved the decoding analyses fully to the supplemental material to streamline the main text. The remaining results reported in the manuscript are indeed all based on apriori, key questions (unless specified otherwise, for example, supplemental analyses for other regions of interest for the sake of completeness). The only exception is the final set of results (Neural markers of merit sensitivity predict merit-related behavioral changes during altruistic choice) which represent posthoc tests to clarify the role of activation in the right temporoparietal junction (rTPJ) in merit-related changes in other-regard in altruistic decisions. While we acknowledge that this is a complex paper, after careful consideration we couldn’t identify any other parts of the results section to remove or report in the supplemental material.

(3) More specifically, the decoding analyses were intriguing to me. If I understand the authors, they are decoding need vs merit, and need+merit vs control, not the content of these inferences. Do they consider that there is a distributed representation of merit that does not relate to its content but is an abstracted version that applies to all merit judgements? I certainly would not have predicted this and think the analyses raise many questions.

Response: We thank the reviewer for sharing their thoughts on the decoding analyses and agree that this set of analyses are intriguing, yet raise additional questions, such as the neural computations required to assess content. However, we wish to clarify that the way we view our current results is very much analogous to results obtained from studies of perception in other fields. For example, in the face perception literature, it is often observed that the fusiform face area is uniformly more active, not only when a face (as opposed to an object) is on the screen, but when a compound stimulus consistent of features of a face and other features (e.g. of objects) is on the screen, but participants are instructed to attend to and identify solely the face. Moreover, multivariate activity in the FFA (but not univariate activity) is sufficient to decode the identity of the face. We view the results we report in the manuscript as more akin to the former types of analyses, where any region that is involved in the computation is uniformly more active when attention is directed to judgment-specific features. Unfortunately, the present data are not sufficient to properly answer the latter questions, about which areas enable decoding of specific intensity or identity of merit-related content. Follow-up experiments with a more optimized design are needed. Although interesting, we thus refrain from further discussing the decoding analyses in the manuscript to avoid distracting from the main findings based on the univariate comparison of brain responses observed while participants make merit or need inferences in the social perception task.

Reviewer #2 (Public Review):

When people help others is an important psychological and neuroscientific question. It has received much attention from the psychological side, but comparatively less from neuroscience. The paper translates some ideas from a social Psychology domain to neuroscience using a neuroeconomically oriented computational approach. In particular, the paper is concerned with the idea that people help others based on perceptions of merit/deservingness, but also because they require/need help. To this end, the authors conduct two experiments with an overlapping participant pool:

(1) A social perception task in which people see images of people that have previously been rated on merit and need scales by other participants. In a blockwise fashion, people decide whether the depicted person a) deserves help, b) needs help, and c) whether the person uses both hands (== control condition).

(2) In an altruism task, people make costly helping decisions by deciding between giving a certain amount of money to themselves or another person. How much the other person needs and deserves the money is manipulated.

The authors use a sound and robust computational modelling approach for both tasks using evidence accumulation models. They analyse behavioural data for both tasks, showing that the behaviour is indeed influenced, as expected, by the deservingness and the need of the shown people. Neurally, the authors use a block-wise analysis approach to find differences in activity levels across conditions of the social perception task (there is no fMRI data for the other task). The authors do find large activation clusters in areas related to the theory of mind. Interestingly, they also find that activity in TPJ that relates to the deservingness condition correlates with people's deservingness ratings while they do the task, but also with computational parameters related to helping others in the second task, the one that was conducted many months later. Also, some behavioural parameters correlate across the two tasks, suggesting that how deserving of help others are perceived reflects a relatively stable feature that translates into concrete helping decisions later-on.

The conclusions of the paper are overall well supported by the data.

Response: We thank the reviewer for the positive evaluation of our study and the comprehensive summary of our main findings. We would like to clarify, though, that we did originally collect fMRI data for the independent altruism task. Unfortunately, due to COVID-19-related interruptions, only 25 participants from the sample that performed the social perception task also completed the fMRI altruism task (see pg. 18). Given the limited sample size and noise level of fMRI data, we moved anything related to the neuroimaging data of the altruism task to the supplemental material (see Note S7) and decided to focus solely on the behavior of the altruism task to address our research objectives. We apologize for any confusion.

(1) I found that the modelling was done very thoroughly for both tasks. Overall, I had the impression that the methods are very solid with many supplementary analyses. The computational modelling is done very well.

Response: We are pleased that the reviewer found the computational model sensible.

(2) A slight caveat, however, regarding this aspect, is that, in my view, the tasks are relatively simplistic, so even the complex computational models do not do as much as they can in the case of more complex paradigms. For example, the bias term in the model seems to correspond to the mean response rate in a very direct way (please correct me if I am wrong).

Response. We agree that the Bias term relates to mean responding (although it is not the sole possibility: thresholds and starting default biases can also produce changes in mean levels of responding that, without the computational model, are not possible to dissociate). However, we think that the primary value of this parameter comes not from the analysis of the social judgment task (where the reviewer is correct that the bias relates in a quite straightforward way to the mean response rate), but in the relationship of this parameter to the un-contextual generosity response in the altruism task. Here, we find that this general bias term relates not to overall generosity, but rather to the overall weight given to others’ outcomes, a finding that makes sense if the tendency to perceive others as deserving overall yields an increase in overall attention/valuation of their outcomes. Thus, a simple finding in one task relates to a more nuanced finding in another. However, we agree it is important to acknowledge the point raised by the reviewer, and now do so on pg. 20: “It is worth noting that the Bias parameters are strongly associated with (though not the sole determinant of) the mean response rate.”

(3) Related to the simple tasks: The fMRI data is analysed in a simple block-fashion. This is in my view not appropriate to discern the more subtle neural substrates of merit/need-based decision-making or person perception. Correspondingly, the neural activation patterns (merit > control, need > control) are relatively broad and unspecific. They do not seem to differ in the classic theory of mind regions, which are the focus of the analyses.

Response: The social perception task is modified from a well-established social inference task (Spunt & Adolphs, 2014; 2015) designed to reliably localize the mentalizing network in the brain. As such, we acknowledge that it is not optimally designed to discern the intrinsic complexities of social perception, or the specific appraisals or computations that yield more or less perception (of need or merit) in a given context. Instead, it was designed to highlight regions that are more generally recruited for performing these social perceptions/inferences.

We heartily agree with the reviewer that it would be interesting and informative to analyze this task in a trial-wise way, with parametric variation in evidence for each image predicting parametric variation in brain activity. Unfortunately, the timing of this task is not optimal for this kind of an analysis, since trials were presented in rapid and blocked fashion. We were also limited in the amount of time we could devote to this task, since it was collected in conjunction with a number of other tasks as part of a larger effort to detail the neural correlates of social inference (reported elsewhere). Thus, we were not able to introduce the kind of jittered spacing between trials that would have enabled such analysis, despite our own wish to do so. We hope that this work will thus be a motivator for future work designed more specifically to address this interesting question, and now include a statement to this effect on pgs. 2223: “Future research may reveal additional distinctions between merit and need appraisals in trial-wise (compared to our block-wise) fMRI designs.”

References:

Spunt, R. P. & Adolphs, R. Validating the Why/How contrast for functional MRI studies of Theory of Mind. Neuroimage 99, 301-311, doi:10.1016/j.neuroimage.2014.05.023 (2014).

Spunt, R. P. & Adolphs, R. Folk explanations of behavior: a specialized use of a domain-general mechanism. Psychological Science 26, 724-736, doi:10.1177/0956797615569002 (2015).

(4) However, the relationship between neural signal and behavioural merit sensitivity in TPJ is noteworthy.

Response: We agree with this assessment and thank the reviewer for their positive assessment; we feel that linking individual differences in merit sensitivity with variance in TPJ activity during merit judgments is one of the key findings of the study.

(5) The latter is even more the case, as the neural signal and aspects of the behaviour are correlated across subjects with the second task that is conducted much later. Such a correlation is very impressive and suggests that the tasks are sensitive for important individual differences in helping perception/behaviour.

Response: Again, we share the reviewer’s impression that this finding is more noteworthy for appearing in tasks separated both by considerable conceptual/paradigmatic differences, and by such a long temporal distance. These findings make us particularly excited to follow up on these results in future research.

(6) That being said, the number of participants in the latter analyses are at the lower end of the number of participants that are these days used for across-participant correlations.

Response: We fully agree with this assessment. Unfortunately, COVID-related disruptions in data collection, as well as the expiration of grant funds due to the delay, severely limited our ability to complete assessments in a larger sample. Future research needs to replicate these results in a larger sample. We comment on this issue in the discussion on pg. 40. If the editor or reviewer has suggestions for other ways in which we could more fully acknowledge this, we would be happy to include them.

Reviewer #3 (Public Review):

Summary:

The paper aims to provide a neurocomputational account of how social perception translates into prosocial behaviors. Participants first completed a novel social perception task during fMRI scanning, in which they were asked to judge the merit or need of people depicted in different situations. Secondly, a separate altruistic choice task was used to examine how the perception of merit and need influences the weights people place on themselves, others, and fairness when deciding to provide help. Finally, a link between perception and action was drawn in those participants who completed both tasks.

Strengths:

The paper is overall very well written and presented, leaving the reader at ease when describing complex methods and results. The approach used by the author is very compelling, as it combines computational modeling of behavior and neuroimaging data analyses. Despite not being able to comment on the computational model, I find the approach used (to disentangle sensitivity and biases, for merit and need) very well described and derived from previous theoretical work. Results are also clearly described and interpreted.

Response: We thank the reviewer for their positive comments regarding presentation, approach, and content.

Weaknesses:

My main concern relates to the selection of the social perception task, which to me is the weakest point. Such weakness has been also addressed by the same authors in the limitation section, and related to the fact that merit and need are evaluated by means of very different cues that rely on different cognitive processes (more abstract thinking for merit than need). I wonder whether and how such difference can bias the overall computational model and interpretation of the results (e.g. ideal you vary merit and need to leave all other aspects invariant).

Response: We agree with the reviewer on the importance of future research to more fully unpack the differences in this task, and develop better ways to manipulate need and merit in more comparable fashion. However, we point out that the issue of differences in abstractness of cues for need and merit does not actually seem to have a strong influence on the parameters retrieved by the computational model. Participants seem to be equally sensitive to BOTH merit and need information, despite that information deriving from different sources, as evidenced by the fact that the magnitude of the sensitivity parameters for need and merit in the social judgment task were nearly identical, and not statistically distinguishable. Nor were other parameters related to non-decision time or threshold statistically different (see Supplemental Table S2). If our results were driven purely by differences in the difficulty or abstractness of these judgments, we would have expected to see some evidence of this in the computational model, in the form of longer non-decision times, higher thresholds, or both. We do not. Likewise, the neural underpinnings evoked by both need and merit perceptions in this task (in the mentalizing brain network) were comparable. This is not to say that there aren’t real differences in the cues that might signal these quantities in our social perception task - just that there is little direct evidence for this difference in computational parameters or evoked brain responses, and thus it is unlikely that our results (which rely on an analysis of computational parameters) are driven solely by computational model biases, or the inability of the model to adequately assess participant sensitivity to need as opposed to merit.

A second weakness is related to the sample size which is quite small for study 2. I wonder, given that study 2 fRMI data are not analyzed, whether is possible to recover some of the participants' behavioral results, at least the ones excluded because of bad MR image quality.

Response: We fully agree with the reviewer that increasing the sample size for the cross-task correlations would be desirable. Unfortunately, the current sample size already presents the maximum of ‘usable’ data; the approach suggested by the reviewer won’t affect the sample size. We used all participants whose behavioral data in the altruism task suggested they were performing the task in good faith and conscientiously.

Finally, on a theoretical note, I would elaborate more on the distinction of merit and need. These concepts tap into very specific aspects of morality, which I suspect have been widely explored. At the moment I am missing a more elaborate account of this.

Response: Need and merit are predominantly studied in separate lines of research (Molouki & Bartels, 2020) so there is relatively little theoretical research on the distinction between the two. Consequently, Siemoneit (2023) states that the relation between the concepts of need and merit in allocative distributions remains diffuse. To emphasize the distinct concepts of morality in the introduction we have now added to pg. 3: “Need and deservingness (merit) are two distinct principles of morality. The need principle involves distributing resources to those who require them, irrespective of whether they have earned them, while the "merit principle" focuses on allocating resources based on individuals' deservingness, regardless of their actual need (Wilson, 2003).”

One of the added values of our paper to the research literature is in adding to the clarification of computational and neural underpinnings of broad concepts like merit and need. To highlight the latter point, we have added the following statement on pg. 5 to the manuscript: “Examining need and merit concurrently in this task will also help clarify the computational and neural underpinnings of related, but distinct concepts, distinguishing between them more effectively.”

References:

Molouki, S., & Bartels, D. M. (2020). Are future selves treated like others? Comparing determinants and levels of intrapersonal and interpersonal allocations. Cognition, 196, 104150.

Siemoneit, A. (2023). Merit first, need and equality second: hierarchies of justice. International Review of Economics, 70(4), 537-567.

Wilson, C. (2003). The role of a merit principle in distributive justice. The Journal of ethics, 7, 277-314.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

I acknowledge the difficulty with respect to recruitment, especially in the age of covid, but is it possible for the authors to collect larger samples for their behavioural questions via online testing? Admittedly, I'm sure they don't want to wait 300 days to have the complete dataset, but I would be in favour of collecting a sample in the hundreds on these behavioural tasks, completed at a much shorter separation (if any). I believe this would strengthen the authors' conclusions considerably if they could both replicate the effects they have and check these null effects in a sample where they could draw conclusions from them. Indeed, Bayesian stats to provide evidence for the null would also help here.

Response: We share the reviewer’s desire to see these results replicated (ideally in a sample of hundreds of participants). We have seriously considered the possibility of trying to replicate our results online, even before submitting the first version of the paper. However, it is difficult to fully replicate this paradigm online, given the elaborate story and context we engaged in to convince participants that they were playing with real others, as well as the usage of physical pain (Cold Pressor Task) for the need manipulation in the altruism task. Moreover, given comments by this reviewer that the results are already a little long, adding a new, behavioral replication would likely only add to the memory burden for the reader. We have thus opted not to include a replication study in the current work. However, we are actively working on a replication that can be completed online, using a modified experimental paradigm and different ways to manipulate need and merit. Because of the differences between that paradigm and the one described here, which would require considerable additional exposition, we have opted not to include the results of this work in the current paper. We hope to be able to publish this work as a separate, replication attempt in the future.

Given the difficulty of wading through the results section while keeping track of the key question being answered, I would suggest moving any analyses that are less central to the supplementary. And perhaps adding some more guiding sentences at the start and end of each section to remind the reader how each informs the core question.

Response: We deliberated for quite some time about what results could be removed, but in the end, felt that nearly all results that we already described need to be included in the paper, since each piece of the puzzle contributes to the central finding (relating parameters and behavior to neural and choice data across two separate tasks). However, we did move the decoding analysis results to the supplemental (see point below). We also take the reviewers point that the results can be made clearer. We thus have worked to include some guiding sentences at the start and end of sections to remind the readers how each analysis informs the core questions.

I think it needs unpacking more for the reader what they should conclude from the significant need+merit vs control decoding analyses, and what they would have expected in terms of cortical representation from the decoding analyses in general.

Response: We agree with the reviewer that given the decoding results position in the main manuscript it would need unpacking. After considering the reviewer's prior suggestion, we have reevaluated the placement of these supplemental results. Consequently, we have relocated it to the supplemental materials, as it was deemed less relevant to directly addressing the core research questions in the main manuscript. On pg. 23, the main manuscript now only states “We also employed supplemental multivariate decoding analyses (searchlight analysis 85-87), as commonly used in social perception and neuroscience research 7,58,82,88,89, corroborating our univariate findings (see Supplemental Note S6, Supplemental Table S10).”

Reviewer #2 (Recommendations For The Authors):

(1) I would suggest moving information on how the computational models were fitted to the main text.

Response: The computational models are a key element of the paper and we deliberated about the more central exposure of the description of how the models were fitted in the main manuscript. However, we are concerned about the complexity and length of the article, which requires quite a lot from readers to keep in mind (as also commented on by reviewer 1). Those readers who are particularly interested in details of model fitting can still find an extensive discussion of the procedures we followed in the supplements. We thus have opted to retain the streamlined presentation in the main manuscript. However, if the editor feels that including the full and extensive description of model fitting in the main paper would significantly improve the flow and exposition of ideas, we are happy to do so.

(2) For the fMRI analyses: Could it be worth analysing the choices in the different conditions? They could be modelled as a binary regressor (yes/no) and this one might be different across conditions (merit/need/hands). Maybe this won't work because of the tight trial timeline, but it could be another avenue to discern differences across fMRI conditions.

Response: We thank the reviewer for this interesting suggestion! Unfortunately, the block design and rapid presentation of stimuli within each condition make it challenging to distinguish the different choices (within or across conditions). While we see the merit in the suggested analytical approach (in fact, we discussed it before the initial submission of the article), it would require some modifications of the task structure (e.g., longer inter-trial-intervals between individual stimuli) and an independent replication fMRI study. We were not able to have such a long inter-trial interval in the original design due to practical constraints on the inclusion of this paradigm in a larger effort to examine a wide variety of social judgment and inference tasks. We hope to investigate this kind of question in greater detail in future fMRI work.

(3) The merit effects seem to be more stable across time than the need conditions. Would it be worthwhile to test if the tasks entailed a similar amount of merit and need variation? Maybe one variable varied more than the other in the task design, and that is why one type of effect might be stronger than the other?

Response: We thank the reviewer for drawing attention to this important point. We used extensive pilot testing to select the stimuli for the social perception task, ensuring an overall similar amount of need and merit variation. For example, the social perception ratings of the independent, normative sample suggest that the social perception task entails a similar amount of need and merit variation (normative participant-specific percentage of yes responses for merit (mean ± standard deviation: 53.95 ± 13.87) and need (45.65 ± 11.07)). The results of a supplemental paired t-test (p = 0.122) indicate comparable SD for need and merit judgments. Moreover, regarding the actual fMRI participant sample, Figure S3 illustrates comparable levels of variations in need and merit perceptions (participant-specific percentage of yes responses for merit (56.70 ± 11.91) and need (48.69 ± 10.81) in the social perception task). Matching the results for the normative sample, the results of a paired t-test (p = 0.705) suggest no significant difference in variation between need and merit judgments. With respect to the altruism task, we manipulated the levels of merit and need externally (high vs. low).

Reviewer #3 (Recommendations For The Authors):

(1) It would be good to provide the demographics of each remaining sample.

Response: We appreciate the attention to detail and agree with the reviewer’s suggestion. We have now added the demographics for each remaining sample to the revised manuscript.

(2) The time range from study 1 to study 2, is quite diverse. Did you use it as a regressor of no interest?

Response: We thank the reviewer for this interesting suggestion. We have examined this in detail in the context of our cross-task analyses (i.e., via regressions and partial correlations). Interestingly, variance in the temporal delay between both tasks does not account for any meaningful variation, and results don’t qualitatively change controlling for this factor.

For example, when we controlled for the delay between both separate tasks (partial correlation analysis), we confirmed that variance in merit sensitivity (social perception task) still reflected meritinduced changes in overall generosity (altruism task; p = 0.020). Moreover, we confirmed that variance in merit sensitivity reflected individuals’ other-regard (p = 0.035) and self-regard (p = 0.040), but not fairness considerations (p = 0.764) guiding altruistic choices. Regarding people’s general tendency to perceive others as deserving, we found that the link between merit bias (social perception task) and overall other-regard (p = 0.008) and fairness consideration (p = 0.014) (altruism task) holds when controlling for the time range (no significant relationship between merit bias and self-regard, p = 0.191, matching results of the main paper).

We refer to these supplemental analyses in the revised manuscript on ps. 33 and 35: “Results were qualitatively similar when statistically controlling for the delay between both tasks (partial correlations).”

(3) Why in study 1 a dichotomous answer has been used? Would not have been better (also for modeling) a continuous variable (VAS)?

Response: We appreciate the reviewer's thoughtful feedback. In Study 1, opting for a dichotomous response format in the social perception task (Figure 1a) was a deliberate methodological choice. This decision, driven by the study's model requirements, aligns with the common use of a computational model employing two-alternative forced choices ("yes" and "no") as decision boundaries. While drift– diffusion models for multiple-alternative forced-choice designs exist, our study's novel research questions were effectively addressed without their complexity. Finally, our model cannot accept continuous response variables as input unless they are transformed into categorical variables.

(4) In the fMRI analyses, when you assess changes in brain activity as a function of merit, I would control for need (and the other way round), to see whether such association is specific.

Response: Regarding the reviewer’s suggestion on controlling for need when assessing changes in brain activity as a function of merit, and vice versa, we would like to clarify the nature of our fMRI analyses in the social perception task. Our focus is on block-wise assessments (need vs. control, merit vs. control, need vs. merit blocks, following the fMRI task design from which our social perception task was modified from). We don’t assess changes in brain activity as a function of the level of perceived merit or need (i.e., “yes” vs. “no” trials within or across task blocks). Blocks are clearly defined by the task instruction given to participants prior to each block (i.e., need, merit, or control judgments). Thus, unfortunately, given the short inter-stimulus-intervals of each block, the task design is not optimal to implement the suggested approach.

Author Response

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

Reviewer #1, in both the public review and recommendations to authors, raises the important question of generalizability of the new technique to other brain areas, to analysis with sorters other than Kilosort, and in the absence of reference data. Specifically, how can experimenters working in brain areas other than visual cortex understand if the tracking is functioning, and set the parameters in the tracking pipeline.

We agree that generalizability of the tracking procedure is a serious issue, especially with respect to other brain areas with varying degrees of measured waveform preservation over time. As the number of potential recording conditions is combinatorial to experimentally test, we instead address these issues in the manuscript by providing a general prescription for interpreting the distribution of vertical distances of matched pairs that can be used for data from any recording using any spike-sorter (Methods section 4.2, Supplement section 8.4, figure S9, paragraphs 7-10 of the Discussion section). This extension of the method allows users to estimate the matching success in the context of their own data, even in the absence of reference data. To address the concern of overfitting, we have also added discussion covering adjustment of the two parameters in the procedure (the relative weight of waveform distance vs. physical distance, and the threshold for accepting matches as real) to the Discussion section.

Reviewer #2 suggested clarification of the following points in the public review. We answer those here and have also clarified these points in the main text where appropriate.

(1) What is the purpose of testing the drift correction with imposed drift (Figure 2, page 6 in the original manuscript), and how the value was chosen?

To test the ability of EMD to detect substantial drift, we need examples that resemble experimental data, including error in fit unit positions and units with no correct matches. We chose to create these examples by taking waveform and position sets from real data with modest drift, and adding a fixed shift to one dataset. The value of 12 um in the figure is arbitrary, simply an example in the range of real drift. These tests allow us to demonstrate the success of EMD for detection of drift in real data.

(2) How is performance affected by using a different weighting of the 2 measures (physical distance and waveform distance) in the EMD?

Recovery rate (number of reference units successfully matched in EMD) vs weighting of the waveform distance is shown in Supplement section 8.10. Recovery rate increases with low values of waveform weighting, leveling off at a value of 1500. We selected that inflection point for the analysis in this paper, to avoid coincidental matching of physically distant units with similar waveforms.

(3) Should the intervals measured in the survival plot in Figure 5 be identical for the three different classes of tracked neurons?

The plot includes all chains of tracked neurons, which can start on arbitrary days in the set of all recordings (see the definition of chains in section 2.4). As a result, the gaps between days, which determine where there is a point on the plot, can be different for the three sets of neurons (reference, putative, and mixed). We have added a comment to the Figure 5 caption to ensure this is clear.

(4) Would other metrics of the similarity of visual responses work better?

The similarity metric we use was adopted from the original paper using this data (reference 7). We chose to use the same metric both to take advantage of the original authors’ expertise about the data and allow for reasonable comparison of the new technique to theirs. It is correct that this similarity metric alone does not allow for unique matching (see Discussion and Supplement section 8.2). However, the agreement of EMD with reference pairs determined from the combination of position and visual response similarity is very high, suggesting there are few incorrect reference pairs. Any incorrect reference pairs cause an underestimate of the tracking accuracy.

(5) Add a definition of ROC.

Added this definition to the text.

Reviewer #1 Recommendation to authors:

The main text needs proofreading.

We agree that the manuscript needed more thorough proofreading, and we have made corrections of typos and minor language errors throughout.

Additional comment from the authors:

Since the posting of this manuscript, another method for tracking neurons has been introduced:

Enny H. van Beest, Célian Bimbard, Julie M. J. Fabre, Flóra Takács, Philip Coen, Anna Lebedeva, Kenneth Harris, Matteo Carandini, Tracking neurons across days with high-density probes, bioRxiv 2023.10.12.562040; doi: https://doi.org/10.1101/2023.10.12.562040

Author Response

Reviewer #1 (Public Review):

Summary:

By examining the prevalence of interactions with ancient amino acids of coenzymes in ancient versus recent folds, the authors noticed an increased interaction propensity for ancient interactions. They infer from this that coenzymes might have played an important role in prebiotic proteins.

Strengths:

(1) The analysis, which is very straightforward, is technically correct. However, the conclusions might not be as strong as presented.

(2) This paper presents an excellent summary of contemporary thought on what might have constituted prebiotic proteins and their properties.

(3) The paper is clearly written.

We are grateful for the kind comments of the reviewer on our manuscript. However, we would like to clarify a possible misunderstanding in the summary of our study. Specifically, analysis of "ancient versus recent folds" was not really reported in our results. Our analysis concerned "coenzyme age" rather than the "protein folds age" and was focused mainly on interaction with early vs. late amino acids in protein sequence. While structural propensities of the coenzyme binding sites were also analyzed, no distinction on the level of ancient vs. recent folds was assumed and this was only commented on in the discussion, based on previous work of others.

Weaknesses:

(1) The conclusions might not be as strong as presented. First of all, while ancient amino acids interact less frequently in late with a given coenzyme, maybe this just reflects the fact that proteins that evolved later might be using residues that have a more favorable binding free energy.

We would like to point out that there was no distinction to proteins that evolved early or late in our dataset of coenzyme-binding proteins. The aim of our analysis was purely to observe trends in the age of amino acids vs. age of coenzymes. While no direct inference can be made from this about early life as all the proteins are from extant life (as highlighted in the discussion of our work), our goal was to look for intrinsic propensities of early vs. late amino acids in binding to the different coenzyme entities. Indeed, very early interactions would be smeared by the eons of evolutionary history (perhaps also towards more favourable binding free energy, as pointed out also by the reviewer). Nevertheless, significant trends have been recorded across the PDB dataset, pointing to different propensities and mechanistic properties of the binding events. Rather than to a specific evolutionary past, our data therefore point to a “capacity” of the early amino acids to bind certain coenzymes and we believe that this is the major (and standing) conclusion of our work, along with the properties of such interactions. In our revised version, we will carefully go through all the conclusions and make sure that this message stands out but we are confident that the following concluding sentences copied from the abstract and the discussion of our manuscript fully comply with our data:

“These results imply the plausibility of a coenzyme-peptide functional collaboration preceding the establishment of the Central Dogma and full protein alphabet evolution”

“While no direct inferences about distant evolutionary past can be drawn from the analysis of extant proteins, the principles guiding these interactions can imply their potential prebiotic feasibility and significance.”

“This implies that late amino acids would not be necessarily needed for the sovereignty of coenzyme-peptide interplay.”

We would also like to add that proteins that evolved later might not always have higher free energy of binding. Musil et al., 2021 (https://www.ncbi.nlm.nih.gov/pmc/articles/PMC8294521/) showed in their study on the example of haloalkane dehalogenase Dha A that the ancestral sequence reconstruction is a powerful tool for designing more stable, but also more active proteins. Ancestral sequence reconstruction relies on finding ancient states of protein families to suggest mutations that will lead to more stable proteins than are currently existing proteins. Their study did not explore the ligand-protein interactions specifically, but showed that ancient states often show more favourable properties than modern proteins.

(2) What about other small molecules that existed in the probiotic soup? Do they also prefer such ancient amino acids? If so, this might reflect the interaction propensity of specific amino acids rather than the inferred important role of coenzymes.

We appreciate the comment of the reviewer towards other small molecules, which we assume points mainly towards metal ions (i.e. inorganic cofactors). We completely agree with the reviewer that such interactions are of utmost importance to the origins of life. Intentionally, they were not part of our study, as these have already been studied previously by others (e.g. Bromberg et al., 2022; and reviewed in Frenkel-Pinter et al., 2020) and also us (Fried et al., 2022). For example, it is noteworthy that prebiotically relevant metal binding sites (e.g. of Mg2+) exhibit enrichment in early amino acids such as Asp and Glu while more recent metal (e.g. Cu and Zn) site in the late amino acids His and Cys (Fried et al., 2022). At the same time, comparable analyses of amino acid - coenzyme trends were not available.

Nevertheless, involvement of metal ions in the coenzyme binding sites was also studied here and pointed to their bigger involvement with the Ancient coenzymes. In the revised version of the manuscript, we will be happy to enlarge the discussion of the studies concerning inorganic cofactors.

(3) Perhaps the conclusions just reflect the types of active sites that evolved first and nothing more.

We partly agree on this point with the reviewer but not on the fact why it is listed as the weakness of our study and on the “nothing more” notion. Understanding what the properties of the earliest binding sites is key to merging the gap between prebiotic chemistry and biochemistry. The potential of peptides preceding ribosomal synthesis (and the full alphabet evolution) along with prebiotically plausible coenzymes addresses exactly this gap, which is currently not understood.

Reviewer #2 (Public Review):

I enjoyed reading this paper and appreciate the careful analysis performed by the investigators examining whether 'ancient' cofactors are preferentially bound by the first-available amino acids, and whether later 'LUCA' cofactors are bound by the late-arriving amino acids. I've always found this question fascinating as there is a contradiction in inorganic metal-protein complexes (not what is focused on here). Metal coordination of Fe, Ni heavily relies on softer ligands like His and Cys - which are by most models latecomer amino acids. There are no traces of thiols or imidazoles in meteorites - although work by Dvorkin has indicated that could very well be due to acid degradation during extraction. Chris Dupont (PNAS 2005) showed that metal speciation in the early earth (such as proposed by Anbar and prior RJP Williams) matched the purported order of fold emergence.

As such, cofactor-protein interactions as a driving force for evolution has always made sense to me and I admittedly read this paper biased in its favor. But to make sure, I started to play around with the data that the authors kindly and importantly shared in the supplementary files. Here's what I found:

Point 1: The correlation between abundance of amino acids and protein age is dominated by glycine. There is a small, but visible difference in old vs new amino acid fractional abundance between Ancient and LUCA proteins (Figure 3, Supplementary Table 3). However, the bias is not evenly distributed among the amino acids - which Figure 4A shows but is hard to digest as presented. So instead I used the spreadsheet in Supplement 3 to calculate the fractional difference FDaa = F(old aa)-F(new aa). As expected from Figure 3, the mean FD for Ancient is greater than the mean FD for LUCA. But when you look at the same table for each amino acid FDcofactor = F(ancient cofactor) - F(LUCA cofactor), you now see that the bias is not evenly distributed between older and newer amino acids at all. In fact, most of the difference can be explained by glycine (FDcofactor = 3.8) and the rest by also including tryptophan (FDcofactor = -3.8). If you remove these two amino acids from the analysis, the trend seen in Figure 3 all but disappears.

Troubling - so you might argue that Gly is the oldest of the old and Trp is the newest of the new so the argument still stands. Unfortunately, Gly is a lot of things - flexible, small, polar - so what is the real correlation, age, or chemistry? This leads to point 2.

We truly acknowledge the effort that the reviewer made in the revision of the data and for the thoughtful, deeper analysis. We agree that this deserves further discussion of our data. As invited by the reviewer, we indeed repeated the analysis on the whole dataset. First, we would like to point out that the reviewer was most probably referring to the Supplementary Fig. 2 (and not 3, which concerns protein folds). While the difference between Ancient and LUCA coenzyme binding is indeed most pronounced for Gly and Trp, we failed to confirm that the trend disappears if those two amino acids are removed from the analysis (additional FDcofactors of 3.2 and -3.2 are observed for the early and late amino acids, resp.), as seen in Table I below. The main additional contributors to this effect are Asp (FD of 2.1) and Ser (FD of 1.8) from the early amino acids and Arg (FD of -2.6) and Cys (FD of -1.7) of the late amino acids. Hence, while we agree with the reviewer that Gly and Trp (the oldest and the youngest) contribute to this effect the most, we disagree that the trend reduces to these two amino acids.

In addition, the most recent coenzyme temporality (the Post-LUCA) was neglected in the reviewer’s analysis. The difference between F (old) and F (new) is even more pronounced in PostLUCA than in LUCA, vs. Ancient (Table II) and depends much less on Trp. Meanwhile, Asp, Ser, Leu, Phe, and Arg dominate the observed phenomenon (Table I). This further supports our lack of agreement with the reviewer’s point. Nevertheless, we remain grateful for this discussion and we will happily include this additional analysis in the Supplementary Material of our revised manuscript.

Author response table 1.

Amino acid fractional difference of all coenzymes at residue level

Author response table 2.

Amino acid fractional difference of all coenzymes

Point 2 - The correlation is dominated by phosphate.

In the ancient cofactor list, all but 4 comprise at least one phosphate (SAM, tetrahydrofolic acid, biopterin, and heme). Except for SAM, the rest have very low Gly abundance. The overall high Gly abundance in the ancient enzymes is due to the chemical property of glycine that can occupy the right-hand side of the Ramachandran plot. This allows it to make the alternating alphaleftalpharight conformation of the P-loop forming Milner-White's anionic nest. If you remove phosphate binding folds from the analysis the trend in Figure 3 vanishes.

Likewise, Trp is an important functional residue for binding quinones and tuning its redox potential. The LUCA cofactor set is dominated by quinone and derivatives, which likely drives up the new amino acid score for this class of cofactors.

Once again, we are thankful to the reviewer for raising this point. The role of Gly in the anionic nests proposed by Milner-White and Russel, as well as the Trp role in quinone binding are important points that we would be happy to highlight more in the discussion of the revised manuscript.<br /> Nevertheless, we disagree that the trends reduce only to the phosphate-containing coenzymes and importantly, that “the trend in Figure 3 vanishes” upon their removal. Table III and IV (below) show the data for coenzymes excluding those with phosphate moiety and the trend in Fig. 3 remains, albeit less pronounced.

Author response table 3.

Amino acid fractional difference of non-phosphate containing coenzymes

Author response table 4.

Amino acid fractional difference of non-phosphate containing coenzymes at residue level

In summary, while I still believe the premise that cofactors drove the shape of peptides and the folds that came from them - and that Rossmann folds are ancient phosphate-binding proteins, this analysis does not really bring anything new to these ideas that have already been stated by Tawfik/Longo, Milner-White/Russell, and many others.

I did this analysis ad hoc on a slice of the data the authors provided and could easily have missed something and I encourage the authors to check my work. If it holds up it should be noted that negative results can often be as informative as strong positive ones. I think the signal here is too weak to see in the noise using the current approach.

We are grateful to the reviewer for encouraging further look at our data. While we hope that the analysis on the whole dataset (listed in Tables I - IV) will change the reviewer’s standpoint on our work, we would still like to comment on the questioned novelty of our results. In fact, the extraordinary works by Tawfik/Longo and Milner-While/Russel (which were cited in our manuscript multiple times) presented one of the motivations for this study. We take the opportunity to copy the part of our discussion that specifically highlights the relevance of their studies, and points out the contribution of our work with respect to theirs.

“While all the coenzymes bind preferentially to protein residue sidechains, more backbone interactions appear in the ancient coenzyme class when compared to others. This supports an earlier hypothesis that functions of the earliest peptides (possibly of variable compositions and lengths) would be performed with the assistance of the main chain atoms rather than their sidechains (Milner-White and Russel 2011). Longo et al., recently analyzed binding sites of different phosphate-containing ligands which were arguably of high relevance during earliest stages of life, connecting all of today’s core metabolism (Longo et al., 2020 (b)). They observed that unlike the evolutionary younger binding motifs (which rely on sidechain binding), the most ancient lineages indeed bind to phosphate moieties predominantly via the protein backbone. Our analysis assigns this phenomenon primarily to interactions via early amino acids that (as mentioned above) are generally enriched in the binding interface of the ancient coenzymes. This implies that late amino acids would not be necessarily needed for the sovereignty of coenzymepeptide interplay.”

Unlike any other previous work, our study involves all the major coenzymes (not just the phosphate-containing ones) and is based on their evolutionary age, as well as age of amino acids. It is the first PDB-wide systematic evolutionary analysis of coenzyme-amino acid binding. Besides confirming some earlier theoretical assertions (such as role of backbone interactions in early peptide-coenzyme evolution) and observations (such as occurrence of the ancient phosphatecontaining coenzymes in the oldest protein folds), it uncovers substantial novel knowledge. For example, (i) enrichment of early amino acids in the binding of ancient coenzymes, vs. enrichment of late amino acids in the binding of LUCA and Post-LUCA coenzymes, (ii) the trends in secondary structure content of the binding sites of coenzyme of different temporalities, (iii) increased involvement of metal ions in the ancient coenzyme binding events, and (iv) the capacity of only early amino acids to bind ancient coenzymes. In our humble opinion, all of these points bring important contributions in the peptide-coenzyme knowledge gap which has been discussed in a number of previous studies.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

The authors compared four types of hiPSCs and four types of hESCs at the proteome level to elucidate the differences between hiPSCs and hESCs. Semi-quantitative calculations of protein copy numbers revealed increased protein content in iPSCs. Particularly in iPSCs, proteins related to mitochondrial and cytoplasmic were suggested to reflect the state of the original differentiated cells to some extent. However, the most important result of this study is the calculation of the protein copy numbers per cell, and the validity of this result is problematic. In addition, several experiments need to be improved, such as using cells of different genders (iPSC: female, ESC: male) in mitochondrial metabolism experiments.

Strengths:

The focus on the number of copies of proteins is exciting and appreciated if the estimated calculation result is correct and biologically reproducible.

Weaknesses:

The proteome results in this study were likely obtained by simply looking at differences between clones, and the proteome data need to be validated. First, there were only a few clones for comparison, and the gender and number of cells did not match between ESCs and iPSCs. Second, no data show the accuracy of the protein copy number per cell obtained by the proteome data.

We agree with the reviewer in their assessment that more independent stem cell clones and an equal gender balance would be preferable. We will mention these considerations as limitations of our study and encourage a larger-scale follow-up.

Regarding the estimated copy numbers, we would like to highlight that they have been extensively in the field, with direct validation of the differences in copy numbers with orthogonal methods like FACS2-4,7,10. Furthermore, the original paper directly compared the copy numbers estimated using the “proteomic ruler” to spike-in protein epitope signature tags and found remarkable concordance. This was performed with a much older generation mass spectrometer with reduced peptide coverage, and the author predicted that higher coverage would increase the quantitative performance.

Reviewer #2 (Public Review):

Summary:

Pluripotent stem cells are powerful tools for understanding development, differentiation, and disease modeling. The capacity of stem cells to differentiate into various cell types holds great promise for therapeutic applications. However, ethical concerns restrict the use of human embryonic stem cells (hESCs). Consequently, induced human pluripotent stem cells (ihPSCs) offer an attractive alternative for modeling rare diseases, drug screening, and regenerative medicine.

A comprehensive understanding of ihPSCs is crucial to establish their similarities and differences compared to hESCs.

This work demonstrates systematic differences in the reprogramming of nuclear and non-nuclear proteomes in ihPSCs.

We thank the reviewer for the positive assessment.

Strengths:

The authors employed quantitative mass spectrometry to compare protein expression differences between independently derived ihPSC and hESC cell lines. Qualitatively, protein expression profiles in ihPSC and hESC were found to be very similar. However, when comparing protein concentration at a cellular level, it became evident that ihPSCs express higher levels of proteins in the cytoplasm, mitochondria, and plasma membrane, while the expression of nuclear proteins is similar between ihPSCs and hESCs. A higher expression of proteins in ihPSCs was verified by an independent approach, and flow cytometry confirmed that ihPSCs had larger cell sizes than hESCs. The differences in protein expression were reflected in functional distinctions. For instance, the higher expression of mitochondrial metabolic enzymes, glutamine transporters, and lipid biosynthesis enzymes in ihPSCs was associated with enhanced mitochondrial potential, increased ability to uptake glutamine, and increased ability to form lipid droplets.

Weaknesses:

While this finding is intriguing and interesting, the study falls short of explaining the mechanistic reasons for the observed quantitative proteome differences. It remains unclear whether the increased expression of proteins in ihPSCs is due to enhanced transcription of the genes encoding this group of proteins or due to other reasons, for example, differences in mRNA translation efficiency. Another unresolved question pertains to how the cell type origin influences ihPSC proteomes. For instance, whether ihPSCs derived from fibroblasts, lymphocytes, and other cell types all exhibit differences in their cell size and increased expression of cytoplasmic and mitochondrial proteins. Analyzing ihPSCs derived from different cell types and by different investigators would be necessary to address these questions.

We agree with the Reviewer that our study does not provide a mechanistic reason for the quantitative differences between the two cell types. However, we will include an expanded section in the discussion where we discuss the potential causes.<br /> We also agree studying hiPSCs reprogrammed from different cell types, such as blood lymphocytes, would be of great interest and will include a section about this within the discussion to encourage further research into the area.

Reviewer #3 (Public Review):

Summary:

In this study, Brenes and colleagues carried out proteomic analysis of several human induced pluripotent (hiPSC) and human embryonic stem cell (hESC) lines. The authors found quantitative differences in the expression of several groups of cytoplasmic and mitochondrial proteins. Overall, hiPSC expressed higher levels of proteins such as glutamine transporters, mitochondrial metabolism proteins, and proteins related to lipid synthesis. Based on the protein expression differences, the authors propose that hiPSC lines differ from hESC in their growth and metabolism.

Strengths:

The number of generated hiPSC and hESC lines continues to grow, but potential differences between hiPSC and hESC lines remain to be quantified and explained. This study is a promising step forward in understanding of the differences between different hiPSC and hESC lines.

Weaknesses:

It is unclear whether changes in protein levels relate to any phenotypic features of cell lines used. For example, the authors highlight that increased protein expression in hiPSC lines is consistent with the requirement to sustain high growth rates, but there is no data to demonstrate whether hiPSC lines used indeed have higher growth rates.

We respectfully disagree with the reviewer on this point. Our data shows that hESCs and hiPSCs show significant differences in protein mass and cell size, validated by the EZQ assay and FACS, while having no significant differences in their cell cycle profiles. Thus increased size and protein content would require higher growth rates to sustain the increased mass, which is what we show.

The authors claim that the cell cycle of the lines is unchanged. However, no details of the method for assessing the cell cycle were included so it is difficult to appreciate if this assessment was appropriately carried out and controlled for.<br /> We apologise for this omission; the details will be included in the revised version of the document.

Details and characterisation of iPSC and ESC lines used in this study were overall lacking. The lines used are merely listed in methods, but no references are included for published lines, how lines were obtained, what passage they were used at, their karyotype status, etc. For details of basic characterisation, the authors should refer to the ISSC Standards for the use of human stem cells in research. In particular, the authors should consider whether any of the changes they see may be attributed to copy number variants in different lines.

We agree with the reviewer on this. The hiPSC lines were generated by the HipSci consortium in the Wellcome Sanger Centre as described in the flagship HipSci paper13. We cite the flagship paper which specifies in great detail the reprogramming protocols and quality control measures, including looking at copy number variations13. However, we agree that we did not make this information easily accessible for readers. We also believe it is relevant to also explicitly include this information on our manuscript instead of expecting readers to look at the flagship paper. These details will be added to the revised version.

The expression data for markers of undifferentiated state in Figure 1a would ideally be shown by immunocytochemistry or flow cytometry as it is impossible to tell whether cultures are heterogeneous for marker expression.

We agree with the reviewer on this. FACS is indeed much more quantitative and a better method to study heterogeneity. However, we did not have protocols to study these markers using FACS.

TEM analysis should ideally be quantified.

We agree with the reviewer that it would be nice to have a quantitative measure.

All figure legends should explicitly state what graphs are representing (e.g. average/mean; how many replicates (biological or technical), which lines)? Some data is included in Methods (e.g. glutamine uptake), but not for all of the data (e.g. TEM).

We agree with the reviewer completely. These points will be remediated in the revised version of the manuscript.

Validation experiments were performed typically on one or two cell lines, but the lines used were not consistent (e.g. wibj_2 versus H1 for respirometry and wibj_2, oaqd_3 versus SA121 and SA181 for glutamine uptake). Can the authors explain how the lines were chosen?

We will include these details within the updated manuscript.

The authors should acknowledge the need for further functional validation of the results related to immunosuppressive proteins.

We agree with the reviewer and will add a clear sentence in the discussion making this point explicitly.

Differences in H1 histone abundance were highlighted. Can the authors speculate as to the meaning of these differences?

Regarding H1 histones, our study of the literature as well as interaction with chromatin and histone experts both within our institute and externally have not shed light into what the differences could imply. We think this is an interesting result that merits further study, but we don’t have a clear hypothesis on the consequences.

In summary, we thank the reviewers for their comments and will prepare a revised version that addresses their suggestions.

Author Response

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

Reviewer #1 (Public Review):

Assessment:

The manuscript titled 'Rab7 dependent regulation of goblet cell protein CLCA1 modulates gastrointestinal 1 homeostasis' by Gaur et al discusses the role of Rab7 in the development of ulcerative colitis by regulating the lysosomal degradation of Clca1, a mucin protease. The manuscript presents interesting data and provides a potential molecular mechanism for the pathological alterations observed in ulcerative colitis. Gaur et al demonstrate that Rab7 levels are lowered in UC and CD. However, a similar analysis of Rab7 levels in ulcerative colitis (UC) and Crohn's disease (CD) patient samples was conducted recently (Du et al, Dev Cell, 2020) which showed that Rab7 levels are found to be elevated under these conditions. While Gaur et al have briefly mentioned Du et al's paper in passing in the discussion, they need to discuss these contradictory results in their paper and clarify these differences. Additionally, Du et al are not included in the list of references.

Strengths:

The manuscript used a multi-pronged approach and compares patient samples, mouse models of DSS, and protocols that allow differentiation of goblet cells. They also use a nanogel-based delivery system for siRNAs, which is ideal for the knockdown of specific genes in the gut.

Weaknesses:

(1) Du et al, Dev Cell 2020 (https://doi.org/10.1016/j.devcel.2020.03.002) have previously shown that Rab7 levels are elevated in a similar set of colonic samples (age group, number etc.) from UC and CD patients. Gaur et al have not discussed this paper or its findings in detail, which directly contradicts their results. Clarification regarding this should be provided.

We thank and appreciate the reviewer for bringing this point.

The results shown by Du et al, Dev Cell, 2020 depict elevated expression of Rab7 in UC and CD patients compared to controls. In first occurrence, these results appear contradictory, but there may be a few possible explanations for this.

Firstly, Rab7 expression levels may fluctuate in the tissue depending on the degree of the gut inflammation. This can be concluded from our observations in DSS-mice dynamics model and the human patient samples with mild and moderate UC. Furthermore, Du et al provide no information of the severity of the condition among the patients employed in the study. Our motive, in the current work, was to emphasize this aspect. This point was mentioned in the discussion section of the manuscript. However, in view of the reviewer’s concern, we have now added a detailed comment on this in the main text of the revised version of the manuscript.

Secondly, the control biopsies in our investigation were acquired from non-IBD patients, and not what was done by Du et al., wherein biopsies from the normal para-carcinoma region of the colorectal cancer patients were used. One cannot overlook the fact that physiological and molecular changes are apparent even in non-inflamed regions in the gut of an IBD or CRC patient. It is possible that the observed discrepancy arises due to the differences in the sample type used for comparing the Rab7 expression.

Finally, the main sub-tissue region showing a decrease in Rab7 expression in UC samples, appeared to be the Goblet cells which was not covered by Du et al.

Keeping these points in mind we do not think that there is a contradiction in our findings with that of Du et al., 2020. In the revised submission some of these explanations are incorporated (Lines 106-109).

This was an oversight from our side. We have actually mentioned Du et al., 2020 in the discussion (line number 345) but somehow the reference was missing in the main list. We have ensured that the reference is included in the revised version and that their findings are included both in main text and in the discussion.

Reviewer #2 (Public Review):

Summary:

In this work, the authors report a role for the well-studied GTPase Rab7 in gut homeostasis. The study combines cell culture experiments with mouse models and human ulcerative colitis patient tissues to propose a model where, Rab7 by delivering a key mucous component CLCA1 to lysosomes, regulates its secretion in the goblet cells. This is important for the maintenance of mucous permeability and gut microbiota composition. In the absence of Rab7, CLCA1 protein levels are higher in tissues as well as the mucus layer, corroborating with the anticorrelation of Rab7 (reduced) and CLCA1 (increased) from ulcerative colitis patients. The authors conclude that Rab7 maintains CLCA1 level by controlling its lysosomal degradation, thereby playing a vital role in mucous composition, colon integrity, and gut homeostasis.

Strengths:

The biggest strength of this manuscript is the combination of cell culture, mouse model, and human tissues. The experiments are largely well done and, in most cases, the results support their conclusions. The authors go to substantial lengths to find a link, such as alteration in microbiota, or mucus proteomics.

Weaknesses:

(1) There are also some weaknesses that need to be addressed. The association of Rab7 with UC in both mice and humans is clear, however, claims on the underlying mechanisms are less clear. Does Rab7 regulate specifically CLCA1 delivery to lysosomes, or is it an outcome of a generic trafficking defect?

We thank the reviewer for the insightful comment. We would like to bring forth the following explanation for each these concerns:

Our immunofluorescence imaging experiments revealed co-localization of Rab7 protein with CLCA1 and the lysosomes (Fig 7I). In addition, the absence of Rab7 affects the transport of CLCA1 to lysosomes (Fig 7J). This demonstrates that Rab7 may be involved in regulation of CLCA1 transport (presumably along with other cargo), to lysosomes selectively. However, we do recognize that the point raised by the reviewer about possible effect of a generic trafficking defect is valid.

(2) CLCA1 is a secretory protein, how does it get routed to lysosomes, i.e., through Golgi-derived vesicles, or by endocytosis of mucous components? Mechanistic details on how CLCA1 is routed to lysosomes will add substantial value.

As mentioned in the manuscript, the trafficking of CLCA1 protein or CLCA1-containing vesicles within the goblet cell is unknown, with no information on the proteins involved in its mobility. The switching of CLCA1 containing vesicles from the secretory route to lysosomes needs extensive investigation involving overall trafficking of the protein. Taken together, the complete answer to both these important questions will need a series of experiments and those may be interesting avenues for future research.

(3) Why does the level of Rab7 fluctuate during DSS treatment (Fig 1B)?

This is a very thoughtful point from the reviewer. We detected a distinct pattern of Rab7 expression fluctuation in intestinal epithelial cells after DSS-dynamics treatment in mice. Perhaps, these changes are the result of complex cellular signaling in response to the DSS treatment. Rab7, being a fundamental protein involved in protein sorting pathway, is expected to undergo alteration based on cells requirement. Presently there are no reports suggesting the regulatory mechanisms that govern Rab7 levels in the gut.

(4) Does the reduction seen in Rab7 levels (by WB) also reflect in reduced Rab7 endosome numbers?

We observed reduction in Rab7 expression both at RNA and protein levels. To confirm whether this alteration will lead to reduced Rab7 positive endosome numbers may require detailed investigations.

(5) Are other late endosomal (and lysosomal) populations also reduced upon DSS treatment and UC? Is there a general defect in lysosomal function?

There are no direct evidences showing reduction in the late endosomal and lysosomal population during gut inflammation, but few studies link lysosomal dysfunction with risk for colitis (doi: 10.1016/j.immuni.2016.05.007).

(6) The evidence for lysosomal delivery of CLCA1 (Fig 7 I, J) is weak. Although used sometimes in combination with antibodies, lysotracker red is not well compatible with permeabilization and immunofluorescence staining. The authors can substantiate this result further using lysosomal antibodies such as Lamp1 and Lamp2. For Fig 7J, it will be good to see a reduction in Rab7 levels upon KD in the same cell.

We used Lysotracker red in live cells followed by fixation. So, permeabilization issues were resolved. Lamp1, as suggested by the reviewer, is definitely a better marker for lysosomes in immunofluorescence studies, but is also shown to mark late endosomes (doi: 10.1083/jcb.132.4.565). As Rab7 protein also marks the late endosomes, using Lamp1 may leave the ambiguity of CLCA1 in Rab7 positive late endosomes versus lysosomes. Nevertheless, we have carried out this experiment, as suggested by the reviewer, by staining the cells with LAMP1 (author response image 1). As demonstrated in our previous data, the colocalization of CLCA1 with LAMP1 positive vesicles decreased upon Rab7 knockdown. Also, we observed a decrease in the intensity of LAMP1 staining in cells with Rab7 knockdown. Additionally, we noted a reduction in the LAMP1 staining intensity in cells where Rab7 was knocked down. This observation can be attributed to the decrease in the presence of Rab7-positive vesicles or late endosomes which also exhibit LAMP1 staining.

Author response image 1.

(A) Representative confocal images of HT29-MTX-E12 cells transfected with either scrambled siRNA (control) or Rab7 siRNA (Rab7Knockdown). Cells are stained with CLCA1 (green) using antiCLCA1 antibody and lysosomes with LAMP1. (B) Graph shows quantitation of colocalization between CLCA1 and LAMP1 from images (n=20) using Mander’s overlap coefficient. Inset shows zoomed areas of the image with colocalization puncta (yellow) marked with arrows.

(7) In this connection, Fig S3D is somewhat confusing. While it is clear that the pattern of Muc2 in WT and Rab7-/- cells are different, how this corroborates with the in vivo data on alterations in mucus layer permeability -- as claimed -- is not clear.

The data in Fig. S3D suggest the involvement of Rab7 in packaging of Muc2. The whole idea for doing this experiment was to support our observation in the Rab7KD-mice model where mucus layer was seen to be loose and more permeable in Rab7 deficient mice.

(8) Overall, the work shows a role for a well-studied GTPase, Rab7, in gut homeostasis. This is an important finding and could provide scope and testable hypotheses for future studies aimed at understanding in detail the mechanisms involved.

We thank the reviewer for this comment.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Specific questions to the authors:

(1) Why is the dotted line in Fig. 1c at -7.5? What does this signify?

Response: The dotted line was intended to represent the baseline; in the revised manuscript it is corrected and placed at y=0.

(2) Du et al should be cited. Fig 6 K-Q from Du et al should be discussed and reasons for contradictory findings should be given in greater detail, rather than a single sentence in the discussion.

Response: The reference for Du et al is included in the list and the possible reasons the findings of the current work are discussed in the main text (Line 106-109).

(3) Fig1. Why are Rab7 levels low even in remission patient samples? Can DSS be withdrawn to induce remission followed by analysis of colonic samples?

Response: A possible explanation for this observation could be that the restoration of Rab7 levels may not immediately follow the resolution of clinical symptoms in remission patients. After the remission initiation, the normalization of cellular processes, including the regulation of Rab7 expression, might exhibit a time lag. A thorough investigation of Rab7 levels and the allied pathways at different time points during the remission phase could provide deeper insights into the gradual dynamics of recovery. As suggested by the reviewer, DSS withdrawal induced recovery model can be utilized for understanding the same and could be a good approach for future investigations.

(4) Fig. 2: Single-channel fluorescence should be shown.

Response: The single channel fluorescence images are incorporated in Fig. S2.

(5) Line 456 should be modified. 'Blind pathologist' does not read well!

Response: The line has been modified with ‘Blinded pathologist’.

(6) Other inflammatory markers, cytokine levels should be looked at in addition to TNF alpha.

Response: TNF-α is a crucial mediator in intestinal inflammation, actively contributing to the development of IBD. Elevated levels of TNF-α are observed in patients of IBD (Billmeier U. et al, World J Gastroenterol. 2016). In the current work, while probing for TNF-α our primary objective was to examine this significant indicator of colitis following Rab7 knockdown in mice, aiming to gain insights into heightened gut inflammation.

(7) Quantitation of S3D should be provided.

Response: The dispersed expression of Muc2 was observed in n=20 cells per sample and it was a qualitative observation. The aim was to identify any changes in Muc2 packaging under Rab7 knockout conditions.

(8) Microbiota analysis should include Rab7KD+DSS mice.

Response: We understand the importance of this point, however, in the current work our primary objective was to specifically investigate changes in microbial diversity and abundance in Rab7KD mice compared to both DSS+CScr and CScr mice. Rab7KD+DSS mice is expected to show higher dysbiosis in comparison to DSS+CScr.

(9) Fig 6 H and I, G. How do Clca1 levels reduce in Rab7kd +DSS relative to Scr+DSS while they are higher in Rab7kd compared to Scr. Comment.

Response: The decreased expression of CLCA1 in the mucus of DSS+Rab7KD mice can be attributed to a consequence of significant reduction in goblet cell numbers in these mice, as evidenced by the observed loss of these cells (Fig.S3 B and Fig. S3C). CLCA1 is exclusively secreted by goblet cells, so a decline in their numbers directly affects CLCA1 levels.

(10) How are Rab7 levels downregulated? What is the predicted mechanism?

Response: While our current study didn't explore this aspect, it's worth noting that Rab7 protein levels undergo regulation through various mechanisms, including post-translational modifications such as Ubiquitination and SUMOylation. These modifications are known to regulate Rab7 stability, transport and recycling. Specific experiments conducted during this study (work not included in the manuscript) indicated the participation of SENP7, a deSUMOylase, in controlling the stability of Rab7 protein, particularly in the context of colitis. Additionally, goblet cell specific mechanisms are also likely to be controlling the Rab7 in the gut.

(11) What is the explanation for opposite changes in CLCa1 RNA (down) and protein (up).

Response: The reduction in CLCA1 at the RNA level could be associated with the decrease in goblet cell numbers during colitis. Our investigation indicates that Rab7 predominantly influences CLCA1 at the protein level by impacting its degradation pathway. It is important to acknowledge that not all the alterations in CLCA1 observed during colitis can be solely attributed to Rab7, but our study has identified a connection between Rab7 and CLCA1.

(12) In light of Du et al, it would be interesting to see how the number of peroxisomes changes upon alteration of Rab7 levels.

Response: The suggestion by the reviewer is noteworthy. Since, being an altogether different domain, it deviates from the primary objectives of current work. Here, our goal was specifically on exploring the role of Rab7 in goblet cell functioning. Thus is an attractive theme for future investigations.

(13) While Gaur et al suggest in their discussion that Du et al may have observed an upregulation in Rab7 levels in different cell types of the intestine, this is not apparent from the data provided. Tissue sections should be carefully analysed to provide data supporting this observation. Differences in reagents used (antibodies) should also be considered. As far as the human patient data is concerned, it does not appear that the sample stages are very different across the two manuscripts (based on age, inclusion criteria etc.).

Response: This has been explained in detail in our public comments.

Reviewer #2 (Recommendations For The Authors):

(1) In general, image-based measurements could be done better (for example, object-based statistics than pixel-based overlaps) and represented differently. It is difficult to appreciate the reduction in Rab7 levels in goblet cells in Fig 2 A, C. It might be good to show the channels separately, and perhaps use an intensity gradient LUT for the Rab7 channel.

Response: The single channel fluorescence images are incorporated in Fig. S2.

(2) The EM images, and particularly Fig 2F are not convincing, with an oddly square-shaped vesicle. I'm not sure what value they are adding to the interpretation.

Response: The observed square-shaped vesicle in Fig. 2F could be attributed to the dynamic nature of vesicles within a cell. This dynamicity allows them to adopt various shapes depending on their state and function within the cell. The presence of Rab7 near vacuoles of goblet cells signify its probable involvement in the regulation of secretory function of these cells which is the key aspect being covered in this work.

(3) A general method question concerns the definition of the distal colon. How is this decided, particularly when colon lengths are reduced upon DSS treatment?

Response: The murine colon is divided into proximal and distal colon of mouse and has a visual difference of inner folds which are quite prominent in proximal colon. Additionally, the portion towards the rectum (predominantly distal colon) was majorly utilized for the experiments. In each case the various experimental groups were matched for the respective areas.

(4) The use of an in vivo intestine-specific Rab7 silencing model is good. Why does Rab7 KD itself not capitulate aspects of DSS treatment, rather it seems to exacerbate it.

Response: Our objective was to determine whether the downregulation of Rab7 during colitis was the cause or consequence of gut inflammation. Interestingly, our investigation using the murine Rab7 knockdown model revealed that the reduction of Rab7 expression in the intestine exacerbates inflammation. Subsequent analysis demonstrated that the absence of Rab7 disrupts goblet cell secretory function, consequently contributing to heightened inflammation. Our findings overall suggest that Rab7 downregulation is not merely a consequence but plays a contributory role in aggravating inflammation in the context of colitis.

(5) The axes labels in Fig 5 are not readable. It is unclear how Rab7 KD is more similar in gut microbiota phenotypes to DSS than to CScr.

Response: The microbial analysis revealed an abnormal composition of gut microbiota in Rab7KD mice compared to CScr. Interestingly, this composition exhibited some similarity to the inflamed gut microbiota observed in DSSScr mice. The analysis further demonstrated a shift in microbial diversity in Rab7KD mice, showcasing characteristics akin to those observed in inflamed mice. This similarity in gut microbiota phenotypes between Rab7KD and DSSScr suggests a potential link or influence of Rab7 downregulation on the microbiota, contributing to the observed similarities with DSS-induced inflammation.

(6) The use of mucous proteomics to identify mechanisms of Rab7-mediated phenotype is a good approach. The replicates in the proteomics dataset (Fig 6F) do not seem to match. Detailing of methodology used for analysis will help to overcome these doubts.

Response: The identified proteins in different samples of mucus proteomics were subjected to label free quantification. Subsequently, the significantly altered proteins were subjected to analysis with the False Discovery Rate (FDR) to control for potential false positives and ascertain the validity of the findings.

(7) It will be good to see the immunoblots showing the negative correlation between Rab7 and CLCL1 in Fig 7D.

Response: Fig. 7C shows western blot for protein expression of CLCA1of the same control and UC samples which were used in Fig. 1F to show Rab7 expression. Fig. 7D is the quantitative correlation plot for Fig. 1F (Rab7 expression) and Fig. 7C (CLCA1 expression).

(8) Why is UC different from the DSS model for Rab7 gene expression but not protein levels? Endosomal counts could help address this.

Response: We encountered challenges in accurately counting the individual puncta of Rab7 expression in immunofluorescence images due to the nature of tissue samples. Locating endosomes within a single cell proved to be challenging, and the proximity of many puncta made it difficult to delineate them individually. Despite these technical difficulties, the intriguing prospect of correlating Rab7 expression with endosomal counts remains a compelling aspect that may well be area for future investigations.

Author Response

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

eLife assessment

This study uses a multi-pronged empirical and theoretical approach to advance our understanding of how differences in learning relate to differences in the ways that male versus female animals cope with urban environments, and more generally how reversal learning may benefit animals in urban habitats. The work makes an important contribution and parts of the data and analyses are solid, although several of the main claims are only partially supported or overstated and require additional support.

Public Reviews:

We thank the Editor and both Reviewers for their time and for their constructive evaluation of our manuscript. We worked to address each comment and suggestion offered by the Reviewers in our revision—please see our point-by-point responses below.

Reviewer #1 (Public Review):

Summary:

In this highly ambitious paper, Breen and Deffner used a multi-pronged approach to generate novel insights on how differences between male and female birds in their learning strategies might relate to patterns of invasion and spread into new geographic and urban areas.

The empirical results, drawn from data available in online archives, showed that while males and females are similar in their initial efficiency of learning a standard color-food association (e.g., color X = food; color Y = no food) scenario when the associations are switched (now, color Y = food, X= no food), males are more efficient than females at adjusting to the new situation (i.e., faster at 'reversal learning'). Clearly, if animals live in an unstable world, where associations between cues (e.g., color) and what is good versus bad might change unpredictably, it is important to be good at reversal learning. In these grackles, males tend to disperse into new areas before females. It is thus fascinating that males appear to be better than females at reversal learning. Importantly, to gain a better understanding of underlying learning mechanisms, the authors use a Bayesian learning model to assess the relative role of two mechanisms (each governed by a single parameter) that might contribute to differences in learning. They find that what they term 'risk sensitive' learning is the key to explaining the differences in reversal learning. Males tend to exhibit higher risk sensitivity which explains their faster reversal learning. The authors then tested the validity of their empirical results by running agent-based simulations where 10,000 computersimulated 'birds' were asked to make feeding choices using the learning parameters estimated from real birds. Perhaps not surprisingly, the computer birds exhibited learning patterns that were strikingly similar to the real birds. Finally, the authors ran evolutionary algorithms that simulate evolution by natural selection where the key traits that can evolve are the two learning parameters. They find that under conditions that might be common in urban environments, high-risk sensitivity is indeed favored.

Strengths:

The paper addresses a critically important issue in the modern world. Clearly, some organisms (some species, some individuals) are adjusting well and thriving in the modern, human-altered world, while others are doing poorly. Understanding how organisms cope with human-induced environmental change, and why some are particularly good at adjusting to change is thus an important question.

The comparison of male versus female reversal learning across three populations that differ in years since they were first invaded by grackles is one of few, perhaps the first in any species, to address this important issue experimentally.

Using a combination of experimental results, statistical simulations, and evolutionary modeling is a powerful method for elucidating novel insights.

Thank you—we are delighted to receive this positive feedback, especially regarding the inferential power of our analytical approach.

Weaknesses:

The match between the broader conceptual background involving range expansion, urbanization, and sex-biased dispersal and learning, and the actual comparison of three urban populations along a range expansion gradient was somewhat confusing. The fact that three populations were compared along a range expansion gradient implies an expectation that they might differ because they are at very different points in a range expansion. Indeed, the predicted differences between males and females are largely couched in terms of population differences based on their 'location' along the rangeexpansion gradient. However, the fact that they are all urban areas suggests that one might not expect the populations to differ. In addition, the evolutionary model suggests that all animals, male or female, living in urban environments (that the authors suggest are stable but unpredictable) should exhibit high-risk sensitivity. Given that all grackles, male and female, in all populations, are both living in urban environments and likely come from an urban background, should males and females differ in their learning behavior? Clarification would be useful.

Thank you for highlighting a gap in clarity in our conceptual framework. To answer the Reviewer’s question—yes, even with this shared urban ‘history’, it seems plausible that males and females could differ in their learning. For example, irrespective of population membership, such sex differences could come about via differential reliance on learning strategies mediated by an interaction between grackles’ polygynous mating system and malebiased dispersal system, as we discuss in L254–265 (now L295–306). Population membership might, in turn, differentially moderate the magnitude of any such sex-effect since an edge population, even though urban, could still pose novel challenges—for example, by requiring grackles to learn novel daily temporal foraging patterns such as when and where garbage is collected (grackles appear to track this food resource: Rodrigo et al. 2021 [DOI: 10.1101/2021.06.14.448443]). We now introduce this important conceptual information— please see L89–96.

Reinforcement learning mechanisms:

Although the authors' title, abstract, and conclusions emphasize the importance of variation in 'risk sensitivity', most readers in this field will very possibly misunderstand what this means biologically. Both the authors' use of the term 'risk sensitivity' and their statistical methods for measuring this concept have potential problems.

Please see our below responses concerning our risk-sensitivity term.

First, most behavioral ecologists think of risk as predation risk which is not considered in this paper. Secondarily, some might think of risk as uncertainty. Here, as discussed in more detail below, the 'risk sensitivity' parameter basically influences how strongly an option's attractiveness affects the animal's choice of that option. They say that this is in line with foraging theory (Stephens and Krebs 2019) where sensitivity means seeking higher expected payoffs based on prior experience. To me, this sounds like 'reward sensitivity', but not what most think of as 'risk sensitivity'. This problem can be easily fixed by changing the name of the term.

We apologise for not clearly introducing the field of risk-sensitive foraging, which focuses on how animals evaluate and choose between distinct food options, and how such foraging decisions are influenced by pay-off variance i.e., risk associated with alternative foraging options (seminal reviews: Bateson 2002 [DOI: 10.1079/PNS2002181]; Kacelnik & Bateson 1996 [DOI: 10.1093/ICB/36.4.402]). We have added this information to our manuscript in L494–497. We further apologise for not clearly explaining how our lambda parameter estimates such risk-sensitive foraging. To do so here, we need to consider our Bayesian reinforcement learning model in full. This model uses observed choice-behaviour during reinforcement learning to infer our phi (information-updating) and lambda (risksensitivity) learning parameters. Thus, payoffs incurred through choice simultaneously influence estimation of each learning parameter—that is, in a sense, they are both sensitive to rewards. But phi and lambda differentially direct any reward sensitivity back on choicebehaviour due to their distinct definitions. Glossing over the mathematics, for phi, stronger reward sensitivity (bigger phi values) means faster internal updating about stimulus-reward pairings, which translates behaviourally into faster learning about ‘what to choose’. For lambda, stronger reward sensitivity (bigger lambda values) means stronger internal determinism about seeking the non-risk foraging option (i.e., the one with the higher expected payoffs based on prior experience), which translates behaviourally into less choice-option switching i.e., ‘playing it safe’. We hope this information, which we have incorporated into our revised manuscript (please see L153–161), clarifies the rationale and mechanics of our reinforcement learning model, and why lamba measures risk-sensitivity.

In addition, however, the parameter does not measure sensitivity to rewards per se - rewards are not in equation 2. As noted above, instead, equation 2 addresses the sensitivity of choice to the attraction score which can be sensitive to rewards, though in complex ways depending on the updating parameter. Second, equations 1 and 2 involve one specific assumption about how sensitivity to rewards vs. to attraction influences the probability of choosing an option. In essence, the authors split the translation from rewards to behavioral choices into 2 steps. Step 1 is how strongly rewards influence an option's attractiveness and step 2 is how strongly attractiveness influences the actual choice to use that option. The equation for step 1 is linear whereas the equation for step 2 has an exponential component. Whether a relationship is linear or exponential can clearly have a major effect on how parameter values influence outcomes. Is there a justification for the form of these equations? The analyses suggest that the exponential component provides a better explanation than the linear component for the difference between males and females in the sequence of choices made by birds, but translating that to the concepts of information updating versus reward sensitivity is unclear. As noted above, the authors' equation for reward sensitivity does not actually include rewards explicitly, but instead only responds to rewards if the rewards influence attraction scores. The more strongly recent rewards drive an update of attraction scores, the more strongly they also influence food choices. While this is intuitively reasonable, I am skeptical about the authors' biological/cognitive conclusions that are couched in terms of words (updating rate and risk sensitivity) that readers will likely interpret as concepts that, in my view, do not actually concur with what the models and analyses address.

To answer the Reviewer’s question—yes, these equations are very much standard and the canonical way of analysing individual reinforcement learning (see: Ch. 15.2 in Computational Modeling of Cognition and Behavior by Farrell & Lewandowsky 2018 [DOI: 10.1017/CBO9781316272503]; McElreath et al. 2008 [DOI: 10.1098/rstb/2008/0131]; Reinforcement Learning by Sutton & Barto 2018). To provide a “justification for the form of these equations'', equation 1 describes a convex combination of previous values and recent payoffs. Latent values are updated as a linear combination of both factors, there is no simple linear mapping between payoffs and behaviour as suggested by the reviewer. Equation 2 describes the standard softmax link function. It converts a vector of real numbers (here latent values) into a simplex vector (i.e., a vector summing to 1) which represents the probabilities of different outcomes. Similar to the logit link in logistic regression, the softmax simply maps the model space of latent values onto the outcome space of choice probabilities which enter the categorial likelihood distribution. We can appreciate how we did not make this clear in our manuscript by not highlighting the standard nature of our analytical approach—we now do so in our revised manuscript (please see L148–149). As far as what our reinforcement learning model measures, and how it relates cognition and behaviour, please see our previous response.

To emphasize, while the authors imply that their analyses separate the updating rate from 'risk sensitivity', both the 'updating parameter' and the 'risk sensitivity' parameter influence both the strength of updating and the sensitivity to reward payoffs in the sense of altering the tendency to prefer an option based on recent experience with payoffs. As noted in the previous paragraph, the main difference between the two parameters is whether they relate to behaviour linearly versus with an exponential component.

Please see our two earlier responses on the mechanics of our reinforcement learning model.

Overall, while the statistical analyses based on equations (1) and (2) seem to have identified something interesting about two steps underlying learning patterns, to maximize the valuable conceptual impact that these analyses have for the field, more thinking is required to better understand the biological meaning of how these two parameters relate to observed behaviours, and the 'risk sensitivity' parameter needs to be re-named.

Please see our earlier response to these suggestions.

Agent-based simulations:

The authors estimated two learning parameters based on the behaviour of real birds, and then ran simulations to see whether computer 'birds' that base their choices on those learning parameters return behaviours that, on average, mirror the behaviour of the real birds. This exercise is clearly circular. In old-style, statistical terms, I suppose this means that the R-square of the statistical model is good. A more insightful use of the simulations would be to identify situations where the simulation does not do as well in mirroring behaviour that it is designed to mirror.

Based on the Reviewer’s summary of agent-based forward simulation, we can see we did a poor job explaining the inferential value of this method—we apologise. Agent-based forward simulations are posterior predictions, and they provide insight into the implied model dynamics and overall usefulness of our reinforcement learning model. R-squared calculations are retrodictive, and they say nothing about the causal dynamics of a model. Specifically, agent-based forward simulation allows us to ask—what would a ‘new’ grackle ‘do’, given our reinforcement learning model parameter estimates? It is important to ask this question because, in parameterising our model, we may have overlooked a critical contributing mechanism to grackles’ reinforcement learning. Such an omission is invisible in the raw parameter estimates; it is only betrayed by the parameters in actu. Agent-based forward simulation is ‘designed’ to facilitate this call to action—not to mirror behavioural results. The simulation has no apriori ‘opinion’ about computer ‘birds’ behavioural outcomes; rather, it simply assigns these agents random phi and lambda draws (whilst maintaining their correlation structure), and tracks their reinforcement learning. The exercise only appears circular if no critical contributing mechanism(s) went overlooked—in this case computer ‘birds’ should behave similar to real birds. A disparate mapping between computer ‘birds’ and real birds, however, would mean more work is needed with respect to model parameterisation that captures the causal, mechanistic dynamics behind real birds’ reinforcement learning (for an example of this happening in the human reinforcement learning literature, see Deffner et al. 2020 [DOI: 10.1098/rsos.200734]). In sum, agent-based forward simulation does not access goodness-of-fit—we assessed the fit of our model apriori in our preregistration (https://osf.io/v3wxb)—but it does assess whether one did a comprehensive job of uncovering the mechanistic basis of target behaviour(s). We have worked to make the above points on the method and the insight afforded by agent-based forward simulation explicitly clear in our revision—please see L192–207 and L534–537.

Reviewer #2 (Public Review):

Summary:

The study is titled "Leading an urban invasion: risk-sensitive learning is a winning strategy", and consists of three different parts. First, the authors analyse data on initial and reversal learning in Grackles confronted with a foraging task, derived from three populations labeled as "core", "middle" and "edge" in relation to the invasion front. The suggested difference between study populations does not surface, but the authors do find moderate support for a difference between male and female individuals. Secondly, the authors confirm that the proposed mechanism can actually generate patterns such as those observed in the Grackle data. In the third part, the authors present an evolutionary model, in which they show that learning strategies as observed in male Grackles do evolve in what they regard as conditions present in urban environments.

Strengths:

The manuscript's strength is that it combines real learning data collected across different populations of the Great-tailed grackle (Quiscalus mexicanus) with theoretical approaches to better understand the processes with which grackles learn and how such learning processes might be advantageous during range expansion. Furthermore, the authors also take sex into account revealing that males, the dispersing sex, show moderately better reversal learning through higher reward-payoff sensitivity. I also find it refreshing to see that the authors took the time to preregister their study to improve transparency, especially regarding data analysis.

Thank you—we are pleased to receive this positive evaluation, particularly concerning our efforts to improve scientific transparency via our study’s preregistration (https://osf.io/v3wxb).

Weaknesses:

One major weakness of this manuscript is the fact that the authors are working with quite low sample sizes when we look at the different populations of edge (11 males & 8 females), middle (4 males & 4 females), and core (17 males & 5 females) expansion range. Although I think that when all populations are pooled together, the sample size is sufficient to answer the questions regarding sex differences in learning performance and which learning processes might be used by grackles but insufficient when taking the different populations into account.

In Bayesian statistics, there is no strict lower limit of required sample size as the inferences do not rely on asymptotic assumptions. With inferences remaining valid in principle, low sample size will of course be reflected in rather uncertain posterior estimates. We note all of our multilevel models use partial pooling on individuals (the random-effects structure), which is a regularisation technique that generally reduces the inference constraint imposed by a low sample size (see Ch. 13 in Statistical Rethinking by Richard McElreath [PDF: https://bit.ly/3RXCy8c]). We further note that, in our study preregistration (https://osf.io/v3wxb), we formally tested our reinforcement learning model for different effect sizes of sex on learning for both target parameters (phi and lambda) across populations, using a similarly modest N (edge: 10 M, 5 F; middle: 22 M, 5 F ; core: 3 M, 4 F) to our actual final N, that we anticipated to be our final N at that time. This apriori analysis shows our reinforcement learning model: (i) detects sex differences in phi values >= 0.03 and lambda values >= 1; and (ii) infers a null effect for phi values < 0.03 and lambda values < 1 i.e., very weak simulated sex differences (see Figure 4 in https://osf.io/v3wxb). Thus, both of these points together highlight how our reinforcement learning model allows us to say that across-population null results are not just due to small sample size. Nevertheless the Reviewer is not wrong to wonder whether a bigger N might change our population-level results (it might; so might muchneeded population replicates—see L310), but our Bayesian models still allow us to learn a lot from our current data. We now explain this in our revised manuscript—please see L452–457.

Another weakness of this manuscript is that it does not set up the background well in the introduction. Firstly, are grackles urban dwellers in their natural range and expand by colonising urban habitats because they are adapted to it? The introduction also fails to mention why urban habitats are special and why we expect them to be more challenging for animals to inhabit. If we consider that one of their main questions is related to how learning processes might help individuals deal with a challenging urban habitat, then this should be properly introduced.

In L74–75 (previously L53–56) we introduce that the estimated historical niche of grackles is urban environments, and that shifts in habitat breadth—e.g., moving into more arid, agricultural environments—is the estimated driver of their rapid North American colonisation. We hope this included information sufficiently answers the Reviewer’s question. We have worked towards flushing out how urban-imposed challenges faced by grackles, such as the wildlife management efforts introduced in L64–65 (now L85–86), may apply to animals inhabiting urban environments more broadly; for example, we now include an entire paragraph in our Introduction detailing how urban environments may be characterised differently to nonurban environments, and thus why they are perhaps more challenging for animals to inhabit— please see L56–71.

Also, the authors provide a single example of how learning can differ between populations from more urban and more natural habitats. The authors also label the urban dwellers as the invaders, which might be the case for grackles but is not necessarily true for other species, such as the Indian rock agama in the example which are native to the area of study. Also, the authors need to be aware that only male lizards were tested in this study. I suggest being a bit more clear about what has been found across different studies looking at: (1) differences across individuals from invasive and native populations of invasive species and (2) differences across individuals from natural and urban populations.

We apologise for not including more examples of such learning differences. We now include three examples (please see L43–49), and we are careful to call attention to the fact that these data cover both resident urban and non-urban species as well as urban invasive species (please see L49–50). We also revised our labelling of the lizard species (please see L44). We are aware only male lizards were tested but this information is not relevant to substantiating our use of this study; that is, to highlight that learning can differ between urbandwelling and non-urban counterparts. We hope the changes we did make to our manuscript satisfy the Reviewer’s general suggestion to add biological clarity.

Finally, the introduction is very much written with regard to the interaction between learning and dispersal, i.e. the 'invasion front' theme. The authors lay out four predictions, the most important of which is No. 4: "Such sex-mediated differences in learning to be more pronounced in grackles living at the edge, rather than the intermediate and/or core region of their range." The authors, however, never return to this prediction, at least not in a transparent way that clearly pronounces this pattern not being found. The model looking at the evolution of risk-sensitive learning in urban environments is based on the assumption that urban and natural environments "differ along two key ecological axes: environmental stability 𝑢 (How often does optimal behaviour change?) and environmental stochasticity 𝑠 (How often does optimal behaviour fail to pay off?). Urban environments are generally characterised as both stable (lower 𝑢) and stochastic (higher 𝑠)". Even though it is generally assumed that urban environments differ from natural environments the authors' assumption is just one way of looking at the differences which have generally not been confirmed and are highly debated. Additionally, it is not clear how this result relates to the rest of the paper: The three populations are distinguished according to their relation to the invasion front, not with respect to a gradient of urbanization, and further do not show a meaningful difference in learning behaviour possibly due to low sample sizes as mentioned above.

Thank you for highlighting a gap in our reporting clarity. We now take care to transparently report our null result regarding our fourth prediction; more specifically, that we did not detect credible population-level differences in grackles’ learning (please see L130). Regarding our evolutionary model, we agree with the Reviewer that this analysis is only one way of looking at the interaction between learning phenotype and apparent urban environmental characteristics. Indeed, in L282–288 (now L325–329) we state: “Admittedly, our evolutionary model is not a complete representation of urban ecology dynamics. Relevant factors—e.g., spatial dynamics and realistic life histories—are missed out. These omissions are tactical ones. Our evolutionary model solely focuses on the response of reinforcement learning parameters to two core urban-like (or not) environmental statistics, providing a baseline for future study to build on”. But we can see now that ‘core’ is too strong a word, and instead ‘supposed’, ‘purported’ or ‘theorised’ would be more accurate—we have revised our wording throughout our manuscript to say as much (please see, for example, L24; L56; L328). We also further highlight the preliminary nature of our evolutionary model, in terms of allowing a narrow but useful first-look at urban eco-evolutionary dynamics—please see L228–232. Finally, we now detail the theorised characteristics of urban environments in our Introduction (rather than in our Results; please see L56–71), and we hope that by doing so, how our evolutionary results relate to the rest of our paper is now better set up and clear.

In conclusion, the manuscript was well written and for the most part easy to follow. The format of eLife having the results before the methods makes it a bit harder to follow because the reader is not fully aware of the methods at the time the results are presented. It would, therefore, be important to more clearly delineate the different parts and purposes. Is this article about the interaction between urban invasion, dispersal, and learning? Or about the correct identification of learning mechanisms? Or about how learning mechanisms evolve in urban and natural environments? Maybe this article can harbor all three, but the borders need to be clear. The authors need to be transparent about what has and especially what has not been found, and be careful to not overstate their case.

Thank you, we are pleased to read that the Reviewer found our manuscript to be generally digestible. We have worked to add further clarity, and to tempter our tone (please see our above and below responses).

Reviewer #1 (Recommendations For The Authors):

Several of the results are based on CIs that overlap zero. Tone these down somewhat.

We apologise for overstating our results, which we have worked to tone down in our revision. For instance, in L185–186 we now differentiate between estimates that did or did not overlap zero (please also see our response to Reviewer 2 on this tonal change). We note we do not report confidence intervals (i.e., the range of values expected to contain the true estimate if one redoes the study/analysis many times). Rather, we report 89% highest posterior density intervals (i.e., the most likely values of our parameters over this range). We have added this definition in L459, to improve clarity.

The literature review suggesting that urban environments are more unpredictable is not convincing. Yes, they have more noise and light pollution and more cars and planes, but does this actually relate to the unpredictability of getting a food reward when you choose an option that usually yields rewards?

To answer the Reviewer’s question—yes. But we can see that by not including empirical examples from the literature, we did a poor job of arguing such links. In L43–49 we now give three empirical examples; more specifically, we state: “[...] experimental data show the more variable are traffic noise and pedestrian presence, the more negative are such human-driven effects on birds' sleep (Grunst et al., 2021), mating (Blickley et al., 2012), and foraging behaviour (Fernández-Juricic, 2000).” We note we now detail such apparently stable but stochastic urban environmental characteristics in our Introduction rather than our Results section, to hopefully improve the clarity of our manuscript (please see L56–71). We further note that we cite three literature reviews—not one—suggesting urban environments are stable in certain characteristics and more unpredictable in others (please see L59–60). Finally, we appreciate such characterisation is not certain, and so in our revision we have qualified all writing about this potential dynamic with words such as “apparent”, “supposed”, “theorised”, “hypothesised” etc.

It would be interesting to see if other individual traits besides sex affect their learning/reversal learning ability and/or their learning parameters. Do you have data on age, size, condition, or personality? Or, the habitat where they were captured?

We do not have these data. But we agree with the Reviewer that examining the potential influence of such covariates on grackles’ reinforcement learning would be interesting in future study, especially habitat characteristics (please see L306–309).

For most levels of environmental noise, there appears to be an intermediate maximum for the relationship between environmental stability and the risk sensitivity parameter. What does this mean?

There is indeed an intermediate maximum for certain values of environmental stochasticity (although the differences are rather small). The most plausible reason for this is that for very stable environments, simulated birds essentially always “know” the rewarded solution and never need to “relearn” behaviour. In this case, differences in latent values will tend to be large (because they consistently get rewarded for the same option), and different lambda values (in the upper range) will produce the same choice behaviour, which results in very weak selection. While in very unstable environments, optimal choice behaviour should be more exploratory, allowing learners to track frequently-changing environments. We now note this pattern in L240–248.

Reviewer #2 (Recommendations For The Authors):

L2: I'd encourage the authors to reconsider the term "risk-sensitive learning", at least in the title. It's not apparent to me how 'risk' relates to the investigated foraging behaviour. Elsewhere, risk-reward sensitivity is used which may be a better term.

We apologise for not clearly introducing the field of risk-sensitive foraging, which focuses on how animals evaluate and choose between distinct food options, and how such foraging decisions are influenced by pay-off variance i.e., risk associated with alternative foraging options (seminal reviews: Bateson 2002 [DOI: 10.1079/PNS2002181]; Kacelnik & Bateson 1996 [DOI: 10.1093/ICB/36.4.402]). We have added this information to our manuscript in L494–497. In explaining our reinforcement model, we also now detail how risk relates to foraging behaviour. Specifically, in L153–161 we now state: “Both learning parameters capture individual-level internal response to incurred reward-payoffs, but they differentially direct any reward sensitivity back on choice-behaviour due to their distinct definitions (full mathematical details in Materials and methods). For 𝜙, stronger reward sensitivity (bigger values) means faster internal updating about stimulus-reward pairings, which translates behaviourally into faster learning about ‘what to choose’. For 𝜆, stronger reward sensitivity (bigger values) means stronger internal determinism about seeking the nonrisk foraging option (i.e., the one with the higher expected payoffs based on prior experience), which translates behaviourally into less choice-option switching i.e., ‘playing it safe’.” We hope this information clarifies why lamba measures risk-sensitivity, and why we continue to use this term.

L1-3: The title is a bit misleading with regard to the empirical data. From the data, all that can be said is that male grackles relearn faster than females. Any difference between populations actually runs the other way, with the core population exhibiting a larger difference between males and females than the mid and edge populations.

It is customary for a manuscript title to describe the full scope of the study. In our study, we have empirical data, cognitive modelling, and evolutionary simulations of the background theory all together. And together these analytical approaches show: (1) across three populations, male grackles—the dispersing sex in this historically urban-dwelling and currently urban-invading species—outperform female counterparts in reversal learning; (2) they do this via risk-sensitive learning, so they’re more sensitive to relative differences in reward payoffs and choose to stick with the ‘safe’ i.e., rewarding option, rather than continuing to ‘gamble’ on an alternative option; and (3) risk-sensitive learning should be favoured in statistical environments characterised by purported urban dynamics. So, we do not feel our title “Leading an urban invasion: risk-sensitive learning is a winning strategy” is misleading with regard to our empirical data; it just doesn’t summarise only our empirical data. Finally, as we now state in L312–313, we caution against speculating about any between-population variation, as we did not infer any meaningful behavioural or mechanistic population-level differences.

L13: "Assayed", is that correctly put, given that the authors did not collect the data?

Merrian-Webster defines assay as “to analyse” or “examination or determination as to characteristics”, and so to answer the Reviewer’s question—yes, we feel this is correctly put. We note we explicitly introduce in L102–103 that we did not collect the data, and we have an explicit “Data provenance” section in our methods (please see L342–347).

L42-46: The authors provide a single example of how learning can differ between populations from more urban and more natural habitats. I would like to point out that many of these studies do not directly confirm that the ability in question has indeed led to the success of the species tested (e.g. show fitness consequences). Then the authors could combine these insights to form a solid prediction for the grackles. As of now, this looks like cherry-picking supportive literature without considering negative results.

Here are some references that might be helpful in identifying relevant literature to cite:

Szabo, B., Damas-Moreira, I., & Whiting, M. J. (2020). Can cognitive ability give invasive species the means to succeed? A review of the evidence. Frontiers in Ecology and Evolution, 8, 187.

Griffin AS, Tebbich S, Bugnyar T, 2017. Animal cognition in a human-dominated world. Anim Cogn 20(1):1-6.

Kark, S., Iwaniuk, A., Schalimtzek, A., & Banker, E. (2007). Living in the city: Can anyone become an "urban exploiter"? Journal of Biogeography, 34(4), 638-651.

We apologise for not including more examples of such learning differences. We now include three examples (please see L43–49). We are aware that direct evidence of fitness consequences is entirely lacking in the scientific literature on cognition and successful urban invasion; hence why such data is not present in our paper. But we now explicitly point out a role for likely fitness-affecting anthropogenic disturbances on sleep, mate, and foraging behaviour on animals inhabiting urban environments (please see L63–68). We hope these new data bolster our predictions for our grackles. Finally, the Reviewer paints a (in our view) inaccurate picture of our use of available literature. Nevertheless, to address their comment, we now highlight a recent meta-analysis advocating for further research to confirm apparent ‘positive’ trends between animal ‘smarts’ and successful ‘city living’ (please see L43).

L64: Is their niche historically urban, or have they recently moved into urban areas?

In L74–75 (previously L53–56) we introduce that the estimated historical niche of grackles is urban environments, and that shifts in habitat breadth—e.g., moving into more arid, agricultural environments—is the estimated driver of their rapid North American colonisation. We hope this included information sufficiently answers the Reviewer’s question.

L66-67: This is an important point that is however altogether missing from the discussion.

We thank the Reviewer for highlighting a gap in our discussion regarding populationlevel differences in grackles’ reinforcement learning. In L310–312 we now state: “The lack of spatial replicates in the existing data set used herein inherently poses limitations on inference. Nevertheless, the currently available data do not show meaningful population-level behavioural or mechanistic differences in grackles’ reinforcement learning, and we should thus be cautious about speculating on between-population variation”.

L68-71: The paper focuses on cognitive ability. The whole paragraph sets up the prediction of why male grackles should be better learners due to their dispersal behaviour. This example, however, focuses on aggression, not cognition. Here is a study showing differences in learning in male and female mynas that might be better suited:

Federspiel IG, Garland A, Guez D, Bugnyar T, Healy SD, Güntürkün O, Griffin AS, 2017. Adjusting foraging strategies: a comparison of rural and urban common mynas (Acridotheres tristis). Anim Cogn 20(1):65-74.

We thank the Reviewer for suggesting this paper. We feel it is better suited to substantiating our point in the Discussion about reversal learning not being indicative of cognitive ability—please see L276–277.

L73: Generally, I suggest not writing "for the first time" as this is not a valid argument for why a study should be conducted. Furthermore, except for replication studies, most studies investigate questions that are novel and have not been investigated before.

The Reviewer makes a fair point—we have removed this statement.

L80-81: Here again, this is left undiscussed later on.

By ‘this’ we assume the Reviewer is referring to our hypothesis, which is that sex differences in dispersal are related to sex differences in learning in an urban invader— grackles. At the beginning of our Discussion, we state how we found support for this hypothesis (please see L250–261); and in our ‘Ideas and speculation’ section, we discuss how these hypothesis-supporting data fit into the literature more broadly (please see L294–331). We feel this is therefore sufficiently discussed.

L77-81: This sentence is very long and therefore hard to read. I suggest trying to split it into at least 2 separate sentences which would improve readability.

Per the Reviewer’s useful suggestion, we have split this sentence into two separate sentences—please see L97–115.

L83: Please explain choice-option switches. I am not aware of what that is and it should be explained at first mention.

We apologise for this operational oversight. We now include a working definition of speed and choice-option switches at first mention. Specifically, in L107–108 we state: “[...] we expect male and female grackles to differ across at least two reinforcement learning behaviours: speed (trials to criterion) and choice-option switches (times alternating between available stimuli)”.

L83-87: Again, a very long sentence. Please split.

We thank the Reviewer for their suggestion. In this case we feel it is important to not change our sentence structure because we want our prediction statements to match between our manuscript and our preregistration.

L96-97: Important to not overstate this. It merely demonstrates the potential of the proposed (not detected) mechanism to generate the observed data.

As in any empirical analysis, our drawn conclusions depend on causal assumptions about the mechanisms generating behaviour (Pearl, J. (2009). Causality). Therefore, we “detected” specific learning mechanisms assuming a certain generative model, namely reinforcement learning. As there is overwhelming evidence for the widespread importance of value-based decision making and Rescorla-Wagner updating rules across numerous different animals (Sutton & Barto (2018) Reinforcement Learning), we would argue that this assumed model is highly plausible in our case. Still, we changed the text to “inferred” instead of “detected” learning mechanisms to account for this concern—please see L123–124.

L99: "urban-like settings" again a bit confusing. The authors talk about invasion fronts, but now also about an urbanisation gradient. Is the main difference between the size and the date of establishment, or is there additionally a gradient in urbanisation to be considered?

We now include a paragraph in our Introduction detailing apparent urban environmental characteristics (please see 56–71), and we now refer to this dynamic specifically when we define urban-like settings (please see L126–127). To answer the Reviewer’s question—we consider both differences. Specifically, we consider the time since population establishment in our paper (with respect to our behavioural and mechanistic modelling), as well as how statistical environments that vary in how similar they are to apparently characteristically urban-like environments, might favour particular learning phenotypes (with respect to our evolutionary modelling). We hope the edits to our Introduction as a whole now make both of the aims clear.

L11-112: Above the authors talk about a comparable number of switches (10.5/15=0.7), and here of fewer number of switches (25/35=0.71), even though the magnitude of the difference is almost identical and actually runs the other way. The authors are probably misled by their conservative priors, which makes the difference appear greater in the second case than in the first. Using flat priors would avoid this particular issue.

Mathematically, the number of trials-to-finish and the number of choice-optionswitches are both a Poisson distributed outcome with rate λ (we note lambda here is not our risk-sensitivity parameter; just standard notation). As such, our Poisson models infer the rate of these outcomes by sex and phase—not the ratio of these outcomes by sex and phase. So comparing the magnitude of divided medians of choice-option-switches between the sexes by phase is not a meaningful metric with respect to the distribution of our data, as the Reviewer does above. For perspective, 1 vs. 2 switches provides much less information about the difference in rates of a Poisson distribution than 50 vs 100 (for the former, no difference would be inferred; for the latter, it would), but both exhibit a 1:2 ratio. To hopefully prevent any such further confusion, and to focus on the fact that our Poisson models estimate the expected value i.e., the mean, we now report and graph (please see Fig. 2) mean and not median trialsto-finish and total-switch-counts. Finally, we can see that our use of the word “conservative” to describe our weakly informative priors is confusing, because conservative could mean either strong priors with respect to expected effect size (not our parameterisation) or weak priors with respect to such assumptions (our parameterisation). To address this lack of clarity, we now state that we use “weakly informative priors” in L457–458.

L126: It is not clear what risk sensitivity means in the context of these experiments.

Thank you for pointing out our lack of clarity. In L153–161 we now state: “Both learning parameters capture individual-level internal response to incurred reward-payoffs, but they differentially direct any reward sensitivity back on choice-behaviour due to their distinct definitions (full mathematical details in Materials and methods). For 𝜙, stronger reward sensitivity (bigger values) means faster internal updating about stimulus-reward pairings, which translates behaviourally into faster learning about ‘what to choose’. For 𝜆, stronger reward sensitivity (bigger values) means stronger internal determinism about seeking the nonrisk foraging option (i.e., the one with the higher expected payoffs based on prior experience), which translates behaviourally into less choice-option switching i.e., ‘playing it safe’.” We hope this information clarifies what risk sensitivity means and measures, with respect to our behavioural experiments.

L128-129: I find this statement too strong. A plethora of other mechanisms could produce similar patterns, and you cannot exclude these by way of your method. All you can show is whether the mechanism is capable of producing broadly similar outcomes as observed

In describing the inferential value of our reinforcement learning model, we now qualify that the insight provided is of course conditional on the model, which is tonally accurate. Please see L161.

L144: As I have already mentioned above, here is the first time we hear about unpredictability related to urban environments. I suggest clearly explaining in the introduction how urban and natural environments are assumed to be different which leads to animals needing different cognitive abilities to survive in them which should explain why some species thrive and some species die out in urbanised habitats.

Thank you for this suggestion. We now include a paragraph in our Introduction detailing as much—please see L56–71.

L162: "almost entirely above zero" again, this is worded too strongly.

In reporting our lambda across-population 89% HPDI contrasts in L185–186, we now state: “[...] across-population contrasts that lie mostly above zero in initial learning, and entirely above zero in reversal learning”. Our previous wording stated: ““[...] across-population contrasts that lie almost entirely above zero”. The Reviewer was correct to point out that this previous wording was too strong if we considered the contrasts together, as, indeed, we find the range of the contrast in initial learning does minimally overlap zero (L: -0.77; U: 5.61), while the range of the contrast in reversal learning does not (L: 0.14; U: 4.26). This rephrasing is thus tonally accurate.

L178-179: I think it should be said instead that the model accounts well for the observed data.

We have rephrased in line with the Reviewer’s suggestion, now stating in L217–218 that “Such quantitative replication confirms our reinforcement learning model results sufficiently explain our behavioural sex-difference data.”

L188-190: I am not convinced this is a general pattern. It is quite a bold claim that I don't find to be supported by the citations. Why should biotic and abiotic factors differ in how they affect behavioural outcomes? Also, events in urban environments such as weekend/weekday could lead to highly regular optimal behaviour changes.

Please see our response to Reviewer 1 on this point. We note we now touch on such regular events in L94–96.

L209-211: The first sentence is misleading. The authors have found that males and females differ in 'risk sensitivity', that their learning model can fit the data rather well, and that under certain, not necessarily realistic assumptions, the male learning type is favoured by natural selection in urban environments. A difference between core, middle, and edge habitats however is barely found, and in fact seems to run the other way than expected.

In our study, we found: (1) across three populations, male grackles—the dispersing sex in this historically urban-dwelling and currently urban-invading species—outperform female counterparts in reversal learning; (2) they do this via risk-sensitive learning, so they’re more sensitive to relative differences in reward payoffs and choose to stick with the ‘safe’ i.e., rewarding option, rather than continuing to ‘gamble’ on an alternative option; (3) we are sufficiently certain risk-sensitive learning generates our sex-difference data, as our agentbased forward simulations replicate our behavioural results (not because our model ‘fits’ the data, but because we inferred meaningful mechanistic differences—see our response to Reviewer 1 on this point); and (4) under theorised dynamics of urban environments, natural selection should favour risk-sensitive learning. We therefore do not feel it is misleading to say that we mapped a full pathway from behaviour to mechanisms through to selection and adaptation. Again, as we now state in L311–313, we caution against speculating about any between-population variation, as we did not infer any meaningful behavioural or mechanistic population-level differences. And we note the Reviewer is wrong to assume an interaction between learning, dispersal, and sex requires population-level differences on the outcome scale—please see our discussion on phenotypic plasticity and inherent species trait(s) in L313–324.

L216: "indeed explain" again worded too strongly.

We have tempered our wording. Specifically, we now state in L218: “sufficiently explain”. This wording is tonally accurate with respect to the inferential value of agent-based forward simulations—please see L192–207 on this point.

L234: "reward-payoff sensitivity" might be a better term than risk-sensitivity?

Please see our earlier response to this suggestion. We note we have changed this text to state “risk-sensitive learning” rather than “reward-payoff sensitivity”, to hopefully prevent the reader from concluding only our lambda term is sensitive to rewards—a point we now include in L153–154.

L234-237: I think these points may be valuable, but come too much out of the blue. Many readers will not have a detailed knowledge of the experimental assays. It therefore also does not become clear how they measure the wrong thing, what this study does to demonstrate this, or whether a better alternative is presented herein. It almost seems like this should be a separate paper by itself.

We apologise for this lack of context. We now explicitly state in L275 that we are discussing reversal learning assays, to give all readers this knowledge. In doing so, we hope the logic of our argument is now clear: reversal learning assays do not measure behavioural flexibility, whatever that even is. The Reviewer’s suggestion of a separate paper focused on what reversal learning assays actually measure, in terms of mechanism(s), is an interesting one, and we would welcome this discussion. But any such paper should build on the points we make here.

L270-288: Somewhere here the authors have to explain how they have not found differences between populations, or that in so far as they found them, they run against the originally stated hypothesis.

We thank the Reviewer for these suggestions. In L310—313 we now state: “The lack of spatial replicates in the existing data set used herein inherently poses limitations on inference. Nevertheless, the currently available data do not show meaningful population-level behavioural or mechanistic differences in grackles’ reinforcement learning, and we should thus be cautious about speculating on between-population variation”.

L284: should be "missing" not "missed out"

We have made this change.

L290-291: It is unclear what "robust interactive links" were found. A pattern of sexbiased learning was found, which can potentially be attributed to evolutionary pressures in urban environments. An interaction e.g. between learning, dispersal, and sex can only be tentatively suggested (no differences between populations). Also "fully replicable" is a bit misleading. The analysis may be replicable, but the more relevant question of whether the findings are replicable we cannot presently answer.

We apologise for our lack of clarity. By “robust” we mean “across population”, which we now state in L333. We again note the Reviewer is wrong to assume an interaction between learning, dispersal, and sex requires population-level differences on the outcome scale— please see our discussion on phenotypic plasticity and inherent species trait(s) in L313–324. Finally, the Reviewer makes a good point about our analyses but not our findings being replicable. In L334 we now make this distinction by stating “analytically replicable”.

L306-315: I think you have a bit of a sample size issue not so much when populations are pooled but when separated. This might also factor in the fact that you do not really find differences across the populations in your analysis. When we look at the results presented in Figure 2 (and table d), we can see a trend towards males having better risk sensitivity in core (HPDI above 0) and middle populations (HPDI barely crossing 0) but the difference is very small. Especially the results on females are based on the performance of only 8 and 4 females respectively. I suggest making this clear in the manuscript.

In Bayesian statistics, there is no strict lower limit of required sample size as the inferences do not rely on asymptotic assumptions. With inferences remaining valid in principle, low sample size will of course be reflected in rather uncertain posterior estimates. We note all of our multilevel models use partial pooling on individuals (the random-effects structure), which is a regularisation technique that generally reduces the inference constraint imposed by a low sample size (see Ch. 13 in Statistical Rethinking by Richard McElreath [PDF: https://bit.ly/3RXCy8c]). We further note that, in our study preregistration (https://osf.io/v3wxb), we formally tested our reinforcement learning model for different effect sizes of sex on learning for both target parameters (phi and lambda) across populations, using a similarly modest N (edge: 10 M, 5 F; middle: 22 M, 5 F ; core: 3 M, 4 F) to our actual final N, that we anticipated to be our final N at that time. This apriori analysis shows our reinforcement learning model: (i) detects sex differences in phi values >= 0.03 and lambda values >= 1; and (ii) infers a null effect for phi values < 0.03 and lambda values < 1 i.e., very weak simulated sex differences (see Figure 4 in https://osf.io/v3wxb). Thus, both of these points together highlight how our reinforcement learning model allows us to say that across-population null results are not just due to small sample size. Nevertheless the Reviewer is not wrong to wonder whether a bigger N might change our population-level results; it might; so might muchneeded population replicates—see L310. But our Bayesian models still allow us to learn a lot from our current data, and, at present, we infer no meaningful population-level behavioural or mechanistic differences in grackles’ behaviour. To make clear the inferential sufficiency of our analytical approach, we now include some of the above points in our Statistical analyses section in L452–457. Finally, we caution against speculating on any between-population variation, as we now highlight in L311—313 of our Discussion.

Figure 2: I think the authors should rethink their usage of colour in this graph. It is not colour-blind friendly or well-readable when printed in black and white.

We used the yellow (hex code: #fde725) and green (hex code: #5ec962) colours from the viridis package. As outlined in the viridis package vignette (https://cran.rproject.org/web/packages/viridis/index.html), this colour package is “designed to improve graph readability for readers with common forms of color blindness and/or color vision deficiency. The color maps are also perceptually-uniform, both in regular form and also when converted to black-and-white for printing”.

Figure 3B: Could the authors turn around the x-axis and the colour code? It would be easier to read this way.

We appreciate that aesthetic preferences may vary. In this case, we prefer to have the numbers on the x-axis run the standard way i.e., from small to large. We note we did remove the word ‘Key’ from this Figure, in line with the Reviewer’s point about these characteristics not being totally certain.

I also had a look at the preregistration. I do think that there are parts in the preregistration that would be worth adding to the manuscript:

L36-40: This is much easier to read here than in the manuscript.

We changed this text generally in the Introduction in our revision, so we hope the Reviewer will again find this easier to read.

L49-56: This is important information that I would also like to see in the manuscript.

We no longer have confidence in these findings, as our cleaning of only one part of these data revealed considerable experimenter oversight (see ‘Learning criterion’).

L176: Why did you remove the random effect study site from the model? It is not part of the model in the manuscript anymore.

The population variable is part of the RL_Comp_Full.stan model that we used in our manuscript to assess population differences in grackles’ reinforcement learning, the estimates from which we report in Table C and D (please note we never coded this variable as “study cite”). But rather than being specified as a random effect, in our RL_Comp_Full.stan model we index phi and lambda by population as a predictor variable, to explicitly model population-level effects. Please see our code:

https://github.com/alexisbreen/Sex-differences-in-grackles- learning/blob/main/Models/Reinforcement%20learning/RL_Comp_Full.stan

L190-228: I am wondering if the model validation should also be part of the manuscript as well, rather than just being in the preregistration?

We are not sure how the files were presented to the Reviewer for review, but our study preregistration, which includes our model validation, should be part of our manuscript as a supplementary file.

Author Response

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

eLife assessment

This fundamental study evaluates the evolutionary significance of variations in the accuracy of the intron-splicing process across vertebrates and insects. Using a powerful combination of comparative and population genomics approaches, the authors present convincing evidence that species with lower effective population size tend to exhibit higher rates of alternative splicing, a key prediction of the drift-barrier hypothesis. The analysis is carefully conducted and all observations fit with this hypothesis, but focusing on a greater diversity of metazoan lineages would make these results even more broadly relevant. This study will strongly appeal to anyone interested in the evolution of genome architecture and the optimisation of genetic systems.

Public Reviews):

Reviewer #1 (Public Review:

Summary:

Functionally important alternative isoforms are gold nuggets found in a swamp of errors produced by the splicing machinery.

The architecture of eukaryotic genomes, when compared with prokaryotes, is characterised by a preponderance of introns. These elements, which are still present within transcripts, are rapidly removed during the splicing of messenger RNA (mRNA), thus not contributing to the final protein. The extreme rarity of introns in prokaryotes, and the elimination of these introns from mRNAs before translation into protein, raises questions about the function of introns in genomes. One explanation comes from functional biology: introns are thought to be involved in post-transcriptional regulation and in the production of translational variants. The latter function is possible when the positions of the edges of the spliced intron vary. While some light has been shed on specific examples of the functional role of alternative splicing, to what extent are they representative of all introns in metazoans?

In this study, the hypothesis of a functional role for alternative splicing, and therefore to a certain extent for introns, is evaluated against another explanation coming from evolutionary biology: isoforms are above all errors of imprecision by the molecular machinery at work during splicing. This hypothesis is based on a principle established by Motoo Kimura, which has become central to population genetics, explaining that the evolutionary trajectory of a mutation with a given effect is intimately linked to the effective population size (Ne) where this mutation emerges. Thus, the probability of fixation of a weakly deleterious mutation increases when Ne decreases, and the probability of fixation of a weakly advantageous mutation increases when Ne increases. The genomes of populations with low Ne are therefore expected to accumulate more weakly deleterious mutations and fewer weakly advantageous mutations than populations with high Ne. In this framework, if splicing errors have only small effects on the fitness of individuals, then natural selection cannot increase the precision of the splicing machinery, allowing tolerance for the production of alternative isoforms.

In the past, the debate opposed one-off observations of effectively functional isoforms on the one hand, to global genomic quantities describing patterns without the possibility of interpreting them in detail. The authors here propose an elegant quantitative approach in line with the expected continuous variation in the effectiveness of selection, both between species and within genomes. The result describing the inter-specific pattern on a large scale confirms what was already known (there is a negative relationship between effective size and average alternative splicing rate). The essential novelty of this study lies in 1) the quantification, for each intron studied, of the relative abundance of each isoform, and 2) the analysis of a relationship between this abundance and the evolutionary constraints acting on these isoforms.

What is striking is the light shed on the general very low abundance of alternative isoforms. Depending on the species, 60% to 96% of cases of alternatively spliced introns lead to an isoform whose abundance is less than 5% of the total variants for a given intron.

In addition to the fact that 60 %-96% of the total isoforms are more than 20 times less abundant than their majority form, this large proportion of alternative isoforms exhibit coding-phase shift at rates similar to what would be expected by chance, i.e. for a third of them, which reinforces the idea that there is no particular constraint on these isoforms.

The remaining 4%-40% of isoforms see their coding-phase shift rate decrease as their relative abundance increases. This result represents a major step forward in our understanding of alternative splicing and makes it possible to establish a quantitative model directly linking the relative abundance of an isoform with a putative functional role concerning only those isoforms produced in abundance. Only the (rare) isoforms which are abundantly produced are thought to be involved in a biological function.

Within the same genome, the authors show that only highly expressed genes, i.e. those that tend to be more constrained on average, are also the genes with the lowest alternative splicing rates on average.

The comparison between species in this study reveals that the smaller the effective size of a species, the more its genome produces isoforms that are low in abundance and low in constraint. Conversely, species with a large effective size relatively reduce rare isoforms, and increase stress on abundant isoforms. To sum up:

• the higher the effective size of a species, the fewer introns are spliced.

• highly expressed genes are spliced less.

• when splicing occurs, it is mainly to produce low-abundance isoforms.

• low-abundance isoforms are also less constrained.

Taken together, these results reinforce a quantitative view of the evolution of alternative splicing as being mainly the product of imprecision in the splicing machinery, generating a great deal of molecular noise. Then, out of all this noise, a few functional gold nuggets can sometimes emerge. From the point of view of the reviewer, the evolutionary dynamics of genomes are depressing. The small effective population sizes are responsible for the accumulation of multiple slightly deleterious introns. Admittedly, metazoan genomes try to get rid of these introns during RNA maturation, but this mechanism is itself rendered imprecise by population sizes.

Strengths:

• The authors simultaneously study the effects of effective population size, isoform abundance, and gene expression levels on the evolutionary constraints acting on isoforms. Within this framework, they clearly show that an isoform becomes functionally important only under certain rare conditions.

• The authors rule out an effect putatively linked to variations in expression between different organs which could have biased comparisons between different species.

Weaknesses:

• While the longevity of organisms as a measure of effective size seems to work overall, it may not be relevant for discriminating within a clade. For example, within Hymenoptera, we might expect them to have the same overall longevity, but that effective size would be influenced more by the degree of sociality: solitary bees/ants/wasps versus eusocial. I am therefore certain that the relationship shown in Figure 4D is currently not significant because the measure of effective size is not relevant for Hymenoptera. The article would have been even more convincing by contrasting the rates of alternative splicing between solitary versus social hymenopterans.

As suggested by the reviewer, we investigated the degree of sociality for the 18 hymenopterans included in our study. We observed that the average dN/dS of the 12 eusocial species (4 bees, 6 ants, 2 wasps) is significantly higher than that of the 6 solitary species (p=2.1x10-3; Fig. R1A), consistent with a lower effective population size in eusocial species compared to solitary ones.

However, the AS rate does not differ significantly between these two groups, neither for the full set of major-isoform introns (Fig. R1B), nor for the subsets of low-AS or high-AS major-isoform introns (Fig. R1C,D). Given the limited sample size (12 eusocial species, 6 solitary species), it is possible that some uncontrolled variables affecting the AS rate hide the impact of Ne.

Author response image 1.

Comparison of solitary (N=6) and eusocial hymenopterans (N=12). A: dN/dS ratio. B: AS rate (all major-isoform introns). C: AS rate (low-AS major-isoform introns). D: AS rate (high-AS major-isoform introns). The means of the two group were compared with a Wilcoxon test.

<ahref="https://imgur.com/NiBIJde">

• When functionalist biologists emphasise the role of the complexity of living things, I'm not sure they're thinking of the comparison between "drosophila" and "homo sapiens", but rather of a broader evolutionary scale. Which gives the impression of an exaggeration of the debate in the introduction.

We disagree with the referee: in fact, all the debate regarding the paradox of the absence of relationship between the number of genes and organismal complexity arose from the comparative analysis of gene repertoires across metazoans. This debate started in the early 2000’s, when the sequencing of the human genome revealed that it contains only ~20,000 protein-coding genes (far less than the ~100,000 genes that were expected at that time). This came as a big surprise because it showed that the gene repertoire of mammals is not larger than that of invertebrates such as Caenorhabditis elegans (19,000 genes) or Drosophila melanogaster (14,000 genes) . We cite below several articles that illustrate how this paradox has been perceived by the scientific community:

Graveley BR 2001 Alternative splicing: increasing diversity in the proteomic world. Trends in Genetics 17 : 100–107. https://doi.org/10.1016/S0168-9525(00)02176-4

“ How can the genome of Drosophila melanogaster contain fewer genes than the undoubtedly simpler organism Caenorhabditis elegans? ”

Ewing B and Green P 2000 Analysis of expressed sequence tags indicates 35,000 human genes. Nature Genetics 25 : 232–234. https://doi.org/10.1038/76115

“ the invertebrates Caenorhabditis elegans and Drosophila melanogaster having 19,000 and 13,600 genes, respectively. Here we estimate the number of human genes […] approximately 35,000 genes, substantially lower than most previous estimates. Evolution of the increased physiological complexity of vertebrates may therefore have depended more on the combinatorial diversification of regulatory networks or alternative splicing than on a substantial increase in gene number. ”

Kim E, Magen A and Ast G 2007 Different levels of alternative splicing among eukaryotes. Nucleic Acids Research 35 : 125–131. https://doi.org/10.1093/nar/gkl924

“we reveal that the percentage of genes and exons undergoing alternative splicing is higher in vertebrates compared with invertebrates. […] The difference in the level of alternative splicing suggests that alternative splicing may contribute greatly to the mammal higher level of phenotypic complexity,”

Nilsen TW and Graveley BR 2010 Expansion of the eukaryotic proteome by alternative splicing. Nature 463 : 457–463. https://doi.org/10.1038/nature08909

“ It is noteworthy that Caenorhabditis elegans, D. melanogaster and mammals have about 20,000 (ref. 68), 14,000 (ref. 69) and 20,000 (ref. 70) genes, respectively, but mammals are clearly much more complex than nematodes or flies.”

Reviewer #2 (Public Review):

Summary:

Two hypotheses could explain the observation that genes of more complex organisms tend to undergo more alternative splicing. On one hand, alternative splicing could be adaptive since it provides the functional diversity required for complexity. On the other hand, increased rates of alternative splicing could result through nonadaptive processes since more complex organisms tend to have smaller effective population sizes and are thus more prone to deleterious mutations resulting in more spurious splicing events (drift-barrier hypothesis). To evaluate the latter, Bénitière et al. analyzed transcriptome sequencing data across 53 metazoan species. They show that proxies for effective population size and alternative splicing rates are negatively correlated. Furthermore, the authors find that rare, nonfunctional (and likely erroneous) isoforms occur more frequently in more complex species. Additionally, they show evidence that the strength of selection on splice sites increases with increasing effective population size and that the abundance of rare splice variants decreases with increased gene expression. All of these findings are consistent with the drift-barrier hypothesis.

This study conducts a comprehensive set of separate analyses that all converge on the same overall result and the manuscript is well organized. Furthermore, this study is useful in that it provides a modified null hypothesis that can be used for future tests of adaptive explanations for variation in alternative splicing.

Strengths:

The major strength of this study lies in its complementary approach combining comparative and population genomics. Comparing evolutionary trends across phylogenetic diversity is a powerful way to test hypotheses about the origins of genome complexity. This approach alone reveals several convincing lines of evidence in support of the drift-barrier hypothesis. However, the authors also provide evidence from a population genetics perspective (using resequencing data for humans and fruit flies), making results even more convincing.

The authors are forward about the study's limitations and explain them in detail. They elaborate on possible confounding factors as well as the issues with data quality (e.g. proxies for Ne, inadequacies of short reads, heterogeneity in RNA-sequencing data).

Weaknesses:

The authors primarily consider insects and mammals in their study. This only represents a small fraction of metazoan diversity. Sampling from a greater diversity of metazoan lineages would make these results and their relevance to broader metazoans substantially more convincing. Although the authors are careful about their tone, it is challenging to reconcile these results with trends across greater metazoans when the underlying dataset exhibits ascertainment bias and represents samples from only a few phylogenetic groups. Relatedly, some trends (such as Figure 1B-C) seem to be driven primarily by non-insect species, raising the question of whether some results may be primarily explained by specific phylogenetic groups ( although the authors do correct for phylogeny in their statistics). How might results look if insects and mammals (or vertebrates) are considered independently?

Following the referee’s suggestion, we investigated the relationship between AS rate and proxies of Ne, separately for insects and vertebrates (Supplementary Fig. 11) . We observed that the relationship was consistent in vertebrates and insects: linear regressions show a positive correlation, significant (p<0.05) in all cases, except for body length in vertebrates. We added a sentence (line 166) to mention this point.

Note that for these analyses we have smaller sample sizes, so we have a weaker power to detect signal. We therefore prefer to present the combined analyses, using PGLS to account for phylogenetic inertia.

Throughout the manuscript, the authors refer to infrequently spliced ( mode <5%) introns as "minor introns" and frequently spliced (mode >95%) as "major introns". This is extremely confusing since "minor introns" typically represent introns spliced by the U12 spliceosome, whereas "major introns" are those spliced by the U2 spliceosome.

To avoid any confusion, we modified the terminology: we now refer to infrequently spliced introns as " minor-isoform introns" and frequently spliced as "major -isoform introns" (see line 135-137) . The entire manuscript (including the figures) has been modified accordingly.

Furthermore, it remains unclear whether the study only considers major introns or both major and minor introns. Minor introns typically have AT-AC splice sites whereas major introns usually have GT/GC-AG splice sites, although in rare cases the U2 can recognize AT-AC (see Wu and Krainer 1997 for example).

We modified the text (line 148-150) to clearly state that we studied all introns, both U2-type and U12-type.

The authors also note that some introns show noncanonical AT-AC splice sites while these are actually canonical splice sites for minor introns.

This is corrected (line 148).

Recommendations for the authors:

Reviewer #2 (Recommendations For The Authors):

Figures 1, 3, and 4: I suggest that authors add regression lines.

We added the regression lines with the “pgls” function from the R package “caper” (in Fig. 1, 3 and 4, and also in all other figures where we present correlations).

Figure 2: As previously mentioned, the terms "minor introns" and "major introns" are extremely confusing. I strongly suggest the authors use different naming conventions.

We changed the terminology:

minor introns -> minor-isoform introns

major introns -> major-isoform introns

Figure 5: Intron-exon boundaries and splice site annotations are shown at the bottom of B, C, and D but not A. I suggest removing the annotation beneath B for consistency and since A+C and B+D are aligned on the x-axis.

Corrected, it was a mistake.

Figure 7: The yellow dotted line is very challenging to see in A.

Corrected, the line has been widened.

Author Response

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

Reviewer #1 (Public Review):

(1.1) This work introduces a new method of imaging the reaction forces generated by small crawling organisms and applies this method to understanding locomotion of Drosophila larva, an important model organism. The force and displacement data generated by this method are a qualitative improvement on what was previously available for studying the larva, improving simultaneously the spatial, temporal, and force resolution, in many cases by an order of magnitude. The resulting images and movies are quite impressive.

We thank the reviewer for their recognition of the achievements our work presents and for their feedback with regard to what they consider our most important findings and the points raised in their review. We will address these points individually below.

(1.2) As it shows the novel application of recent technological innovations, the work would benefit from more detail in the explanation of the new technologies, of the rationales underlying the choice of technology and certain idiosyncratic experimental details, and of the limitations of the various techniques. In the methods, the authors need to be sure to provide sufficient detail that the work can be understood and replicated. The description of the results and the theory of motion developed here focus only on forces generated when the larva pushes against the substrate and ignores the equally strong adhesive forces pulling the larva onto the substrate.

As the reviewer correctly points out, our present work adapts a recently developed set of methods (namely, ERISM and WARP) for use with small soft-bodied animals. The foundational methods have been described in detail in previous publications (refs, 23 and 26). However, upon reflection, we agree that more information can be provided to ensure our work is more accessible and reproducible. We also agree that some additional clarifying information on our approach could be helpful. We have addressed this in the following ways:

(1) We have included a detailed Key Resources table in the methods section to allow for maximum transparency on equipment and reagent sourcing. This can now be found on Pages 16-19.

(2) We have modified the ‘Freely behaving animals force imaging’ section of the Materials and Methods section to include more detailed information on practical aspects of conducting experiments. These changes can be found on page 23-24 (lines 566–567, 571-577).

(3) We have re-ordered the Materials and Methods section, such that microcavity fabrication and microcavity characterisation occur prior to the description of ERISM and WARP experiments - this change should hopefully aid replication. Details regarding the application of a silicone well to the surface of microcavities have also been added (lines 472-474).

(4) We have added additional text in the Introduction and Results (Pages 3-4 and 7, lines 56-86, and 152-153) to explain our rationale for using ERISM/WARP and additional text in the discussion that discusses the potential role(s) of adhesive forces in larval locomotion (Page 12, lines 301307).

(1.3) The substrate applies upward, downward, and horizontal forces on the larva, but only upward and downward forces are measured, and only upward forces are considered in the discussions of "Ground Reactive Forces." An apparent weakness of the WARP technique for the study of locomotion is that it only measures forces perpendicular to the substrate surface ("vertical forces" in Meek et al.), while locomotion requires the generation of forces parallel to the substrate ("horizontal forces"). It should be clarified that only vertical forces are studied and that no direct information is provided about the forces that actually move the larva forward (or about the forces which impede this motion and are also generated by the substrate). Along with this clarification, it would be helpful to include a discussion of other techniques, especially micropillar arrays and traction force microscopy, that directly measure horizontal forces and of why these techniques are inappropriate for the motions studied here.

We attempted to provide a streamlined Introduction in our initial submission and then compared ERISM/WARP to other methods in our discussion. We are happy to provide a brief overview of substrate force measurement methods in the introduction to help set the stage for readers. The Introduction section of our revised manuscript now contains the following comparison of different mechanobiological imaging techniques on pages 3-4 lines 56-86:

‘However, in the field of cellular mechanobiology, many new force measuring techniques have been developed which allow measurement of comparatively small forces from soft structures exhibiting low inertia (15–17) often with relatively high spatial-resolution. Early methods such as atomic force microscopy required the use of laser-entrained silicon probes to make contact with a cell of interest (15). This approach is problematic for studying animal behaviour due to the risk of the laser and probe influencing behaviour. Subsequently, techniques have been developed which allow indirect measurement of substrate interactions. One such approach is Traction Force Microscopy (TFM) in which the displacement of fluorescent markers suspended in a material with known mechanical properties relative to a zero-force reference allows for indirect measurement of horizontally aligned traction forces (17–19). This technique allows for probe-free measurement of forces, but the need to obtain a precise zero-force reference would make time-lapse measurements on behaving animals challenging; further, depending on the version used, it has insufficient temporal resolution for the measurement of forces produced by many behaving animals, despite recent improvements (20). A second approach revolves around the use of micropillar arrays; in this technique, horizontally-aligned traction forces are measured by observing the deflection of pillars made of an elastic material with known mechanical properties. This approach can be limited in spatial resolution and introduces a non-physiological substrate that may influence animal behavior (21,22).

Recently we have introduced a technique named Elastic Resonator Interference Stress Microscopy (ERISM) which allows for the optical mapping of vertically aligned GRFs in the pico and nanonewton ranges with micrometre spatial resolution by monitoring local changes in optical resonances of soft and deformable microcavities. This technique allows reference-free mapping of substrate deformations and calculation of vertically directed GRFs; it has been used to study a range of questions related to exertion of cellular forces (23–25). Until recently, this technique was limited by its low temporal resolution (~10s), making it unsuitable for recording substrate interaction during fast animal movements, but a further development of ERISM known as wavelength alternating resonance pressure microscopy (WARP), has been demonstrated to achieve down to 10 ms temporal resolution (26). Given ERISM/WARP allows for probe-free measurement of vertical ground reaction forces with high spatial and temporal resolution, it becomes an attractive method for animal-scale mechanobiology.’

(1.4) The larvae studied are about 1 mm long and 0.1 mm in cross-section. Their volumes are therefore on order 0.01 microliter, their masses about 0.01 mg, and their weights in the range of 0.1 micronewton. This contrasts with the force reported for a single protpodium of 1 - 7 micronewtons. This is not to say that the force measurements are incorrect. Larvae crawl easily on an inverted surface, showing gravitational forces are smaller than other forces binding the larva to the substrate. The forces measured in this work are also of the same magnitude as the horizontal forces reported by Khare et al. (ref 32) using micropillar arrays.

I suspect that the forces adhering the larva to the substrate are due to the surface tension of a water layer. This would be consistent with the ring of upward stress around the perimeter of the larva visible in S4D, E and in video SV3. The authors remark that upward deflection of the substrate may be due to the Poisson's ratio of the elastomer, but the calibration figure S5 shows that these upward deflections and forces are much smaller than the applied downward force. In any case, there must be a downward force on the larva to balance the measured upward forces and this force must be due to interaction with the substrate. It should be verified that the sum of downward minus upward forces on the gel equals the larva's weight (given the weight is neglible compared to the forces involved, this implies that the upward and downward forces should sum to 0).

We have carefully calculated the forces exerted by protopodia and are confident in the accuracy of our measurements as reported. We further agree with the reviewer’s suggestion that gravitational forces can be largely neglected.

As the reviewer points out, one would expect forces due to upward and downward deflections to cancel when considering the entire system. However, we see indications that the counteracting / balancing force often acts over a much larger area than the acting force, e.g. a sharp indentation by a protopodium might be counteracted by an upward deflection over a 10-20 fold larger radius and hence 100 to 400-fold larger area, thereby reducing the absolute value of the upward deflection at any given pixel surrounding the indentation. This in turn increases error in determining the integrated upward deformation, making it difficult to perform an absolute comparison of acting and counteracting force. Further, recording the entire counteracting force induced deformation would require acquiring data with a prohibitively large field of view.

We agree that in some situations, water surface tension may be adhering animals to the substrate. Importantly, this is a challenge that the animal faces outside the lab in its natural environment of moist rotting fruit and yeast. The intricate force patterns seen in our study in the presence of water surface tension are therefore ecologically relevant. In other situations (e.g. preparing for pupation), larvae are able to stick to dry surfaces, suggesting that other adhesive forces such as mucoid adhesion can also come into play in certain behavioural contexts. A full characterization of the effects of water tension and mucoid adhesion are beyond the scope of this study. However, we have now added a sentence on pages 8 and 12 commenting on these other biomechanical forces at play:

‘We also observed that the animals travel surrounded by a relatively large water droplet (lines 189-190).’

‘We observed that larvae travel surrounded by moisture from a water droplet, which produces a relatively large upwardly directed force in a ring around the animal. The surface tension produced by such a water droplet likely serves a role in adhering the animal to the substrate. However, during forward waves, we found that protopodia detached completely during SwP, suggesting this surface tensionrelated adhesion force can be easily overcome by the behaving animal. (lines 301-307) .’

(1.5) Much of the discussion and the model imply that the sites where the larva exerts downward force on the gel are the sites where horizontal propulsion is generated. This assumption should be justified. Can the authors rule out that the larva 'pulls' itself forward using surface tension instead of 'pushing' itself forward using protopodia?

Determining the exact ‘sites’ where horizontal propulsion is generated is challenging. In our conceptual model, movement is not initiated by protopodia per se, but rather by a constellation of muscle contractions, which act upon the hydrostatic skeleton, which in turn causes visceral pistoning that heaves larvae forward. This is based on previous findings in Ref 31. While there are indeed downward protopodial ‘vaulting’ forces prior to initiation of swing, we propose that the main function of protopodia is not to push the larvae forward, but rather to provide anchoring to counteract opposing forces generated by muscles. We agree that water surface tension could also be sculpting biomechanical interactions; however, a full characterization of how water surface tension shapes larval locomotion is beyond the scope of this study.

Since we have observed larvae move over dry terrain (e.g. glass) without an encasing water bubble, we do not believe that an encasing water bubble is strictly required for locomotion. We have also seen no obvious locomotion related modulations in the pulling forces created by water bubbles encasing larva, which would be expected if animals were somehow using water tension to pull themselves forward. Overall, the most likely explanation is that larvae use a mixture of biomechanical tactics to suit the moment in a given environment. This represents a challenge but also an opportunity for future research.

We have now added additional text in the ‘Functional subdivisions within protopodia’ subsection to discuss these nuances (page 14, lines 382-387):

‘This increased force transmitted into the substrate is unexpected as the forces generated for the initiation of movement should arise from the contraction of the somatic muscles. We propose that the contraction of the musculature responsible for sequestration acts to move haemolymph into the protopodia thus exerting an increased pressure onto the substrate while the contact area decreases as a consequence of the initiation of sequestration.’

and (page 15, lines 398-399):

‘Water surface films appear to facilitate larval locomotion in general but the biomechanical mechanisms by which they do this remain unclear.’

(1.6) More detail should be provided about the methods, their limitations, and the rationale behind certain experimental choices.

We thank the reviewer for this comment. As this significantly overlaps with a point raised earlier, we kindly direct them to our answer to comment #1.2 above.

(1.7) Three techniques are introduced here to study how a crawling larva interacts with the substrate: standard brightfield microscopy of a larva crawling in an agarose capillary, ERISM imaging of an immobilized larva, and WARP imaging of a crawling larva. The authors should make clear why each technique was chosen for a particular study - e.g. could the measurements using brightfield microscopy also be accomplished using WARP? They should also clarify how these techniques relate to and possibly improve on existing techniques for measuring forces organisms exert on a substrate, particularly micropillar arrays and Traction Force Microscopy.

Indeed, each of the three methods used has a specific merit. The brightfield microscopy was selected to track features on the animal’s body and to provide a basic control for the later measurements. However, this technique cannot directly measure the substrate interaction, it only allows inferences to be made from tracked features at the substrate interface. ERISM provides high resolution maps of the indentation induced by the larva; it is also extensively validated for mapping cell forces and the data analysis is robust against defects on the substrate (refs 23, 24 and 25). However, as we explain in the manuscript, ERISM lacks the temporal resolution needed to monitor mechanical activity of behaving larva. Its use was therefore limited to the study of anaesthetised animals. For mapping forces exerted by behaving larva, we used WARP which is a further development of ERISM that offers higher frame rates but at the cost of requiring more extensive calibration (Supplementary Figure S4). The streamlined introduction of the different methods in our original manuscript originates from our attempt to be as concise as possible. However, as state in response to comment #1.2, we agree that additional explanation and discussion will be helpful for readers and that it will helpful to briefly refer to other methods for force mapping. We have now added references to a variety of techniques in the Introduction (Page 3-4, lines 56-86) as stated in a prior response.

(1.8) As written, "(ERISM) (19) and a variant, Wavelength Alternating Resonance Pressure microscopy (WARP) (20) enable optical mapping of GRFs in the nanonewton range with micrometre and millisecond precision..." (lines 53-55) may generate confusion. ERISM as described in this work has a much lower temporal resolution (requires the animal to be still for 5 seconds - lines 474-5); In this work, WARP does not appear to have nanonewton precision (judging by noise on calibration figures) and it is not clear that it has millisecond precision (the camera used and its frame rate should be specified in the methods).

Previous studies have demonstrated the capabilities and limitations of ERISM and WARP. Upon reflection, we agree that our wording here could be more precise. To clarify our claim, we now separate the statements on ERISM and WARP in the introduction as follows (page 4, lines 78-83):

“Until recently, this technique was limited by its low temporal resolution (~10s) making it unsuitable for use in recording substrate interaction during fast animal movements, but a further development of ERISM known as wavelength alternating resonance pressure microscopy (WARP), has been demonstrated to achieve down to 10 ms temporal resolution (26)”

While WARP can achieve comparable force resolution as ERISM when used in a cellular context (c.f. Ref 26), we agree that for the present study, the resolution was in the 10s of nanonewton range, due to the need to use stiffer substrates and larger fields of view.

The camera used in our work was specified in the appropriate subsection of the Materials and Methods (“All WARP and ERISM images were acquired using an Andor Zyla 4.2 sCMOS camera (Andor Technology, Belfast, UK)”). We apologise that the exact frame rate used in our current work was not mentioned in our original manuscript; this has now been added to the ‘Freely behaving animals force imaging’ section of the Materials and Methods (page 23, lines 574-577).

(1.9) It would be helpful to have a discussion of the limits of the techniques presented and tradeoffs that might be involved in overcoming them. For instance, what is the field of view of the WARP microscope, and could it be increased by choosing a lower power objective? What would be required to allow WARP microscopy to measure horizontal forces? Can a crawling larva be imaged over many strides by recentering it in the field of view, or are there only particular regions of the elastomer where a measurement may be made?

We agree with the reviewer that some discussion of the limitations of our technique will allow readers to have a more informed appreciation of what we are capable of measuring using WARP. However, as this is the first work to ever demonstrate such measurements, the limitations and tradeoffs cannot all be known with certainty at the present stage.

To answer your individual questions:

(1) There is a trade-off between numerical aperture and the ability to resolve individual interference fringes. Since our approach to calculate displacement from reflection maps relies upon counting of individual fringe transitions, going to a lower powered objective risks having these fringes blend and thus the identification of the individual transitions becoming impossible. The minimum numerical aperture of the objective will therefore generally depend on the steepness of indentations produced by the animals; the steeper an indentation, the closer the neighbouring fringes and thus the higher the required magnification to resolve them.

(2) From WARP and ERISM data, one can make inferences about horizontal forces, as is described in detail in our earlier publications about ERISM (ref, 23). However, quantitation of horizontal forces at sufficient temporal resolution to allow the investigation of behaving Drosophila larva is currently not possible.

(3) Many strides can indeed be imaged using our technique, however, this comes with additional technical challenges. Whether or not the animal itself can be recentred is an ongoing challenge. We have found that the animals are amenable to recentring themselves within the field of view if chasing an attractive odorant. However, manual recentering using a paintbrush risks destroying the top surface of the soft elastic resonator and recentering the microscope stage would require real-time object tracking which has been outside the scope of this original work, given the other challenging requirements on hardware and optics for obtaining high quality force maps.

To provide more information on limitations of our technique, we have added the following text into the discussion (pages 13-14, lines 356-370).

‘Despite the substantial advances they have provided, the use of WARP and ERISM also brings challenges and has several technical limitations. For example, fabrication of resonators is much more challenging than preparation of the agarose substrates conventionally used for studying locomotion of Drosophila. This problem is compounded by the fragility of the devices owing to the fragility of the thin gold top mirror. This becomes problematic when placing animals onto the microcavities, as often the area local to the initial placement of the animal is damaged by the paintbrush used to move the animals. Further, as a result of the combining of the two wavelengths, the effective framerate of the resultant displacement and stress maps is equal to half of the recorded framerate of the interference maps. To be able to monitor fast movements, recording at very high framerates is therefore necessary which, depending on hardware, might require imaging at reduced image size, but this in turn reduces the number of peristaltic waves that can be recorded before the animal escapes the field of view. A further limitation is that WARP and ERISM are sensitive mainly to forces in the vertical direction; this is complementary to TFM, which is sensitive to forces in horizontal directions. Using WARP in conjunction with high speed TFM (possibly using the tuneable elastomers presented here) could provide a fully integrated picture of underlying vertical and horizontal traction forces during larval locomotion.’ And further on page 13, lines 337-341:

‘More detailed characterisation of this behaviour remains a challenge owing to the changing position of the mouth hooks. Due to their rigid structure and the relatively large forces produced in planting, mouth hooks produce substrate interaction patterns which our technique struggles to map accurately due to overlapping interference fringes ambiguating the fringe transitions.’

We trust that the above discussion and our modifications to our manuscript resulting from these will address the reviewer’s concerns.

Reviewer #2 (Public Review):

(2.1) With a much higher spatiotemporal resolution of ground dynamics than any previous study, the authors uncover new "rules" of locomotory motor sequences during peristalsis and turning behaviors. These new motor sequences will interest the broad neuroscience community that is interested in the mechanisms of locomotion in this highly tractable model. The authors uncover new and intricate patterns of denticle movements and planting that seem to solve the problem of net motion under conditions of force-balance. Simply put, the denticulated "feet" or tail of the Drosophila larva are able to form transient and dynamic anchors that allow other movements to occur.

We thank the reviewer for their feedback and the information regarding which of our results is likely to resonate most impactfully with readers from a biological background.

The biology and dynamics are well-described. The physics is elementary and becomes distracting when occasionally overblown. For example, one doesn't need to invoke Newton's third law, per se, to understand why anchors are needed so that peristalsis can generate forward displacements. This is intuitively obvious.

We are sorry to hear that the reviewer found some of the physics details distracting. To address this concern, we have simplified some of the language while still attempting to keep the core arguments intact. For context and analogy, we still believe that including a brief reference to the laws of motion is helpful for some readers to explain some of our results and highlight their general implications, especially with regard to anchoring against reaction forces.

One of our objectives is to make this article accessible and interesting for biologists and physicists at all levels. We feel it is important to reach out to both communities and try to be inclusive as possible in our writing. Newton’s 3rd law is clearly relevant for our study and it is a common point of reference for anyone with a highschool education, and so we feel it is appropriate to mention it as a way to help readers across disciplines understand the biophysical challenges faced by the animals we study.

(2.2) Another distracting allusion to "physics" is correlating deformation areas with displaced volume, finding that "volume is a consequence of mass in a 2nd order polynomial relationship". I have no idea what this "physics" means or what relevance this relationship has to the biology of locomotion.

Upon reflection, we agree that this language may be overly complex and distracts from what is, at its core, a simple, but important principle governing how Drosophila larvae interact with their substrates. The point we are trying to make is that our data show that forces exerted by an animal are proportional in a non-linear way to contact area. This suggests that to increase force exerted on the substrate, an animal must increase contact area. We do not observe contact area remaining constant while force increases, or vice versa. To make this result more clear, we have made several changes in our revised manuscript. Figure 5B no longer shows the relationship between the protopodial contact area and the displaced volume of the elastic resonator, but instead now shows the protopodial contact area and recorded force transmitted into the substrate. This then shows that in order to increase force transmitted into the substrate, these animals must increase their contact area. We have made changes to the figure legend of Figure 5 and the statements in the Results section accordingly (Page 9, lines 220-222).

2.3 The ERISM and WARP methods are state-of-the-art, but aside from generally estimating force magnitudes, the detailed force maps are not used. The most important new information is the highly accurate and detailed maps of displacement itself, not their estimates of applied force using finite element calculations. In fact, comparing displacements to stress maps, they are pretty similar (e.g., Fig 4), suggesting that all experiments are performed in a largely linear regime. It should also be noted that the stress maps are assumed to be normal stresses (perpendicular to the plane), not the horizontal stresses that are the ones that actually balance forces in the plane of animal locomotion.

We largely agree with the statement made by the reviewer here. However, we have found that in many contexts, audiences appreciate having the absolute number of the forces and stresses involved reported. Therefore, where possible, we have used stress maps, rather than displacement maps. We also observe that while stress and displacement maps show similar patterns, features sometimes appear sharper in the stress map, which is a result of the finite element algorithm being able to attribute a broad indentation to a somewhat more localised downward force. We have thus opted to keep to original stress maps. We have been more explicit about WARP and ERISM being more tuned to recording vertically directed forces throughout the revised manuscript (lines 75, 78, 86, 162, 301, 305, 336).

We have also modified our Discussion section to encourage further investigation of our proposed model using a technique more tuned to horizontal stresses (pages 12-13, lines 324-328):

‘However, WARP microscopy is best suited to measurements of forces in the vertical direction, and though we can make inferences such as this as they are a consequence of fundamental laws of physics, we present this conclusion as a testable prediction which could be confirmed using a force measurement technique more tuned to horizontally directed forces relative to the substrate.’

(2.4) But none of this matters. The real achievements are the new locomotory dynamics uncovered with these amazing displacement measurements. I'm only asking the authors to be precise and down-to-earth about the nature of their measurements.

We thank the reviewer for their perceptiveness in finding that though the forces are interesting, the interactions themselves are the most noteworthy result here. We trust that with the changes made in our revised manuscript, the description is now more “down-to-earth”, more concise where appropriate, and accurate as to which results are particularly important and novel.

(2.5) It would be good to highlight the strength of the paper -- the discovery of new locomotion dynamics with high-resolution microscopy -- by describing it in simple qualitative language. One key discovery is the broad but shallow anchoring of the posterior body when the anterior body undertakes a "head sweep". Another discovery is the tripod indentation at the tail at the beginning of peristalsis cycles.

We thank the reviewer for this recommendation. We agree that including a more explicit statement of some of our findings, especially with regards to these new posterior tripod structures and the whole-abdomen preparatory anchoring prior to head sweeps, would make the paper more impactful. As a result, we have modified the discussion section to include a statement for each new result and have also amended our abstract as a result (lines 407-416):

“Here we have provided new insights into the behaviour of Drosophila larval locomotion. We have provided new quantitative details regarding the GRFs produced by locomoting larvae with high spatiotemporal resolution. This mapping allowed the first detailed observations of how these animals mitigate friction at the substrate interface and thus provide new rules by which locomotion is achieved. Further, we have ascribed new locomotor function to appendages not previously implicated in locomotion in the form of tripod papillae, providing a new working hypothesis of how these animals initiate movement. These new principles underlying the locomotion outlined here may serve as useful biomechanical constraints as called for by the wider modelling community (39).”

(2.6) As far as I know, these anchoring behaviors are new. It is intuitively obvious that anchoring has to occur, but this paper describes the detailed dynamics of anchoring for the first time. Anchoring behavior now has to be included in the motor sequence for Drosophila larva locomotion in any comprehensive biomechanical or neural model.

We agree with the reviewer on this. We think it is best to let our colleagues reflect on our findings and then decide how best to include them in future models.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Please be sure to describe in a figure caption or in the methods the details of the optical setup, especially the focal lengths of all the lenses, including the objective, and part numbers of the LEDs and filters. It would be helpful to have a figure in the main paper explaining the principles of ERISM/WARP microscopy along with the calibration measurements and computational pipeline (this would mainly combine elements already in the supplement). Such a figure should also include details of the setup that are alluded to in the methods but not fully explained (for instance, a "silicone well" is referred to in the methods but never described). The calibration of elastomer stiffness that now appears in the main text could be made a supplementary figure, unless there is some new art in the fabrication of the elastomers that should be highlighted as an advance in the main text.

We appreciate the importance of explaining our methods to readers.

In response to the public comments, we have added further details in our methods section to clarify practical aspects and ensure that readers will be able to reproduce our work.

In Supplemental Figure 2, we show the full optical light path for ERISM and WARP along with named components. In addition, the principles of ERISM and WARP microscopy have already been extensively described in previous publications (See Refs 23-26). In light of this, we feel that the best approach in this paper is to direct readers to those publications.

We feel that it is appropriate to present the calibration of elastomer stiffness in the main text because this is indeed a new innovation that is not just about making the elastomers but making force sensors based on these different materials. This is really important because it shows how researchers can tune the stiffness of an ERISM/WARP elastomer to match the type of tissue or organism under study. This is really the key technical advance that enables whole animal biomechanics across a range of animal sizes, so we think it is appropriate to keep it in the main text.

We want to make sure that we do not oversell this point, and we feel that we make it sufficiently clear in the main text of our manuscript that making elastomer based force sensors of appropriate stiffness is important, when we state

“First, we developed optical microcavities with mechanical stiffnesses in the range found in hydrogel substrates commonly used for studying Drosophila larval behaviour, i.e. Young’s modulus (E) of 10-30kPa (36–38).” (p. 5, ll. 124) and later

“Here we used Drosophila larvae as a test case, but our methods now allow elastic optical resonators to be tuned to a wide range of animal sizes and thus create new possibilities for studying principles of neuro-biomechanics across an array of animals.” (p. 12, ll. 337)

I would appreciate a description of the "why" behind some experimental choices, as understanding the motivation would be helpful for other researchers looking to adopt these techniques.

We have now added additional text in the introduction and discussion that explains the rationale behind our experimental choices. in more detail. Please see our response to Reviewer 1’s public comments on the same point.

(1) The WARP and ERISM experiments were conducted on a collagen coated gold surface rather than agarose. Why? EG does agarose not adhere to the gold, or would its thickness interfere with the measurement?

The gold layer is applied above the elastomer and the collagen on top of the gold layer makes the gold a more natural biological surface for the animals. Agarose is unsuitable as an elastomer because it would dry during the vacuum based deposition of the gold. It is also unsuitable as a surface coating on top of the gold as the coating on the gold needs to very thin to preserve the spatial and mechanical resolution of our sensors. Further, processing of agarose generally requires temperatures of 60°C and higher which we find can damage the elastomer / gold films.

(2) The ERISM measurements are made on a cold anesthetized animal right as it starts to wake up (visible mouth-hooks movement), which presents some difficulty. Why not start imaging while the animal is still completely immobile? Or why not use a dead larva?

This approach allowed us to get measurements of forces exerted by denticles that are physiologically and biomechanically accurate. In dead or fully anesthetized animals, one cannot be sure that the forces exerted by denticles and denticle bands are representative of the forces exerted by an animal with active hydrostatic control.

(3) In the ERISM setup the monochromator is spatially filtered by focusing through pinhole, while in the WARP setup, the LEDs are not.

Yes that’s correct. The LED light sources used in WARP have better spatial homogeneity than the tungsten filament used in ERISM and so a pinhole is not required in WARP.

(4) SV4 shows the interference image of a turning larva (presumably from one illumination wavelength) rather than a reconstruction of the displacement or stresses. Why?

We felt that in this particular case the interference images provided a clearer representation of the behavioural sequence, showing both the small indentations generated by individual denticles and the larger indentations of the animal overall.

Lines 49-50 "a lack of methods with sufficient spatiotemporal resolution for measuring GRFs in freely behaving animals has limited progress." This needs a discussion of what sufficient spatial and temporal resolutions would be and how existing methods fall short of these goals.

We have now rewritten the introduction to include an overview of other alternative approaches and of what we see as the requirements here. See our response to the public comments.

Figure caption 1B (line 789) refers to "concave areas of naked cuticle (black line) which generally do not interact with the substrate" While I think this might be supported by later WARP images, it's not clear how the technique of figure 1 measures interaction, which could e.g. be mediated by surface tension of a transparent fluid.

The technique of Figure 1 provides qualitative information which as the reviewer points out is validated by WARP measurements later.

Lines 184-189 "However, unexpectedly, we observed an additional force on the substrate when protopodia leave the substrate (SI) and when they are replanted (ST). To investigate whether this force was due to an active behaviour or due to shifting body mass, we plotted integrated displacement (i.e. displaced volume) against the contact area for each protopodium, combining data from multiple forwards waves (Figure 5B). Area is correlated with displaced volume for most time points, indicating that volume is a consequence of mass in a 2nd order polynomial relationship." I couldn't follow this argument at all.

We have now reworded this section and explained our rationale. Also see our response to a similar critique in Reviewer 2’s public comments.

Generally the authors might reconsider their use of acronyms. e.g. (244-246) "SI latencies were much more strongly correlated with wave duration across most segments than ST latencies. SIs scale with SwP and this could be mediated by proprioceptor activity in the periphery" is made more difficult to parse by the abbreviations.

As we need to refer to these terms multiple times throughout the manuscript, we feel the use of acronyms is appropriate here.

The video captions are inadequate. Please expand on them to explain clearly what is shown, and also describe in the methods how the data were acquired and processed. For instance, it seems that in SV3 a motion correction algorithm is applied so that the larva appears stationary even as it crawls forward. I think "fourier filtered" means that the images were processed with a spatial high pass filter - this should be explained and the parameters noted.

We have revisited the video captions provided in the supplementary information document and conclude that these contain the important information. The mode of acquisition are described in the methods, e.g. Video 1 and 2 see section in Methods on “Denticle band kinematic imaging” and Videos 3 and 4 see section in Methods on WARP. Supplementary Video 3 does not make use of motion correction; indeed, one can see the larvae moving upwards/forwards in the field of view. We apologize for not explaining the Fourier filtering process for Video 3. We have now modified the video caption to read as follows:

Video SV3. WARP imaging during forwards peristalses.

Video showing high frame rate displacement maps produced by a freely behaving Drosophila larva. Displacement maps were Fourier filtered to make denticulated cuticle more readily visible and projected in 3D to show the effects of substrate interaction. Details of the Fourier filtering procedure were described elsewhere [Kronenberg et al, Nat Cell Biol 19, 864–872 (2017)].

What were the reflectances of the bottom (10 nm Au/Cr) and top (15nm Au) metal layers at the wavelengths used? I imagine the bottom layer should be less than 38%, the top layer higher, and the product of the square of the bottom transmission and the top reflectance coefficients equal to the bottom reflectance (to make the two paths of the interferometer contribute equal intensity), but none of this is stated.

The reflectance of the gold mirrors was studied in detail in prior work on ERISM. See Kronenberg et al, Nat Cell Biol 19, 864–872 (2017). We therefore refrained from adding a complete optical characterization of the ERISM sensors again here. In brief, we found that a reflectance >13% at each Au mirror is required for reliable ERISM measurements.

The description of the gold coated elastomer as a microcavity is confusing to me. Does the light really make multiple round trips between the plates before returning to the detector? The loss of light on each round trip would depend on the reflectance and parallelism of the top and bottom mirrors. From the WARP calculation it's appears that there is only one round trip - a pi/2 phase shift results from the calculation for one round trip: 2pi*2nL 5nm/(630nm)^2, with n = 1.4 and L = 8 microns - if there were two round trips, the phase shift would be pi etc. Would this better be described as a mostly common path interferometer?

The physics of our devices is best described within the framework of thin film interference and (weak) microcavity optics. Indeed, light can make multiple roundtrips, though it gets attenuated with each reflection. The complete calculation of the multiple roundtrips is only required to obtain quantitative information on the amount of light that is reflected. The spectral position of minima in reflectance can also be obtained from assuming one roundtrip which is what is done in the description of the WARP calculations.

Figure 2 e,f: the line fits appear to be dominated by the data points at 2 s. If these are removed, do the fits change? To support the argument that 2e shows a correlation and 2f does not, some kind of statistical test, ideally a hierarchical bootstrap, should be conducted to compare between the two measurements.

If we remove the data points at 2 s, then R^2’s for swing initiation latencies change as follows: A2: 0.35 to 0.005; A4: 0.78 to 0.31; A6: 0.61 to 0.01. The data in 2e,f are the averages from 3 waves in each animal and so the data points at 2 s are not simply the result of single ‘rogue’ waves but rather averages of several trials. Further, if all individual waves are plotted, we can see that the overall trends are still visible.

We don’t think it is appropriate to remove the data at 2 s from our analysis, but we take the point regarding statements about presence or absence of correlation in a formal sense. We have therefore changed the wording in the description of 2e,f to refer simply to the fact that wave duration can ‘largely determine' latencies in some instances, but is less able to in other instances, as is suggested by the R^2 (coefficient of determination) data. In discussion, we have also adjusted our wording.

Figure 4 - please provide in the main figure or as a supplement the full images (i.e. not cropped to the assumed shape of the larva)

We do not feel that it is necessary or helpful to provide the full images given that the focus of the analysis is on dynamics of protopodia movements.

Figure 5e top: single data points around wave duration 0.6s appear to dominate fit lines. Does removing these points alter the fits? To support the argument that 5e top shows a correlation and 5e bottom does not, some kind of statistical test, ideally a hierarchical bootstrap, should be conducted to compare between the two measurements.

In Figure 5e, we are showing all waves analysed across animals. If we remove the datapoints at 0.6 s, A2 R^2 changes from 0.24 to 0.05, A4 R^2 changes from 0.48 to 0.11, A6 R^2 changes from 0.69 to 0.34; however we don’t feel it is appropriate to remove these data from our analysis. We take the point about needing to be cautious about making claims about correlation versus no correlation and have now reworded description of these results along same lines as Figure 4.

It appears from the methods (467-489) that animals were kept wet for warp imaging but not for ERISM imaging. Please confirm or explain further the presence or absence of a water layer in these two sets of measurements, as this could affect the adhesion forces.

In each case, the animals were transferred onto experimental substrates with a moistened paintbrush. We have added text explicitly stating this in the methods section.

Kim et al. Nature Methods 2017 (10.1038/nmeth.4429) describes recording two images separated by less than 60 microseconds using a scientific CMOS camera with a frame rate of 200 Hz. This is accomplished by triggering a pulsed LED once at the end of one frame's capture window and then a second time at the beginning of the next frame's window (see Supplementary Figure 10). I'm not sure if this trick is widely known, but it's worth considering if the authors are running into a problem with movement between the two wavelength exposures in their WARP setup.

Thank you for this tip. We will take this under consideration for future work.

Is the setup compatible with optogenetics? (EG is the red light dim enough that it wouldn't activate CsChrimson, or could a longer wavelength led be used for interferometry?) If so, activation of mooncrawler descending neuron (MDN) could be used to study backward crawling (or thermogenetic activation of MDN), e.g. to contrast the sites and order of "anchoring" between the two directions of crawling.

The set-up is potentially compatible with optogenetics. We are in the process of exploring this in current ongoing work.

Reviewer #2 (Recommendations For The Authors):

Simplify/reduce the commentary about force measurements, and highlight the clear, qualitative descriptions of the novel locomotion patterns that they have observed. The microscopy and movements seem to matter more than the ground force estimations.

We have addressed these issues in our responses to Reviewer 2’s public comments.

Author Response

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

We thank the reviewers for their valuable feedback which has improved this work greatly from its original form, and are elated to have such glowing reviews of the revised work published alongside the revised preprint. Reviewer 3 raises some final salient points, which deserve a brief address here.

Teeth: We thank the reviewer for clarifying their points. We do make the assumption that the ecological parameter space of toothed and beaked organisms will be comparable. Both are governed by the same set of physical principles and have the jaw bone as the most likely point of failure (teeth are harder than bone, and keratinous rhamphothecae are malleable and can be regrown with relative ease when deformed). Differences in stress/strain distribution between toothed and beaked organisms will occur but are already accounted for in our methods as we model both the teeth and rhamphotheca and will observe these different effects. We have added an explicit statement of this hypothesis to the Methods section of the manuscript.

Cranial kinesis: In our opinion, it is a safe assumption that the lower jaws of extant birds and enantiornithines are comparable. We do not see why the acquisition of kinesis in the upper jaw would generally affect the functional role of or constraints on the lower jaw. One possibility we discussed is that a quickly-moving kinetic premaxilla could let the lower jaw move a shorter distance during effective prey capture and lower the selection for speed (i.e. allow jaw-closing MA to remain higher). While we have added this possibility to our call for the investigation of cranial kinesis, we consider it too speculative to begin altering interpretations of fossil taxa. All raw measurement data remains available so that, if evidence is found for cranial kinesis having predictable effects on our measured parameters, future researchers can re-analyse our data and update any ecological predictions accordingly.

Organization: To our knowledge eLife format incorporates what one would think of as a Conclusions section into the Discussion. Our Discussion section currently contains 18 subheadings which should guide a reader to any specific topic of interest. The Discussion also progresses from a more narrow to broad focus which we and several colleagues find intuitive.

We thank all three reviewers once again for their feedback that has improved this work and their kind words throughout the process.

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

We thank all three reviewers for their detailed reviews, and generally agree with their feedback. To accompany the reviewed preprint of this manuscript, we wished to respond to comments from the reviewers so that they (and the public) will know what we are planning to incorporate in the revised manuscript we are currently preparing. If there are any comments on our plans in the meantime, please let us know.

• Reviewer 1, on concerns regarding identification of ontogenetic stage and comparison of taxa from different ontogenetic stages: It is fair to say that enantiornithine ontogeny is still poorly understood, though we believe all current evidence points to each specimen used in this study to being adequately mature for comparison to the extant birds used in the study. Stages of skeletal fusion are the standard method of assessing enantiornithine ontogeny (Hu and O'Connor 2017), and our comparison of histological work (Atterholt, Poust et al. 2021) to skeletal stages in Table S4 suggests a transition from juvenile to subadult in stage 0 or 1 and from subadult to adult within stage 3. Thus, the specimens we quantitatively examine in this study, all at stages 2 or 3 (Figure S10), are advanced subadults or adults. It is well-known that many living animals considered “adults” would be considered subadults or even juveniles to a palaeontologist (Hone, Farke et al. 2016). So, even if some individuals in this study are not fully skeletally mature, they should have obtained the morphology which they would possess for most of their lives and thus the morphology which undergoes selective pressure. We will add this context to the “Bohaiornithid Ontogeny” section and thank the reviewer for seeking more detail for this point.

• Reviewer 2, on need of a context figure: We have an artistic life reconstruction of a bohaiornithid in preparation, and can include that in the revised manuscript as a figure.

• Reviewer 2, on raptor claw categories: We explain these categories in-depth in a previous work (Miller, Pittman et al. 2023). However, we will now add a short summary of that explanation to this work so that this manuscript will become self-contained in this regard. In short, the “large raptor” category includes extant birds with records of regularly taking prey which cannot be encircled with the pes, while birds in the “small raptor” have no such records. As Reviewer 2 points out this does often follow phylogenetic lines, but not always. E.g. most owls specialise in taking small prey, but the great horned owl Bubo virginianus regularly takes mammals and birds larger than its pes (Artuso, Houston et al. 2020); and conversely we can only find reports of the common black hawk Buteogallus anthracinus taking prey samll enough for the pes to encircle (Schnell 2020) despite other accipiters frequently taking large prey. In both cases these taxa plot in PCA nearer to other large or small raptors (respectively) than to their phylogenetic relatives.

• Reviewer 3, on teeth vs beaks: We are not aware of any foods which are exclusive to toothed or beaked animals. There are some aspects of extant bird biology that may affect the way a certain diet may need to be adapted to which we do comment on, e.g. discussion of alternatives to the crop and ventriculus for processing plant matter in the Bohaiornithid Ecology and Evolution section. For functional studies, e.g. FEA, we have included the rhamphotheca in toothless models which serves the same role as teeth, to be a feeding surface. It should not matter, in theory, if the feeding surface is hard or soft as mechanical failure occurs in high stress/strain states regardless of the medium. If having teeth necessarily increases or decreses overall stress/strain relative to a beak (and from our work this does not appear to be the case), this would in turn necessarily limit dietary options. So, all models in our work should be directly comparable.

As an additional note on this topic, we address tooth shape in bohaiornithids at the end of the Bohaiornithid Ecology and Evolution section. We specifically note that their tooth shape is likley controlled by phylogeny in the current version, though we will add a note in the upcoming version that the morphospace of bohaiorntihid teeth overlaps that of many other clades with purportedly diverse diets, which is consistent with a hypothesis of diverse diets within the clade.

• Reviewer 3, on cranial kinesis: Our FE models should be unaffected by cranial kinesis, as these are two-dimensional and model the akinetic lower jaw only. Some mediolateral kinesis may be relevant in the mandible in the form of “wishboning” in different taxa, but its prevalence in extant birds is currently unknown. The preservation of enantiornithines (two-dimensionally and typically in lateral view) limits the ability to capture any mediolateral function regardless.

Our models of mechanical advantage do not account for any cranial kinesis. This is a necessary simplifcation. The nature of cranial kinesis in extant birds, and the role that it plays in feeding, is poorly understood. Cranial kinesis will increase gape, but we don’t yet know how/if it affects jaw closing force and speed (moreover, given the variation in quadrate and hinge morphology present in extant birds, this is also something that is likely to be highly diverse). We have therefore modelled the extant birds’ jaw closing systems as having one, akinetic out lever (the jaw joint to the bite point), to match the situation in our fossil taxa. This is a common simplification that has been used previously with success (Corbin, Lowenberger et al. 2015, Olsen 2017). However, we acknowledge that this simplification may introduce some error. Unfortunately, until the mechanics of cranial kinesis – and the variation in the anatomy and performance of kinetic structures in extant birds – are better understood, we cannot determine exactly what that error looks like. We therefore have greater confidence in the inter-species comparability this conservative, akinetic approach (in other words, we may not be making assumptions that are 100% accurate, but we are at least making the same assumption across all taxa, so it should be comparable in its error). We will add a section in the Mechanical Advantage and Functional Indices discussion calling for further research into the mechanics of cranial kinesis so future mechanical advantage work in birds can take this matter into account.

• Reviewer 3, on skull reconstruction: This issue is partly addressed in the Bohaiornithid Skull Reconstruction section, though we agree that adding more mentions of it in the MA and FEA Discussion sections and the Bohaiornithid Ecology and Evolution sections will benefit the manuscript. Most notably Shenqiornis and Sulcavis have similar ecological interpretations, but much of the Shenqiornis skull reconstruction uses Sulcavis bones. Longusunguis is the only other taxon which takes more than two bones from a different taxon, and in this case all but the quadrate are not used in any quanitative measurements. We have ensured that the skull reconstructions presented in Figure 2 show what portions of the skull come from what specimen so that as new material is discovered and phylogenetic relationships are updated it will be clear to future readers which parts of reconstructions will need to be updated.

• Reviewer 3, on data availability: All data including FEA models and raw measurement data are included in the same repository as the scripts, which we will make clear in the manuscript. Good catch on the data link being dead, we will publish it now.

As a final note, it was brought to our attention by another colleague that the original manuscript’s ancestral state reconstrction lacked an outgroup. An updated reconstruction using Sapeornis as an outgroup will be included in the revised manuscript. The addition of the outgroup does not change any conclusions of the manuscript.

We once again thank our reviewers for their valuable feedback and will submit a revised version of this manuscript for publication shortly. Please let us know if you have any additional comments after reading our response that we can take onboard in our revision.

References

Artuso, C., C. S. Houston, D. G. Smith and C. Rohner (2020). Great Horned Owl (Bubo virginianus), version 1.0. Birds of the World. A. F. Poole. Ithaca, NY, USA, Cornell Lab of Ornithology.

Atterholt, J., A. W. Poust, G. M. Erickson and J. K. O'Connor (2021). "Intraskeletal osteohistovariability reveals complex growth strategies in a Late Cretaceous enantiornithine." Frontiers in Earth Science 9: 640220.

Corbin, C. E., L. K. Lowenberger and B. L. Gray (2015). "Linkage and trade‐off in trophic morphology and behavioural performance of birds." Functional ecology 29(6): 808-815.

Hone, D. W. E., A. A. Farke and M. J. Wedel (2016). "Ontogeny and the fossil record: what, if anything, is an adult dinosaur?" Biology letters 12(2): 20150947.

Hu, H. and J. K. O'Connor (2017). "First species of Enantiornithes from Sihedang elucidates skeletal development in Early Cretaceous enantiornithines." Journal of Systematic Palaeontology 15(11): 909-926.

Miller, C. V., M. Pittman, X. Wang, X. Zheng and J. A. Bright (2023). "Quantitative investigation of Mesozoic toothed birds (Pengornithidae) diet reveals earliest evidence of macrocarnivory in birds." iScience 26(3): 106211.

Olsen, A. M. (2017). "Feeding ecology is the primary driver of beak shape diversification in waterfowl." Functional Ecology 31(10): 1985-1995.

Schnell, J. H. (2020). Common Black Hawk (Buteogallus anthracinus), version 1.0. Birds of the World. A. F. Poole and F. B. Gill. Ithaca, NY, USA, Cornell Lab of Ornithology.

Author Response

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

eLife assessment

This important study combines a range of advanced ultrastructural imaging approaches to define the unusual endosomal system of African trypanosomes. Compelling images show that instead of a distinct set of compartments, the endosome of these protists comprises a continuous system of membranes with functionally distinct subdomains as defined by canonical markers of early, late and recycling endosomes. The findings suggest that the endocytic system of bloodstream stages has evolved to facilitate the extraordinarily high rates of membrane turnover needed to remove immune complexes and survive in the blood, which is of interest to anyone studying infectious diseases.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

Bloodstream stages of the parasitic protist, Trypanosoma brucei, exhibit very high rates of constitutive endocytosis, which is needed to recycle the surface coat of Variant Surface Glycoproteins (VSGs) and remove surface immune complexes. While many studies have shown that the endo-lysosomal systems of T. brucei BF stages contain canonical domains, as defined by classical Rab markers, it has remained unclear whether these protists have evolved additional adaptations/mechanisms for sustaining these very high rates of membrane transport and protein sorting. The authors have addressed this question by reconstructing the 3D ultrastructure and functional domains of the T. brucei BF endosome membrane system using advanced electron tomography and super-resolution microscopy approaches. Their studies reveal that, unusually, the BF endosome network comprises a continuous system of cisternae and tubules that contain overlapping functional subdomains. It is proposed that a continuous membrane system allows higher rates of protein cargo segregation, sorting and recycling than can otherwise occur when transport between compartments is mediated by membrane vesicles or other fusion events.

Strengths:

The study is a technical tour-de-force using a combination of electron tomography, super-resolution/expansion microscopy, immune-EM of cryo-sections to define the 3D structures and connectivity of different endocytic compartments. The images are very clear and generally support the central conclusion that functionally distinct endocytic domains occur within a dynamic and continuous endosome network in BF stages.

Weaknesses:

The authors suggest that this dynamic endocytic network may also fulfil many of the functions of the Golgi TGN and that the latter may be absent in these stages. Although plausible, this comment needs further experimental support. For example, have the authors attempted to localize canonical makers of the TGN (e.g. GRIP proteins) in T. brucei BF and/or shown that exocytic carriers bud directly from the endosomes?

We agree with the criticism and have shortened the discussion accordingly and clearly marked it as speculation. However, we do not want to completely abandon our hypothesis.

The paragraph now reads:

Lines 740 – 751:

“Interestingly, we did not find any structural evidence of vesicular retrograde transport to the Golgi. Instead, the endosomal ‘highways’ extended throughout the posterior volume of the trypanosomes approaching the trans-Golgi interface. It is highly plausible that this region represents the convergence point where endocytic and biosynthetic membrane trafficking pathways merge. A comparable merging of endocytic and biosynthetic functions has been described for the TGN in plants. Different marker proteins for early and recycling endosomes were shown to be associated and/ or partially colocalized with the TGN suggesting its function in both secretory and endocytic pathways (reviewed in Minamino and Ueda, 2019). As we could not find structural evidence for the existence of a TGN we tentatively propose that trypanosomes may have shifted the central orchestrating function of the TGN as a sorting hub at the crossroads of biosynthetic and recycling pathways to the endosome. Although this is a speculative scenario, it is experimentally testable.”

Furthermore, we removed the lines 51 - 52, which included the suggestion of the TGN as a master regulator, from the abstract.

Reviewer #2 (Public Review):

The authors suggest that the African trypanosome endomembrane system has unusual organisation, in that the entire system is a single reticulated structure. It is not clear if this is thought to extend to the lysosome or MVB. There is also a suggestion that this unusual morphology serves as a trans-(post)Golgi network rather than the more canonical arrangement.

The work is based around very high-quality light and electron microscopy, as well as utilising several marker proteins, Rab5A, 11 and 7. These are deemed as markers for early endosomes, recycling endosomes and late or pre-lysosomes. The images are mostly of high quality but some inconsistencies in the interpretation, appearance of structures and some rather sweeping assumptions make this less easy to accept. Two perhaps major issues are claims to label the entire endosomal apparatus with a single marker protein, which is hard to accept as certainly this reviewer does not really even know where the limits to the endosomal network reside and where these interface with other structures. There are several additional compartments that have been defined by Rob proteins as well, and which are not even mentioned. Overall I am unconvinced that the authors have demonstrated the main things they claim.<br /> The endomembrane system in bloodstream form T. brucei is clearly delimited. Compared to mammalian cells it is tidy and confined to the posterior part of the spindleshaped cell. The endoplasmic reticulum is linked to one side of the longitudinal cell axis, marked by the attached flagellum, while the mitochondrion locates to the opposite side. Glycosomes are easily identifiable as spheres, as are acidocalcisomes, which are smaller than glycosomes and – in electron micrographs – are characterized by high electron density. All these organelles extend beyond the nucleus, which is not the case for the endosomal compartment, the lysosome and the Golgi. The vesicles found in the posterior half of the trypanosome cell are quantitatively identifiable as COP1, CCVI or CCVII vesicles, or exocytic carriers. The lysosome has a higher degree of morphological plasticity, but this is not topic of the present work. Thus, the endomembrane system in T. brucei is comparatively well structured and delimited, which is why we have chosen trypanosomes as cell biological model.

We have published EP1::GFP as marker for the endosome system and flagellar pocket back in 2004. We have defined the fluid phase volume of the trypanosome endosome in papers published between 2002 and 2007. This work was not intended to represent the entirety of RAB proteins. We were only interested in 3 canonical markers for endosome subtypes. We do not claim anything that is not experimentally tested, we have clearly labelled our hypotheses as such, and we do not make sweeping assumptions.

The approaches taken are state-of-the-art but not novel, and because of the difficulty in fully addressing the central tenet, I am not sure how much of an impact this will have beyond the trypanosome field. For certain this is limited to workers in the direct area and is not a generalisable finding.

To the best of our knowledge, there is no published research that has employed 3D Tokuyasu or expansion microscopy (ExM) to label endosomes. The key takeaway from our study, which is the concept that "endosomes are continuous in trypanosomes" certainly is novel. We are not aware of any other report that has demonstrated this aspect.

The doubts formulated by the reviewer regarding the impact of our work beyond the field of trypanosomes are not timely. Indeed, our results, and those of others, show that the conclusions drawn from work with just a few model organisms is not generalisable. We are finally on the verge of a new cell biology that considers the plethora of evolutionary solutions beyond ophistokonts. We believe that this message should be widely acknowledged and considered. And we are certainly not the only ones who are convinced that the term "general relevance" is unscientific and should no longer be used in biology.

Reviewer #3 (Public Review):

Summary:

As clearly highlighted by the authors, a key plank in the ability of trypanosomes to evade the mammalian host’s immune system is its high rate of endocytosis. This rapid turnover of its surface enables the trypanosome to ‘clean’ its surface removing antibodies and other immune effectors that are subsequently degraded. The high rate of endocytosis is likely reflected in the organisati’n and layout of the endosomal system in these parasites. Here, Link et al., sought to address this question using a range of light and three-dimensional electron microscopy approaches to define the endosomal organisation in this parasite.

Before this study, the vast majority of our information about the make-up of the trypanosome endosomal system was from thin-section electron microscopy and immunofluorescence studies, which did not provide the necessary resolution and 3D information to address this issue. Therefore, it was not known how the different structures observed by EM were related. Link et al., have taken advantage of the advances in technology and used an impressive combination of approaches at the LM and EM level to study the endosomal system in these parasites. This innovative combination has now shown the interconnected-ness of this network and demonstrated that there are no ‘classical’ compartments within the endosomal system, with instead different regions of the network enriched in different protein markers (Rab5a, Rab7, Rab11).

Strengths:

This is a generally well-written and clear manuscript, with the data well-presented supporting the majority of the conclusions of the authors. The authors use an impressive range of approaches to address the organisation of the endosomal system and the development of these methods for use in trypanosomes will be of use to the wider parasitology community.

I appreciate their inclusion of how they used a range of different light microscopy approaches even though for instance the dSTORM approach did not turn out to be as effective as hoped. The authors have clearly demonstrated that trypanosomes have a large interconnected endosomal network, without defined compartments and instead show enrichment for specific Rabs within this network.

Weaknesses:

My concerns are:

i) There is no evidence for functional compartmentalisation. The classical markers of different endosomal compartments do not fully overlap but there is no evidence to show a region enriched in one or other of these proteins has that specific function. The authors should temper their conclusions about this point.

The reviewer is right in stating that Rab-presence does not necessarily mean Rabfunction. However, this assumption is as old as the Rab literature. That is why we have focused on the 3 most prominent endosomal marker proteins. We report that for endosome function you do not necessarily need separate membrane compartments. This is backed by our experiments.

ii) The quality of the electron microscopy work is very high but there is a general lack of numbers. For example, how many tomograms were examined? How often were fenestrated sheets seen? Can the authors provide more information about how frequent these observations were?

The fenestrated sheets can be seen in the majority of the 37 tomograms recorded of the posterior volume of the parasites. Furthermore, we have randomly generated several hundred tiled (= very large) electron micrographs of bloodstream form trypanosomes for unbiased analyses of endomembranes. In these 2D-datasets the “footprint” of the fenestrated flat and circular cisternae is frequently detectable in the posterior cell area.

We now have included the corresponding numbers in all EM figure legends.

iii) The EM work always focussed on cells which had been processed before fixing. Now, I understand this was important to enable tracers to be used. However, given the dynamic nature of the system these processing steps and feeding experiments may have affected the endosomal organisation. Given their knowledge of the system now, the authors should fix some cells directly in culture to observe whether the organisation of the endosome aligns with their conclusions here.

This is a valid criticism; however, it is the cell culture that provides an artificial environment. As for a possible effect of cell harvesting by centrifugation on the integrity and functionality of the endosome system, we consider this very unlikely for one simple reason. The mechanical forces acting in and on the parasites as they circulate in the extremely crowded and confined environment of the mammalian bloodstream are obviously much higher than the centrifugal forces involved in cell preparation. This becomes particularly clear when one considers that the mass of the particle to be centrifuged determines the actual force exerted by the g-forces. Nevertheless, the proposed experiment is a good control, although much more complex than proposed, since tomography is a challenging technique. We have performed the suggested experiment and acquired tomograms of unprocessed cells. The corresponding data is now included as supplementary movie 2, 3 and 4. We refer to it in lines 202 – 206: To investigate potential impacts of processing steps (cargo uptake, centrifugation, washing) on endosomal organization, we directly fixed cells in the cell culture flask, embedded them in Epon, and conducted tomography. The resulting tomograms revealed endosomal organization consistent with that observed in cells fixed after processing (see Supplementary movie 2, 3, and 4).

We furthermore thank the reviewer for the experiment suggestion in the acknowledgments.

iv) The discussion needs to be revamped. At the moment it is just another run through of the results and does not take an overview of the results presenting an integrated view. Moreover, it contains reference to data that was not presented in the results.

We have improved the discussion accordingly.

Recommendations for the authors:

The reviewers concurred about the high calibre of the work and the importance of the findings.

They raised some issues and made some suggestions to improve the paper without additional experiments - key issues include

(1) Better referencing of the trypanosome endocytosis/ lysosomal trafficking literature.

The literature, especially the experimental and quantitative work, is very limited. We now provide a more complete set of references. However, we would like to mention that we had cited a recent review that critically references the trypanosome literature with emphasis on the extensive work done with mammalian cells and yeast.

(2) Moving the dSTORM data that detracts from otherwise strong data in a supplementary figure.

We have done this.

(3) Removal of the conclusion that the continuous endosome fulfils the functions of TGN, without further evidence.

As stated above, this was not a conclusion in our paper, but rather a speculation, which we have now more clearly marked as such. Lines 740 to 751 now read:

“Interestingly, we did not find any structural evidence of vesicular retrograde transport to the Golgi. Instead, the endosomal ‘highways’ extended throughout the posterior volume of the trypanosomes approaching the trans-Golgi interface. It is highly plausible that this region represents the convergence point where endocytic and biosynthetic membrane trafficking pathways merge. A comparable merging of endocytic and biosynthetic functions was already described for the TGN in plants. Different marker proteins for early and recycling endosomes were shown to be associated and/ or partially colocalized with the TGN suggesting its function in both secretory and endocytic pathways (reviewed in Minamino and Ueda, 2019). As we could not find structural evidence for the existence of a TGN we tentatively propose that trypanosomes may have shifted the central orchestrating function of the TGN as a sorting hub at the crossroads of biosynthetic and recycling pathways to the endosome. Although this is a speculative scenario, it is experimentally testable.”

(4) Broader discussion linking their findings to other examples of organelle maturation in eukaryotes (e.g cisternal maturation of the Golgi)

We have improved the discussion accordingly.

Reviewer #1 (Recommendations For The Authors):

What are the multi-vesicular vesicles that surround the marked endosomal compartments in Fig 1. Do they become labelled with fluid phase markers with longer incubations (e.g late endosome/ lysosomal)?

The function of MVBs in trypanosomes is still far from being clear. They are filled with fluid phase cargo, especially ferritin, but are devoid of VSG. Hence it is likely that MVBs are part of the lysosomal compartment. In fact, this part of the endomembrane system is highly dynamic. MVBs can be physically connected to the lysosome or can form elongated structures. The surprising dynamics of the trypanosome lysosome will be published elsewhere.

Figure 2. The compartments labelled with EP1::Halo are very poorly defined due to the low levels of expression of the reporter protein and/or sensitivity of detection of the Halo tag. Based on these images, it would be hard to conclude whether the endosome network is continuous or not. In this respect, it is unclear why the authors didn't use EP1-GFP for these analyses? Given the other data that provides more compelling evidence for a single continuous compartment, I would suggest removing Fig 2A.

We have used EP1::GFP to label the entire endosome system (Engstler and Boshart, 2004). Unfortunately, GFP is not suited for dSTORM imaging. By creating the EP1::Halo cell line, we were able to utilize the most prominent dSTORM fluorescent dye, Alexa 647. This was not primarily done to generate super resolution images, but rather to measure the dynamics of the GPI-anchored, luminal protein EP with single molecule precision. The results from this study will be published separately. But we agree with the reviewer and have relocated the dSTORM data to the supplementary material.

The observation that Rab5a/7 can be detected in the lumen of lysosome is interesting. Mechanistically, this presumably occurs by invagination of the limiting membrane of the lysosome. Is there any evidence that similar invagination of cytoplasmic markers occurs throughout or in subdomains of the endocytic network (possibly indicative of a 'late endosome' domain)?

So far, we have not observed this. The structure of the lysosome and the membrane influx from the endosome are currently being investigated.

The authors note that continuity of functionally distinct membrane compartments in the secretory/endocytic pathways has been reported in other protists (e.g T. cruzi). A particular example that could be noted is the endo-lysosomal system of Dictyostelium discoideum which mediates the continuous degradation and eventual expulsion of undigested material.

We tried to include this in the discussion but ultimately decided against it because the Dictyostelium system cannot be easily compared to the trypanosome endosome.

Reviewer #2 (Recommendations For The Authors):

Abstract

Not sure that 'common' is the correct term here. Frequent, near-universal..... it would be true that endocytosis is common across most eukaryotes.

We have changed the sentence to “common process observed in most eukaryotes” (line 33).

Immune evasion - the parasite does not escape the immune system, but does successfully avoid its impact, at least at the population level.

We have replaced the word “escape” with “evasion” (line 35).

The third sentence needs to follow on correctly from the second. Also, more than Igs are internalised and potentially part of immune evasion, such as C3, Factor H, ApoL1 etcetera.

We believe that there may be a misunderstanding here. The process of endocytic uptake and lysosomal degradation has so far only been demonstrated in the context of VSGbound antibodies, which is why we only refer to this. Of course, the immune system comprises a wide range of proteins and effector molecules, all of which could be involved in immune evasion.

I do not follow the logic that the high flux through the endocytic system in trypanosomes precludes distinct compartmentalisation - one could imagine a system where a lot of steps become optimised for example. This idea needs expanding on if it is correct.

Membrane transport by vesicle transfer between several separate membrane compartments would be slower than the measured rate of membrane flux.

Again I am not sure 'efficient' on line 40. It is fast, but how do you measure efficiency? Speed and efficiency are not the same thing.

We have replaced the word “efficient” with “fast” (line 42).

The basis for suggesting endosomes as a TGN is unclear. Given that there are AP complexes, retromer, exocyst and other factors that are part of the TGN or at least post-G differentiation of pathways in canonical systems, this seems a step too far. There really is no evidence in the rest of the MS that seems to support this.

Yes, we agree and have clarified the discussion accordingly. We have not completely removed the discussion on the TGN but have labelled it more clearly as speculation.

I am aware I am being pedantic here, but overall the abstract seems to provide an impression of greater novelty than may be the case and makes several very bold claims that I cannot see as fully valid.

We are not aware of any claim in the summary that we have not substantiated with experiments, or any hypothesis that we have not explained.

Moreover, the concept of fused or multifunctional endosomes (or even other endomembrane compartments) is old, and has been demonstrated in metazoan cells and yeast. The concept of rigid (in terms of composition) compartments really has been rejected by most folks with maturation, recycling and domain structures already well-established models and concepts.

We agree that the (transient) presence of multiple Rab proteins decorating endosomes has been demonstrated in various cell types. This finding formed the basis for the endosomal maturation model in mammals and yeast, which has replaced the previous rigid compartment model.

However, we do not appreciate attempts to question the originality of our study by claiming that similar observations have been made in metazoans or yeast. This is simply wrong. There are no reports of a functionally structured, continuous, single and large endosome in any other system. The only membrane system that might be similar was described in the American parasite Trypanosoma cruzi, however, without the use of endosome markers or any functional analysis. We refer to this study in the discussion.

In summary, the maturation model falls short in explaining the intricacies of the membrane system we have uncovered in trypanosomes. Therefore, one plausible interpretation of our data is that the overall architecture of the trypanosome endosomes represents an adaptation that enables the remarkable speed of plasma membrane recycling observed in these parasites. In our view, both our findings and their interpretation are novel and worth reporting. Again, modern cell biology should recognize that evolution has developed many solutions for similar processes in cells, about whose diversity we have learned almost nothing because of our reductionist view. A remarkable example of this are the Picozoa, tiny bipartite eukaryotes that pack the entire nutritional apparatus into one pouch and the main organelles with the locomotor system into the other. Another one is the “extreme” cell biology of many protozoan parasites such as Giardia, Toxpoplasma or Trypanosoma.

Higher plants have been well characterised, especially at the level of Rab/Arf proteins and adaptins.

We now mention plant endosomes in our brief discussion of the trypanosome TGN. Lines 744 – 747:

“A comparable merging of endocytic and biosynthetic functions was already described for the TGN in plants. Different marker proteins for early and recycling endosomes were shown to be associated and/ or partially colocalized with the TGN suggesting its function in both secretory and endocytic pathways (reviewed in Minamino and Ueda, 2019).”

The level of self-citing in the introduction is irritating and unscholarly. I have no qualms with crediting the authors with their own excellent contributions, but work from Dacks, Bangs, Field and others seems to be selectively ignored, with an awkward use of the authors' own publications. Diversity between organisms for example has been a mainstay of the Dacks lab output, Rab proteins and others from Field and work on exocytosis and late endosomal systems from Bangs. These efforts and contributions surely deserve some recognition?

This is an original article and not a review. For a comprehensive overview the reviewer might read our recent overview article on exo- and endocytic pathways in trypanosomes, in which we have extensively cited the work of Mark Field, Jay Bangs and Joel Dacks. In the present manuscript, we have cited all papers that touch on our results or are otherwise important for a thorough understanding of our hypotheses. We do not believe that this approach is unscientific, but rather improves the readability of the manuscript. Nevertheless, we have now cited additional work.

For the uninitiated, the posterior/anterior axis of the trypanosome cell as well as any other specific features should be defined.

In lines 102 - 110 we wrote:

“This process of antibody clearance is driven by hydrodynamic drag forces resulting from the continuous directional movement of trypanosomes (Engstler et al., 2007). The VSG-antibody complexes on the cell surface are dragged against the swimming direction of the parasite and accumulate at the posterior pole of the cell. This region harbours an invagination in the plasma membrane known as the flagellar pocket (FP) (Gull, 2003; Overath et al., 1997). The FP, which marks the origin of the single attached flagellum, is the exclusive site for endo- and exocytosis in trypanosomes (Gull, 2003; Overath et al., 1997). Consequently, the accumulation of VSG-antibody complexes occurs precisely in the area of bulk membrane uptake.”

We think this sufficiently introduces the cell body axes.

I don't understand the comment concerning microtubule association. In mammalian cells, such association is well established, but compartments still do not display precise positioning. This likely then has nothing to do with the microtubule association differences.

We have clarified this in the text (lines 192 – 199). There is no report of cytoplasmic microtubules in trypanosomes. All microtubules appear to be either subpellicular or within the flagellum. To maintain the structure and position of the endosomal apparatus, they should be associated either with subpellicular microtubules, as is the case with the endoplasmic reticulum, or with the more enigmatic actomyosin system of the parasites. We have been working on the latter possibility and intend to publish a follow-up paper to the present manuscript.

The inability to move past the nucleus is a poor explanation. These compartments are dynamic. Even the nucleus does interesting things in trypanosomes and squeezes past structures during development in the tsetse fly.

The distance between the nucleus and the microtubule cytoskeleton remains relatively constant even in parasites that squeeze through microfluidic channels. This is not unexpected as the nucleus can be highly deformed. A structure the size of the endosome will not be able to physically pass behind the nucleus without losing its integrity. In fact, the recycling apparatus is never found in the anterior part of the trypanosome, most probably because the flagellar pocket is located at the posterior cell pole.

L253 What is the evidence that EP1 labels the entire FP and endosomes? This may be extensive, but this claim requires rather more evidence. This is again suggested at l263. Again, please forgive me for being pedantic, but this is an overstatement unless supported by evidence that would be incredibly difficult to obtain. This is even sort of acknowledged on l271 in the context of non-uniform labelling. This comes again in l336.

The evidence that EP1 labels the entire FP and endosomes is presented here: Engstler and Boshart, 2004; 10.1101/gad.323404).

Perhaps I should refrain from comments on the dangers of expansion microscopy, or asking what has actually been gained here. Oddly, the conclusion on l290 is a fair statement that I am happy with.

An in-depth discussion regarding the advantages and disadvantages of expansion microscopy is beyond the manuscript's intended scope. Our approach involved utilizing various imaging techniques to confirm the validity of our findings. We appreciate that our concluding sentence is pleasing.

F2 - The data in panel A seem quite poor to me. I also do not really understand why the DAPI stain in the first and second columns fails to coincide or why the kinetoplast is so diffuse in the second row. The labelling for EP1 presents as very small puncta, and hence is not evidence for a continuum. What is the arrow in A IV top? The data in panel B are certainly more in line with prior art, albeit that there is considerable heterogeneity in the labelling and of the FP for example. Again, I cannot really see this as evidence for continuity. There are gaps.... Albeit I accept that labelling of such structures is unlikely to ever be homogenous.

We agree that the dSTORM data represents the least robust aspect of the findings we have presented, and we concur with relocating it to the supplementary material.

F3 - Rather apparent, and specifically for Rab7, that there is differential representation - for example, Cell 4 presents a single Rab7 structure while the remaining examples demonstrate more extensive labelling. Again, I am content that these are highly dynamic strictures but this needs to be addressed at some level and commented upon. If the claim is for continuity, the dynamics observed here suggest the usual; some level of obvious overlap of organellar markers, but the representation in F3 is clever but not sure what I am looking at. Moreover, the title of the figure is nothing new. What is also a bit odd is that the extent of the Rab7 signal, and to some extent the other two Rabs used, is rather variable, which makes this unclear to me as to what is being detected. Given that the Rab proteins may be defining microdomains or regions, I would also expect a region of unique straining as well as the common areas. This needs to at least be discussed.

The differences in the representation result from the dynamics of the labelled structures. Therefore, we have selected different cells to provide examples of what the labelling can look like. We now mention this in the results section.

The overlap of the different Rab signals was perhaps to be expected, but we now have demonstrated it experimentally. Importantly, we performed a rigorous quantification by calculating the volume overlaps and the Pearson correlation coefficients.

In previous studies the data were presented as maximal intensity projections, which inherently lack the complete 3D information.

We found that Rab proteins define microdomains and that there are regions of unique staining as well as common areas, as shown in Figure 3. The volumes do not completely overlap. This is now more clearly stated in lines 315 – 319:

“These objects showed areas of unique staining as well as partially overlapping regions. The pairwise colocalization of different endosomal markers is shown in Figure 3 A, XI - XIII and 3 B. The different cells in Figure 3 B were selected to represent the dynamic nature of the labelled structures. Consequently, the selected cells provide a variety of examples of how the labelling can appear.”

This had already been stated in lines 331 – 336:

“In summary, the quantitative colocalization analyses revealed that on the one hand, the endosomal system features a high degree of connectivity, with considerable overlap of endosomal marker regions, and on the other hand, TbRab5A, TbRab7, and TbRab11 also demarcate separated regions in that system. These results can be interpreted as evidence of a continuous endosomal membrane system harbouring functional subdomains, with a limited amount of potentially separated early, late or recycling endosomes.”

F4-6 - Fabulous images. But a couple of issues here; first, as the authors point out, there is distance between the gold and the antigen. So, this of course also works in the z-plane as well as the x/y-planes and some of the gold may well be associated with membraneous figures that are out of the plane, which would indicate an absence of colinearity on one specific membrane. Secondly, in several instances, we have Rab7 essentially mixed with Rab11 or Rab5 positive membrane. While data are data and should be accepted, this is difficult to reconcile when, at least to some level, Rab7 is a marker for a late-endosomal structure and where the presence of degradative activity could reside. As division of function is, I assume, the major reason for intracellular compartmentalisation, such a level of admixture is hard to rationalise. A continuum is one thing but the data here seem to be suggesting something else, i.e. almost complete admixture.

We are grateful for the positive feedback regarding the image quality. It is true that the "linkage error," representing the distance between the gold and the antigen, also functions to some extent in the z-axis. However, it's important to note that the zdimension of the section in these Figures is 55 nm. Nevertheless, it's interesting to observe that membranes, which may not be visible within the section itself but likely the corresponding Rab antigen, is discernible in Figure 4C (indicated by arrows).

We have clarified this in lines 397 – 400:

“Consequently, gold particles located further away may represent cytoplasmic TbRab proteins or, as the “linkage error” can also occur in the z-plane, correspond to membranes that are not visible within the 55 nm thickness of the cryosection (Figure 4, panel C, arrows). “

The coexistence of different Rabs is most likely concentrated in regions where transitions between different functions are likely. Our focus was primarily on imaging membranes labelled with two markers. We wanted to show that the prevailing model of separate compartments in the trypanosome literature is not correct.

F7 - Not sure what this adds beyond what was published by Grunfelder.

First, this figure is an important control that links our results to published work (Grünfelder et al. (2003)). Second, we include double staining of cargo with Rab5, Rab7, and Rab11, whereas Grünfelder focused only on Rab11. Therefore, our data is original and of such high quality that it warrants a main figure.

F8 - and l583. This is odd as the claim is 'proof' which in science is a hard thing to claim (and this is definitely not at a six sigma level of certainty, as used by the physics community). However, I am seeing structures in the tomograms which are not contiguous - there are gaps here between the individual features (Green in the figure).

We have replaced the term "proof". It is important to note that the structures in individual tomograms cannot all be completely continuous because the sections are limited to a thickness of 250 nm. Therefore, it is likely that they have more connectivity above and below the imaged section. Nevertheless, we believe that the quality of the tomograms is satisfactory, considering that 3D Tokuyasu is a very demanding technique and the production of serial Tokuyasu tomograms is not feasible in practice.

Discussion - Too long and the self-citing of four papers from the corresponding author to the exclusion of much prior work is again noted, with concerns about this as described above. Moreover, at least four additional Rab proteins are known associated with the trypanosome endosomal system, 4, 5B, 21 and 28. These have been completely ignored.

We have outlined our position on referencing in original articles above. We also explained why we focused on the key marker proteins associated with early (Rab5), late (Rab7) and recycling endosomes (Rab11). We did not ignore the other Rabs, we just did not include them in the present study.

Overall this is disappointing. I had expected a more robust analysis, with a clearer discussion and placement in context. I am not fully convinced that what we have here is as extreme as claimed, or that we have a substantial advance. There is nothing here that is mechanistic or the identification of a new set of gene products, process or function.

We do not think that this is constructive feedback.

This MS suggests that the endosomal system of African trypanosomes is a continuum of membrane structures rather than representing a set of distinct compartments. A combination of light and electron microscopy methods are used in support. The basic contention is very challenging to prove, and I'm not convinced that this has been. Furthermore, I am also unclear as to the significance of such an organisation; this seems not really addressed.

We acknowledge and respect varying viewpoints, but we hold a differing perspective in this matter. We are convinced that the data decisively supports our interpretation. May future work support or refute our hypothesis.

Reviewer #3 (Recommendations For The Authors):

Line 81 - delete 's

Done.

Generally, the introduction was very well written and clearly summarised our current understanding but the paragraph beginning line 134 felt out of place and repeated some of the work mentioned earlier.

We have removed this paragraph.

For the EM analysis throughout quantification would be useful as highlighted in the public review. How many tomograms were examined, and how often were types of structures seen? I understand the sample size is often small but this would help the reader appreciate the diversity of structures seen.

We have included the numbers.

Following on from this how were the cells chosen for tomogram analysis? For example, the dividing cell in 1D has palisades associating with the new pocket - is this commonly seen? Does this reflect something happening in dividing cells. This point about endosomal division was picked up in the discussion but there was little about in the main results.

This issue is undoubtedly inherent to the method itself, and we have made efforts to mitigate it by generating a series of tomograms recorded randomly. We have refrained from delving deeper into the intricacies of the cell cycle in this manuscript, as we believe that it warrants a separate paper.

As the authors prosecute, the co-localisation analysis highlights the variable nature of the endosome and the overlap of different markers. When looking at the LM analysis, I was struck by the variability in the size and number of labelled structures in the different cells. For example, in 3A Rab7 is 2 blobs but in 3B Cell 1 it is 4/5 blobs. Is this just a reflection of the increase in the endosome during the cell cycle?

The variability in representation is a direct consequence of the dynamic nature of the labelled structures. For this reason, we deliberately selected different cells to represent examples of how the labelling can look like. We have decided not to mention the dynamics of the endosome during the cell cycle. This will be the subject of a further report.

Moreover, Rab 11 looks to be the marker covering the greatest volume of the endosomal system - is this true? I think there's more analysis of this data that could be done to try and get more information about the relative volumes etc of the different markers that haven't been drawn out. The focus here is on the co-localisation.

Precisely because we recognize the importance of this point, we intend to turn our attention to the cell cycle in a separate publication.

I appreciate that it is an awful lot of work to perform the immuno-EM and the data is of good quality but in the text, there could be a greater effort to tie this to the LM data. For example, from the Rab11 staining in LM you would expect this marker to be the most extensive across the networks - is this reflected in the EM?

For the immuno-EM there were no numbers, the authors had measured the position of the gold but what was the proportion of gold that was in/near membranes for each marker? This would help the reader understand both the number of particles seen and the enrichment of the different regions.

Our original intent was to perform a thorough quantification (using stereology) of the immuno-EM data. However, we later realized that the necessary random imaging approach is not suitable for Tokuyasu sections of trypanosomes. In short, the cells are too far apart, and the cell sections are only occasionally cut so that the endosomal membranes are sufficiently visible. Nevertheless, we continue to strive to generate more quantitative data using conventional immuno-EM.

The innovative combination of Tokuyasu tomograms with immuno-EM was great. I noted though that there was a lack of fenestration in these models. Does this reflect the angle of the model or the processing of these samples?

We are grateful to the referee, as we have asked ourselves the same question. However, we do not attribute the apparent lack of fenestration to the viewing angle, since we did not find fenestration in any of the Tokuyasu tomograms. Our suspicion is more directed towards a methodological problem. In the Tokuyasu workflow, all structures are mainly fixed with aldehydes. As a result, lipids are only effectively fixed through their association with membrane proteins. We suggest that the fenestration may not be visible because the corresponding lipids may have been lost due to incomplete fixation.

We now clearly state this in the lines 563 – 568.

“Interestingly, these tomograms did not exhibit the fenestration pattern identified in conventional electron tomography. We suspect that this is due to methodological reasons. The Tokuyasu procedure uses only aldehydes to fix all structures. Consequently, effective fixation of lipids occurs only through their association with membrane proteins. Thus, the lack of visible fenestration is likely due to possible loss of lipids during incomplete fixation.”

The discussion needs to be reworked. Throughout it contains references to results not in the main results section such as supplementary movie 2 (line 735). The explicit references to the data and figures felt odd and more suited to the results rather than the discussion. Currently, each result is discussed individually in turn and more effort needs to be made to integrate the results from this analysis here but also with previous work and the data from other organisms, which at the moment sits in a standalone section at the end of the discussion.

We have improved the discussion and removed the previous supplementary movies 2 and 3. Supplementary movie 1 is now mentioned in the results section.

Line 693 - There was an interesting point about dividing cells describing the maintenance of endosomes next to the old pocket. Does that mean there was no endosome by the new pocket and if so where is this data in the manuscript? This point relates back to my question about how cells were chosen for analysis - how many dividing cells were examined by tomography?

The fate of endosomes during the cell cycle is not the subject of this paper. In this manuscript we only show only one dividing cell using tomography. An in-depth analysis focusing on what happens during the cell cycle will be published separately.

Line 729 - I'm unclear how this represents a polarization of function in the flagellar pocket. The pocket I presume is included within the endosomal system for this analysis but there was no specific mention of it in the results and no marker of each position to help define any specialisation. From the results, I thought the focus was on endosomal co-localisation of the different markers. If the authors are thinking about specialisation of the pocket this paper from Mark Field shows there is evidence for the exocyst to be distributed over the entire surface of the pocket, which is relevant to the discussion here. Boehm, C.M. et al. (2017) The trypanosome exocyst: a conserved structure revealing a new role in endocytosis. PLoS Pathog. 13, e1006063

We have formulated our statement more cautiously. However, we are convinced that membrane exchange cannot physically work without functional polarization of the pocket. We know that Rab11, for example, is not evenly distributed on the pocket. By the way, in Boehm et al. (2017) the exocyst is not shown to cover the entire pocket (as shown in Supplementary Video 1).

We now refer to Boehm et al. (Lines 700 – 703):

“Boehm et al (2017) report that in the flagellar pocket endocytic and exocytic sites are in close proximity but do not overlap. We further suggest that the fusion of EXCs with the flagellar pocket membrane and clathrin-mediated endocytosis take place on different sites of the pocket. This disparity explains the lower colocalization between TbRab11 and TbRab5A.”

Line 735 - link to data not previously mentioned I think. When I looked at this data I couldn't find a key to explain what all the different colours related to.

We have removed the previous supplementary movies 2 and 3. We now reference supplementary movie 1 in the results section.

Author Response

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

The current work by Kulich et al. examines the dynamic relocalization of NGR1 (LAZY2) a member of the LAZY protein family which is key for auxin redistribution during gravitropic responses. After gravistimulation of the triple mutant ngr123 (lazy234), the PIN3 activating kinase D6PK is not polarized in the columella cells.

Strengths:

The authors show a thorough characterization of NGR1 relocalization dynamics after gravistimulation.

Weaknesses:

Genetically the relocalization of D6PK depends on the LAZY protein family, but some essential details are missing in this study. On the one hand, NGR1-GFP does not associate with the BFA compartments and maintains its association with the PM and amyloplasts. On the other hand, D6PK relies on GNOM, via vesicle trafficking sensitive to BFA, suggesting that D6PK follows a different relocalization route than NGR1 which is BFA-insensitive. Based on these observations, D6PK relocalization requires the LAZY proteins, but D6PK and NGR1 relocalize through independent routes. How can this be interpreted or reconciled?

Response: Since we demonstrated that D6PK does not relocalize in the absence of NGR proteins, we conclude that NGR1 acts upstream of D6PK. The molecular mechanism driving this interaction is not fully understood; however, it is evident that NGR1 triggers the mobilization of D6PK. Despite previous investigations into D6PK mobility, the underlying mechanisms remain elusive. Notably, despite its sensitivity to BFA, D6PK does not localize to BFA bodies and does not undergo conventional endocytosis (https://doi.org/10.1016/j.devcel.2014.05.006). We fully acknowledge the importance and interest in gaining a better understanding of these processes, and it will be a focal point of our future research.

Two other works (now published) provide valuable and fundamental findings related to the mechanism examined in the current manuscript and display complementary and similar results to the ones shown in the current manuscript. Given the similarities in the examined mechanisms, these preprints should be referenced, recognized, and discussed in the manuscript under review. It is assumed that the three projects were independently developed, but the results of these previous works should be addressed and taken into account at least during the discussion and when drawing any conclusions. This does not mean that this work is less relevant. On the contrary, some of the observations that seem to be redundant are more solid, and firm conclusions can now be drawn from them.

Response: We have included and discussed these works in the revised discussion

Reviewer #2 (Public Review):

Summary:

This manuscript addresses what rapid molecular events underly the earliest responses after gravity-sensing via the sedimentation of starch-enriched amyloplasts in columella cells of the plant root cap. The LAZY or NEGATIVE GRAVITROPIC RESPONSE OF ROOTS (NGR) protein family is involved in this process and localizes to both the amyloplast and to the plasma membrane (PM) of columella cells.

The current manuscript complements and extends Nishimura et al., Science, 2023. Kulich and colleagues describe the role of the LZY2 protein, also called NGR1, during this process, imaging its fast relocation and addressing additional novel points such as molecular mechanisms underlying NGR1 plasma membrane association as well as revealing the requirement of NGR1/LZY2, 3,4 for the polar localization of the AGCVIII D6 protein kinase at the PM of columella cells, in which NGR1/LZY2 acts redundantly with LZY3 and LZY4.

The authors initially monitored relocalization of functional NGR1-GFP in columella cells of the ngr1 ngr2 ngr3 triple mutant after 180-degree reorientation of the roots. Within 10 -15 min NGR1-GFP signal disappeared from the upper PM after reorientation and reappeared at the lower PM of the reoriented cells in close proximity to the sedimented amyloplasts. Reorientation of NGR1-GFP occurred substantially faster than PIN3-GFP reorientation, at about the same time or slightly later than a rise in a calcium sensor (GCaMP3) just preceding a change in D2-Venus auxin sensor alterations. Reorientation of NGR1-GFP proved to be fast and not dependent on a brefeldin A-sensitive ARF GEF-mediated vesicle trafficking, unlike the trafficking of PIN proteins, like PIN3, or the AGCVIII D6 protein kinase. Strikingly, the PM association of NGR1-GFP was highly sensitive to pharmacological interference with sterol composition or concentration and phosphatidylinositol (4)kinase inhibition as well as dithiothreitol (DTT) treatment interfering with thioester bond formation e.g. during S-acylation. Indeed, combined mutation of a palmitoylation site and polybasic regions of NRG1 abolished its PM but not its amyloplast localization and rendered the protein non-functional during the gravitropic response, suggesting NRG1 PM localization is essential for the gravitropic response. Targeting the protein to the PM via an artificially introduced N-terminal myristoylation and an ROP2-derived polybasic region and geranylgeranylation site partially restored its functionality in the gravitropic response.

Strengths:

This timely work should be of broad interest to plant, cell and developmental biologists across the field as gravity sensing and signaling may well be of general interest. The point that NGR1 is rapidly responsive to gravistimulation, polarizes at the PM in the vicinity to amyloplast and that this is required for repolarization of D6 protein kinase, prior to PIN relocation is really compelling. The manuscript is generally well-written and accessible to a general readership. The figures are clear and of high quality, and the methods are sufficiently explained for reproduction of the experiments.

Weaknesses:

Statistical analysis has been performed for some figures but is lacking for most of the quantitative analyses in the figure legends.

Response: We added this information to the figure legends

The title claims a bit more than what is actually shown in the manuscript: While auxin response reporter alterations are monitored, "rapid redirection of auxin fluxes" are not really directly addressed and, while D6PK can activate PIN proteins in other contexts, it is not explicitly shown in the manuscript that PIN3 is a target in the context of columella cells in vivo. A title such as "Rapid redirection of D6 protein kinase during Arabidopsis root gravitropism relies on plasma membrane translocation of NGR proteins" would reflect the results better.

Response: We modified the title to Rapid translocation of NGR proteins driving polarization of PIN-activating D6 protein kinase during root gravitropism

Fig. 4: The point that D6PK is transcytosed cannot be made here based on the data of these authors. They should have used a photoswitchable version of NGR1 to show that the same molecules observed at the upper PM are translocated to the lower PM. Nishimura and colleagues actually did that for NGR4. However, this is a lot of work and maybe for NGR1 that fusion would have too low fluorescence intensity (as it was the case for NGR3). So, I think a rewording would be sufficient such as NGR-dependent reorientation of D6PK plasma membrane localization" as this does not say, from where it comes to the lower PM. Theoretically, the signal could also be amyloplast-derived or newly synthesized (or just folded) NGR1-GFP.

Response: We fully agree and rephrased the text using translocation instead of transcytosis

The authors make a model in which D6PK AGCVIII kinase-dependent on NGRs activates PIN3 to drive auxin fluxes. However, alterations in auxin responses are observed prior to PIN3 reorientation. They should explain this discrepancy better and clearly describe that this is a working hypothesis for the future rather than explicitly proven, yet.

Reviewer #3 (Public Review):

The mechanism controlling plant gravity sensing has fascinated researchers for centuries. It has been clear for at least the past decade that starch-filled plastids (termed statoliths) in specialised gravity-sensing columella cells sense changes in root orientation, triggering an asymmetric auxin gradient that alters root growth direction. Nevertheless, exactly how statolith movement triggers PIN auxin efflux carrier activation and auxin gradient formation has remained unclear until very recently. A series of new papers (in Science and Cell) and this manuscript report how LAZY proteins (also referred to as NEGATIVE GRAVITROPIC 50 RESPONSE OF ROOTS; NGR) play a pivotal role in regulating root gravitropism. In terms of their overall significance, their collective findings provide seminal insights into the very earliest steps for how plant roots sense gravity which are arguably the most important papers about root gravitropism in the past decade.

In the current manuscript, Kulich et al initially report (through creating a functional NGR1-GFP reporter) that "NGR1-GFP displayed a highly specific columella expression, which was most prominent at the PM and the statolith periphery." Is NGR1-GFP expressed in shoot tissues? If yes, is it in starch sheath (the gravity-sensing equivalent of root columella cells)? The authors also note "NGR1-GFP signal from the PM was not evenly distributed, but rather polarized to the lower side of the columella cells in the vicinity of the sedimented statoliths (Fig. 1A)." and (when overexpressing NGR-GFP) "chloroplasts in the vicinity of the PM strongly correlated with NGR1 accumulating at the PM nearby, similar to the scenario in columella" suggesting that NGR1 does not require additional tissue-specific factors (i.e. trafficking proteins or lipids) to assist in its intracellular movement from plastid to PM.

Response: Yes, NGR1, also called LAZY2 is expressed in the inner hypocotyl tissues, according to https://doi.org/10.1104/pp.17.00942. Unfortunately, we saw very little signal with our NGR-GFP construct, possibly due to NGR1-GFP weak signal and/or NGR1 being expressed only exclusively in the inner tissues.

Next, the authors study the spatiotemporal dynamics of NGR1-GFP re-localisation with other early gravitropic signals and/or components Calcium, auxin, and PIN3. The temporal data presented in Figure 1 illustrates how the GCaMP calcium reporter (in panel E) revealed "the first signaling event in the root gravitropic bending is the statolith removal from the top membrane, rather than its arrival at the bottom" It appeared that the auxin DII-VENUS reporter was also changing rapidly (panel G) - was this detectable BEFORE statolith re-sedimentation?

Response: In our data (Figure 1G), we observe that the increase in signal at the top side begins prior to starch sedimentation, in contrast to the bottom side, where the decrease starts only after starch grains land on the bottom membrane. While this observation aligns with our hypothesis and other data, we refrained from commenting on it due to the small differences between the first 2-3 timepoints, which are obscured by noise. This phenomenon arises because the DII response relies on protein degradation and is relatively slow. Hence, for rapid tracking of the auxin response, we utilized auxin-induced calcium as a proxy, with NPA treatment serving as a negative control.

Please can the authors explain their NPA result in Fig 1E? Why would treatment with the auxin transport inhibitor NPA block Ca signalling (unless the latter was dependent on the former)?

Response: Auxin induces rapid calcium transients (e.g., http://dx.doi.org/10.1016/j.cub.2015.10.025). Consequently, when auxin reaches the bottom elongation zone approximately 5-6 minutes after rotation, we observe an increased GCaMP signal at this location. Notably, when we inhibit PIN function using NPA, the GCaMP signal persists, but the difference between the top and bottom diminishes. This validates that the calcium transients at the bottom side can be interpreted as monitoring increase in auxin accumulation as a result of auxin transport.

They go on to note "This initial auxin asymmetry is mediated by PIN-dependent auxin transport, despite visible polarization of PIN3 can be detected only later" which suggests that PIN activity was being modified prior to PIN polarisation.

In contrast to other proteins involved in gravity response like RLDs and PINs, NGR1 localization and gravity-induced polarization does not undergo BFA-sensitive endocytic recycling by ARF-GEF GNOM. This makes sense given NGR1 is initially targeted to plastids, THEN the PM. Does NGR1 contain a cleavable plastid targeting signal? The authors go on to elegantly demonstrate that NGR1 PM targeting relies on palmitoylation through imaging and mutagenesis-based transgenic ngr rescue assays.

Response: Yes, there is weakly conserved plastid targeting signal on NGR1. Although we also started researching in this direction, we quickly realized, that two other groups showed very comprehensive data regarding NGR plastid localization.

Finally, the authors demonstrate that gravitropic-induced auxin gradient formation is initially dependent on PIN3 auxin efflux activation (prior to PIN3 re-localisation). This early PIN3 activation process is dependent on NGR1 re-targeting D6PK (a PIN3 activating kinase). This elegant molecular mechanism integrates all the regulatory components described in the paper into a comprehensive root gravity sensing model.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Minor comments:

Line 83: This construct fully rescued the agravitropic bending phenotype of the ngr1/2/3 triple mutant (see further).

What does it mean the see further in this context?

Response: It is a reference to the second part of the manuscript (Fig. 3, Supplementary Fig S3, Fig S4), where we extensively address the complementation with wild type and point mutated versions of NGR. There we show that the construct we are using is functional. This does not prove, but strongly imply that the GFP signal we obtain is relevant. We updated the text to point this out.

Line 101: Timing of events during the gravitropic response

When describing the equipment employed and the rotation applied to the samples, "the vertical stage microscope and minimized the time required for rotating the sample. 180{degree sign} rotation..."

The authors mentioned a travel time of 5 minutes first and later of 15 minutes for the relocalization of NGR1. Are these two different experiments? Were there two different rotation angles or degrees applied? Could the authors please rephrase this part of the description to answer these questions and help the reader understand how the assay performed?

Response: We added this explanation to the text.

Figure 1 E, F, and G.

Could the authors please provide pictures and/or videos for the PIN3 localization dynamics, intracellular calcium transients, and auxin reporter DII-Venus? In other words, show the complementing images for Figure 1E, 1F, and 1G as the authors did for Figure 2D where authors presented the pictures and the corresponding quantification plots.

Response: We wanted to avoid overcrowding the figure, but we would also love to show the videos. Therefore, we did additional supplementary movie 3, where we put all the additional observations.

Line 194: This implies the existence of posttranslational modifications such as S-acylation to associate with PM.

Why is this specific modification suggested/examined and no other modification? What is the criteria to select this kind of modification? Based on what premises? Could the authors elaborate on that? Could the authors please include references?

Response: Thank you for this comment. We of course first checked the prediction tools which have shown very strongly conserved S-acylation side. We now clarified this in the text and added other modifications as an example. Later on, we rule out myristoylation (that happens on the glycins) and prenylation (it happens only at the C-terminus CAAX box).

Line 255: NGR1 PM localization is synergistically mediated by polybasic regions and a palmitoylation site

Similarly to the previous commentary, How and why are these regions examined/analyzed? Likewise, why is the palmitoylation site selected? Please provide some background, criteria, and references.

Response: Here, we clearly state that the prediction of the palmitoylation site is made based on the GPS lipid prediction tool.

As for the polybasic region, these can be seen upon manual inspection of the primary protein sequence. We simply looked at the protein and saw it there. We rephrased the text so that it is more clear.

Reviewer #2 (Recommendations For The Authors):

Please, proofread the manuscript for style and minor language errors.

Statistical analysis has been performed for some figures but is lacking for most of the quantitative analyses in the figure legends. Where it has been performed it is not given what "n" number of roots, cells, or plasma membranes were analyzed NGR1-GFP and no information is given whether the data is derived from a representative experiment or several or pooled data from several experiments. This certainly requires revision in Fig. 1D-G, Fig. 2B-D, Fig. S2 B,E, Fig. 3B,D, F-H, Fig. S.3 B,D, Fig. S. 4 ,E-H, Fig. 4 D.

Response: Thank you, we added this information to the figure legends.

Author Response

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

Public Reviews:

Reviewer #1 (Public Review):

Summary

This fascinating paper by M. Alfatah et al. describes work to uncover novel genes affecting lifespan in the budding yeast S. cerevisiae, eventually identifying and further characterizing a gene, YBR238C, now named AAG1 by the authors. The authors began by considering published gene sets pulled from the Saccharomyces genome database that described increases or decreases in either chronological lifespan or replicative lifespan in yeast. They also began with gene sets known to be downregulated upon treatment with the lifespan-extending TOR inhibitor rapamycin.

YBR283C was unique in being largely uncharacterized, downregulated upon rapamycin treatment, and linked to both increased replicative lifespan and increased chronological lifespan upon deletion.

The authors show that YBR283C may act to negatively regulate mitochondrial function, in ways that are both dependent on and independent of the stressresponsive transcription factor Hap4, largely by looking at relative expression levels of relevant mitochondrial genes.

In a hard-to-fully interpret but well-documented series of experiments the authors note that the two paralogues YBR283C and RMD9 (which have ~66% similarity) (a) have opposite effects when acting alone, and (b) appear to interact in that some phenotypes of ybr283c are dependent on RMD9.

A particularly interesting finding in light of the current literature and of the authors' strategy in identifying YBR283C is that changes in electron transport chain genes upon rapamycin treatment appear to be affected via YBR283C.

Based on a series of experiments the authors move to conclude the existence of "a feedback loop between TORC1 and mitochondria (the TORC1-Mitochondria-TORC1 (TOMITO) signaling process) that regulates cellular aging processes."

Strengths

Overall, this study describes a great deal of new data from a large number of experiments, that shed light on the potential specific roles of YBR238C and its paralog RMD9 in aging in yeast, and also underscore the potential of an approach looking for "dark matter" such as uncharacterized genes when seining the increasing deluge of published datasets for new hypotheses to test. This work when revised will become a valuable addition to the field.

Weaknesses

A paralog of YBR283C, RMD9, also exists in the yeast genome. While the authors indicate that part of their interest in YBR283C lies in its uncharacterized nature, its paralogue, RMD9, is not uncharacterized but is named due to its phenotype of Required for Meiotic nuclear Division, which is not mentioned or discussed anywhere in the manuscript currently.

In the context of the current work, in addition to the cited Hillen, H.S et al. and Nouet C. et al, the authors might be very interested in the 2007 Genetics paper "Translation initiation in Saccharomyces cerevisiae mitochondria: functional interactions among mitochondrial ribosomal protein Rsm28p, initiation factor 2, methionyl-tRNAformyltransferase and novel protein Rmd9p" (PMID: 17194786), which does not appear to be cited or discussed in the current version of the manuscript.

Thank you for your thorough and insightful review of our manuscript. We value your positive feedback and recognition of the strengths in our study. Your constructive comments have been carefully considered, leading to the inclusion of RMD9, identified as 'Required for Meiotic Nuclear Division,' and the addition of the relevant reference (PMID: 12586695) in the revised manuscript. This information has been incorporated into the second paragraph of the "The YBR238C paralogue RMD9 deletion decreases the lifespan of cells" results section.

Furthermore, we appreciate the reviewer's suggestion to include the 2007 Genetics paper on translation initiation in Saccharomyces cerevisiae mitochondria (PMID: 17194786). This citation has been integrated into our revised manuscript.

We believe that these revisions significantly strengthen the manuscript and address the concerns raised by Reviewer #1. We thank the reviewer for their time and valuable input.

Reviewer #2 (Public Review):

The effectors of cellular aging in yeast have not been fully elucidated. To address this, the authors curated gene expression studies to link genes influenced by rapamycin - a well-known mediator of longevity across model systems - to genes known to affect chronological and replicative lifespan (RLS) in yeast. Through their analyses, they find one gene, ybr238c, whose deletion increases both CLS and RLS upon deletion and that is downregulated by rapamycin. Curiously, despite these selection criteria, the authors only use CLS as a proxy for cellular aging throughout their study and do not explore the effects of ybr238c deletion on RLS. This does not diminish their conclusions, but given the importance of this phenotype in their selection criteria, it is surprising that the authors did not choose to test both types of aging throughout their study.

Nonetheless, the authors demonstrate that deletion of ybr238c increases CLS across multiple yeast strains and through multiple assays. The authors also test the effects of YBR238C overexpression on lifespan and find the opposite effect, with overexpression yeast showing decreased survival relative to wild-type cells, consistent with "accelerated aging" as the authors propose. The authors also note that ybr238c has a paralog, rmd9, whose deletion decreases CLS and seems to be epistatic to ybr238c, as a double ybr238c/rmd9 mutant has decreased CLS relative to a wild-type strain.

Collectively, the data presented by the authors convincingly demonstrate that ybr238c influences lifespan in a manner that is distinct from (and likely opposite to) rmd9. However, the authors then link the increased CLS in Δybr238c yeast to mitochondrial function using only a handful of assays that do not directly test mitochondrial function. These include total cellular ATP levels, levels of reactive oxygen species, and the transcript levels of select nuclear-encoded mitochondrial genes. Yeast is well established to generate ATP through non-mitochondrial pathways such as glycolysis in fermentive conditions. While it is possible that the ATP levels assayed in the manuscript were tested in stationary phase, which would more likely reflect "mitochondrial function," the methods nor the figure legends contain these details, which are critical for the interpretation of these data. Similarly, ROS can be generated through non-mitochondrial pathways, and the transcription of nuclear-encoded mitochondrial genes is an indirect measure of mitochondrial function at best. Thus, the authors' proposed connection of ybr238c to mitochondrial function is correlative and should be substantiated with assays that more closely align with organellar function, such as respirometry or assaying the activity of oxidiative phosphorylation complexes. Finally, the authors attempt to tie the phenotypes of mitochondrial dysfunction caused by the deletion of ybr238c to TORC1 signaling, as the gene is influenced by rapamycin. However, the presentation of the data, such as reporting ATP levels as relative percentages or failing to perform appropriate statistical comparisons between conditions in which the authors derive conclusions, renders the data difficult to interpret. As such, this manuscript establishes that ybr238c is rapamycin responsive and influences CLS, but its influence on mitochondrial activity and ties to TORC1 signaling remain speculative.

We would like to express our gratitude to Reviewer #2 for the thoughtful feedback on our manuscript. We have carefully considered your comments and have made comprehensive revisions to address the concerns raised.

We appreciate the suggestion to investigate the role of YBR238C in replicative lifespan (RLS). However, we want to bring to your attention that four previous studies (references 7, 39, 40, and 41) have already identified the involvement of YBR238C in the RLS phenotype. Given the existing body of literature on this aspect, we chose not to duplicate these efforts in our study.

Instead, we focused our efforts on validating the role of YBR238C in chronological lifespan (CLS) phenotype, a finding reported in only one genome-wide study (reference 38). To enhance the comprehensiveness of our study, we performed analyses on different phenotypes, including mitochondria activity and oxidative stress, under both logarithmic-phase (condition for RLS) and stationary phase (condition for CLS). We now clearly indicate the logarithmic-phase/stationary phase conditions in the figure legends of the manuscript, specifying whether the conditions are relevant to RLS or CLS. Additional results of the new experiments have been included in the revised manuscript as supplementary figures (S3E-S3I).

To address concerns about the indirect nature of our mitochondrial function assays, we have performed relative mitochondria content (S3F), quantification of ROS levels from fermentative to stationary phase conditions (S3G), and assessment in respiratory glycerol medium (S3H), which provides a more direct insight into mitochondrial biology. Additionally, we have investigated the resistance of ybr238c∆ cells to H2O2 toxicity and found them to be more resistant compared to wild-type cells.

We believe these revisions strengthen the scientific rigor and clarity of our study. We sincerely appreciate the guidance from Reviewer #2, and we hope these modifications address the concerns raised effectively.

Reviewer #3 (Public Review):

Summary: The study by Alfatah et al. presented a role for YBR238C in mediating lifespan through improved mitochondrial function in a TOR1-dependent metabolic pathway. The authors used a dataset comparison approach to identify genes positively modulating yeast chronological (CLS) and Replicative (RLS) lifespan when deleted, and their expression is reduced under Rapamycin treatment condition. This approach revealed an unknown, mitochondria-localized yeast gene YBR238C, and through mechanistic studies, they identified its paralogous gene RMD9 regulating lifespan in an antagonistic effect.

Strengths:

Findings have valuable implications for understanding the YBR238C-mediated, mitochondrial-dependent yeast lifespan regulation, and the interplay between two paralogous genes in the regulation of mitochondrial function represents an inserting case for gene evolution.

Weaknesses:

Overall, the implication/findings of this study are restricted only to the yeast model since these two genes do not have any homology in higher eukaryotes. The primary methods must be carefully designed by considering two different metabolic states: respiration-associated with CLS and fermentation-associated with RLS in a single comparative approach. Yeast CLS and RLS are two completely different processes. It is already known that most gene-regulating CLS is not associated with RLS or vice versa. The method section is poorly written and missing important information. The experimental approaches are poorly designed, and variability across the datasets (e.g., media condition "YPD," "SC" etc.) and their experimental conditions are not well described/considered; thus, presented data are not conclusive, which decreases the overall rigor of the study.

We sincerely appreciate your thorough review of our manuscript and your insightful comments. We acknowledge the limitation of our study being yeast-specific due to the absence of homologous genes in higher eukaryotes. However, we would like to highlight the significance of our findings in revealing a feedback loop between mitochondrial function and TORC1 signaling (TORC1-Mitochondria-TORC1 or TOMITO signaling process) in cellular lifespan regulation.

Our interpretation of the experimental results is grounded in recent literature. Two studies (references 62 and 63) support our findings by demonstrating TORC1 activation after mitochondrial electron transport chain dysfunction and the delay in brain pathology progression upon TORC1 inhibition, respectively. These studies, discussed in our manuscript, reinforce the relevance of our work in a broader biological context.

We recognize the importance of carefully designing our primary methods to account for the different metabolic states associated with cellular processes, such as respiration in cellular lifespan (CLS) and fermentation in replicative lifespan (RLS). We want to bring to your attention that four previous studies (references 7, 39, 40, and 41) have already identified the involvement of YBR238C in the RLS phenotype. To avoid duplicating these efforts, we have chosen not to reiterate these findings in our study. However, we have clarified the logarithmic-phase/stationary phase conditions in the figure legends, specifying their metabolic states relevance to RLS or CLS. Additionally, we have included new supplementary figures (S3E-S3I) to provide further details on the new experiments conducted.

We appreciate your feedback regarding the clarity and completeness of our method section. In the revised manuscript, we have invested additional effort to enhance the clarity of the method section, providing a more detailed account of the experimental procedures, including the missing information you identified.

We believe these revisions strengthen the scientific rigor and clarity of our study. We sincerely appreciate the guidance from Reviewer #3, and we hope these modifications address the concerns raised effectively.

Reviewer #1 (Recommendations For The Authors):

Thank you for your detailed review and valuable recommendations. We have carefully addressed each of your comments in the revised manuscript. The specific changes made include:

(1) "TORC1 positively regulates aging, and its inhibition increases lifespan in various eukaryotic organisms including yeast and mammalian 13,26,27,29,30." Here I would suggest replacing "mammalian" with "mammals".

We have amended the sentence as recommended.

(2) "Next, we experimentally tested whether the transcriptome longevity signatures are associated with enhanced mitochondrial metabolism, whether the cellular energy level has gone up and cellular stress responses are induced with a switch to oxidative metabolism 47,48." Here I would replace "transcriptome longevity signatures is" with "transcriptome longevity signatures are".

We have amended the sentence as recommended.

(3) "Thus, HAP4-independent mechanism does exist through which YBR238C also affects cellular aging (Figure 3I)." I would replace "Thus, HAP4-independent" with "Thus, a HAP4-independent".

We have amended the sentence as recommended.

(4) "We examined other mitochondrial dysfunctional conditions to confirm that suppressive effect of rapamycin is not only specific to YBR238C-OE." I would change "that suppressive effect" to "that the suppressive effect".

We have amended the sentence as recommended.

(5) "Understanding the mechanism of aging will also require to understand the role of many genes of yet unknown function as YBR238C at the beginning of this work." I would switch "require to understand" to "require understanding".

We have amended the sentence as recommended.

(6) "The gene lists that modulate cellular lifespan in aging model organism yeast Saccharomyces cerevisiae were extracted from database SGD 22 and GenAge 23 (as of 8th November 2022)" "yeast" should not be italicized.

Corrected.

(7) Figure 1, panels C and D, ybr238c should be italicized.

Corrected.

(8) Figure 2B, top left-most (oxidative phosphorylation) network. I might consider repositioning some labels to make them more readable if possible.

Thank you for your feedback. The figure labels in Figure 2B are default from Metascape analysis, so repositioning isn't feasible. However, we have indicated in the figure legends that the full set of genes for functional enrichment analysis and the MCODE complex is available in Additional File 3.

(9) Figure 4E, rmd9, pet100, and cox6 should be italicized.

Corrected.

(10) Figure 5C, rmd9 and rmd9 ybr238c should be italicized. Corrected.

Reviewer #2 (Recommendations For The Authors):

Thank you for your detailed review and valuable recommendations. We have carefully addressed each of your comments in the revised manuscript. The specific changes made include:

(1) The presentation of data as heatmaps (Figures 1F, 3D, 4C, 4G, 5B, 5H, 5L, 6K) obfuscates the quantitative nature of the data. These data would be much stronger if presented as bar graphs with appropriate statistical analysis. If the authors prefer the visual of the heat map, there should be some statistical analysis performed to accompany these figures. This is particularly important for Figure 3D, in which the authors state "We found that HAP4 deletion significantly decrease the ETC complex I-V genes' expression" (bottom of page 8). As no statistical analyses were performed, the authors should refrain from using such language as it is unsupported by the data as analyzed.

Thank you for your insightful comments and suggestions regarding the presentation of our data. We appreciate the attention you have given to Figures 1F, 3D, 4C, 4G, 5B, 5H, 5L, and 6K.

In response to your feedback, we have carefully re-evaluated our approach. Considering the large volume of data associated with our lifespan analysis at different time points, we initially chose to visualize it using heatmaps to comprehensively capture the complexity of the results. However, we have now incorporated quantification information into the heatmaps.

For Figure 3D, which addresses the impact of HAP4 deletion on the expression of ETC complex I-V genes, we have replaced the heatmap with a bar graph. This modification allows for a clearer representation of the quantitative nature of the data. Moreover, we have conducted thorough statistical analyses comparing data between ybr238c∆ and ybr238c∆ hap4∆ to support the statements made in the text. The results of these analyses are now included in the revised figure. Moreover, we also replaced the Figure 6K heatmap with a bar graph.

We believe that these changes enhance the interpretability and robustness of our findings. We are grateful for your guidance, and we are confident that these adjustments will strengthen the overall quality of our manuscript.

(2) The presentation of ATP data, given its importance in supporting the core conclusions of this manuscript, is poor. The conditions under which yeast was collected are not reported, making these data impossible to interpret; total cellular ATP levels would be significantly altered and influenced by separate pathways in fermentive versus stationary phases. Minimally, the authors should describe the conditions of yeast growth (e.g., age, culture media) in which these measurements were made. The presentation of relative ATP percentages is problematic, particularly with measurements that deviate so far from wild-type ATP levels in conditions such as those in Figure 6A, in which the authors report that rapamycin induces a 1200% increase in cellular ATP. Previous papers have established that ATP levels in yeast hover around 4 mM and are stable through the cell cycle and across nutrient conditions (PMID: 30858198, 35438635). Given this, the reported ATP levels would be expected to be near 48 mM, which is strongly outside of the typically accepted values of 1-10 mM for this metabolite. Without understanding the contexts in which these measurements are made, as well as the absolute values for these measurements (which would be easily achievable through the use of a standard curve of ATP), these data are uninterpretable. Furthermore, it seems unlikely that yeast would be able to accommodate shifts of ATP levels that span an order of magnitude without dire cellular consequences, particularly during rapamycin treatment.

We appreciate the valuable feedback from the reviewer regarding the importance of providing detailed information on yeast growth conditions for interpreting ATP data. In response to this suggestion, we have enhanced the figure legends associated with the relevant figures to include a comprehensive description of the yeast growth conditions. This now specifies the age of the culture, culture media composition, and other pertinent parameters.

In addressing the concern raised about the rapamycin-induced ATP increase, we have carefully re-examined our experimental procedures. We performed additional experiments and confirmed the consistency of our findings in logarithmic-treated cultures. The results remain in alignment with our initial observations, reinforcing the reliability and reproducibility of our data.

(3) As stated above, the inference of mitochondrial function from cellular ATP levels, cellular ROS levels, and gene expression of a handful of nuclear-encoded genes is not sound. The authors should include further experimentation as evidence of mitochondrial functionality, such as respirometry or metabolic flux experiments.

Thank you for your constructive feedback on our manuscript. We appreciate your careful consideration of our work. In response to your concerns regarding the indirect nature of our mitochondrial function assays, we have implemented the following changes: We have incorporated additional assays to provide a more direct insight into mitochondrial biology. Specifically, we performed relative mitochondria content analysis (S3F) and quantified ROS levels under fermentative to stationary phase conditions (S3G). These assays offer a more direct and comprehensive assessment of mitochondrial function. Furthermore, we conducted experiments in respiratory glycerol medium (S3H) to complement our previous findings.

To further support our claims, we investigated the resistance of ybr238c∆ cells to H2O2 toxicity. Our results demonstrate that these cells exhibit increased resistance compared to wild-type cells. This additional evidence strengthens the link between mitochondrial function and cellular response to oxidative stress.

We believe these adjustments address your concerns and significantly enhance the robustness of our study. We hope you find these modifications satisfactory. We are grateful for your valuable input, which has undoubtedly improved the clarity and reliability of our findings.

(4) Multiple gene expression analyses are performed on n=2 measurements, and this should be bolstered by further replicates. Many bar graphs do not have accompanying statistics; these should be added. Some statistical tests are performed across inappropriate comparisons, such as Figure 3G, in which expression levels of mitochondrial genes in both deletion and overexpression strains should be compared to a wild-type control rather than to each other.

Thank you for your thorough review and constructive feedback on our manuscript. We appreciate your careful examination of our work. In response to your comments, we have made the following revisions to address your concerns: The multiple gene expression analysis in our study focused specifically on ETC genes. It is important to note that ETC genes themselves represent multiple replicates within the ybr238c deletion and overexpression cells, as illustrated in Figures 4D, 4G, and 6B.

We acknowledge and appreciate your observation regarding Figure 3G. To address this concern, we have revised the statistical comparisons. The expression levels of mitochondrial genes in the overexpression strain are now appropriately compared to a wild-type control. This correction has been applied in the figure that correctly corresponds to text in the manuscript.

(5) Figure 2B is uninterpretable as it stands, as most gene symbols are obscured.

We appreciate the reviewer's attention to Figure 2B and the feedback provided. Regarding the gene labels in Figure 2B, we would like to clarify that these labels are default outputs from the Metascape analysis, and unfortunately, repositioning them within the current figure layout isn't feasible without compromising the integrity of the information.

However, we have taken the reviewer's concern seriously and have made efforts to address the interpretability issue. To provide readers with access to the full set of genes for functional enrichment analysis and the MCODE complex, we have included this information in Additional File 3. The figure legends have been updated accordingly to guide readers to refer to Additional File 3 for a more detailed examination of the gene symbols and their annotations.

We hope that this solution addresses the concern raised by the reviewer.

(6) The conclusions to be drawn from Figure 3A are not clear, and this figure is cited only once in the text along with two other figures (page 8).

Thank you for your valuable feedback. We have carefully considered your comments and made revisions to improve the clarity of the conclusions drawn from Figure 3A.

(7) Figure 6K reports a range of 100-200% cell survival - how does a cell have 200% survival? Isn't survival binary (i.e., you survive or you are dead)? Perhaps this is meant to be relative to another condition; this should be more clearly stated in the figure, or the axis should be normalized to a maximum of 100% survival.

Thank you for your guidance and valuable feedback. Based on your recommendation, we have made significant changes to Figure 6K in the revised manuscript. Specifically, we replaced the heatmap with a bar graph to enhance clarity. Additionally, we would like to highlight that cell survival of combined treated cells is measured relative to the control treatment, which is considered 100% survival. This aims to provide a more accurate and comprehensible representation of the data. We believe these modifications contribute to a clearer presentation of our findings.

(8) The authors state that "TORC1 inhibition in yeast and human cells with mitochondrial dysfunction suppresses their accelerated aging." No studies of aging were done in human cells; survival in response to mitochondrial toxins does not reveal aging phenotypes. To state such is a substantial overstatement and should be amended to perhaps "cellular survival" rather than directly linked to aging.

We appreciate the careful review of our manuscript and the constructive feedback provided by the reviewer. In response to the concern raised regarding the statement about TORC1 inhibition and accelerated aging in human cells, we have revised the relevant passage as follows: "In turn, TORC1 inhibition in yeast and human cells with mitochondrial dysfunction enhances their cellular survival." We believe that this modification accurately reflects the outcomes of our experiments and addresses the concern raised by the reviewer. We would like to express our gratitude for the valuable feedback, which has contributed to the improvement of our manuscript. Thank you for your thoughtful consideration.

Reviewer #3 (Recommendations For The Authors):

Thank you for your detailed review and valuable recommendations. We have carefully addressed each of your comments in the revised manuscript. The specific changes made include:

The authors should have attempted to fully characterize the RLS and CLS phenotype of strains lacking the YBR238C and RMD9 gene, the single most important gene identified in this study. Before further characterization, its association with aging must be tested to replicate findings from the literature. Although Figure 3 shows partially characterized CLS in SC medium, different media conditions could be tested, and the full spectrum of CLS lifespan curves should be represented. RLS phenotypes of these cells were not analyzed throughout the study.

We appreciate the suggestion to investigate the role of YBR238C in both Replicative Lifespan (RLS) and Chronological Lifespan (CLS). However, it's essential to note that the involvement of YBR238C in the RLS phenotype has been previously documented in four studies (references 7, 39, 40, and 41). Considering the established literature on this matter, we chose not to duplicate these efforts in our study.

Our primary focus was on confirming the role of YBR238C in the chronological lifespan (CLS) phenotype, as indicated by a genome-wide study (reference 43). Accordingly, we also conducted an analysis of the role of RMD9 in CLS. The methods and figure legends explicitly state that CLS experiments for prototrophic CEN.PK113-7D strains were conducted in synthetic defined (SD) medium containing 6.7 g/L yeast nitrogen base with ammonium sulfate without amino acids and 2% glucose. For auxotrophic BY4743 strains, SD medium was supplemented with histidine (40 mg/L), leucine (160 mg/L), and uracil (40 mg/L).

It is important to clarify that SC medium was not used for CLS analysis. Instead, we employed SD medium, recommended for CLS analysis (reference 15; PMID: 22768836). The CLS experiments were conducted using three different methods, providing a comprehensive representation of the entire CLS lifespan (Figures 1C, 1D, 1E, and 1F).

While we did not present the Replicative Lifespan (RLS) phenotype explicitly, we performed experiments such as mitochondrial activity and ROS production under both CLS and RLS conditions. These additional analyses contribute valuable insights into the broader implications of YBR238C and RMD9 on cellular function.

We believe that these clarifications and the inclusion of additional experimental details enhance the robustness and validity of our findings. We hope these explanations address the concerns raised by the reviewer and contribute to the overall improvement of our manuscript.

In addition, authors include RNAseq data from Rapamycin-treated cells to identify differentially expressed genes. Notably, genes with decreased expression were used to compare KO strains' lifespan phenotype. Additional RNAseq analyses were performed on individual KO cells. The methodology section needs to be better written with information on which media and metabolic state that these cells are collected after treatment with rapamycin. If the cells are collected during logarithmic growth, the data can be compared with RLS aging gene sets only. A separate experiment has to be performed on stationary cells (respiratory) to collect RNAseq data after rapamycin treatment, then can be compared to the CLS aging gene set.

Thank you for your insightful comments and considerations regarding our methodology for obtaining Rapamycin response genes (RRGs). We appreciate the opportunity to address your concerns and provide further clarification on our experimental approach.

As mentioned in our manuscript, we obtained RRGs by treating logarithmic cells with 50 nM Rapamycin for 1 hour, and the details have been included in supplementary Figure S1C legends. Our primary objective was to compare these RRGs with agingassociated genes that modulate both Replicative Lifespan (RLS) and Chronological Lifespan (CLS). We acknowledge the significance of this comparison and believe that our approach, treating logarithmic cells, is suitable for achieving this goal.

It is important to note that the use of a higher concentration of Rapamycin for treatment renders the cells less efficient in terms of growth, resulting in a very low optical density (OD) at 72 hours, as illustrated in Figure 6H. Unfortunately, due to this limitation in growth efficiency, obtaining Rapamycin response genes at the stationary phase was not feasible in our experimental setup.

As the experimental conditions vary among the reports and the gene expression signature significantly changes under different metabolic conditions, the media condition that samples are collected for RNAseq analyses should match the media condition that the lifespans of those KO strains are tested. However, more information needs to be detailed on these methodologies. For example, the transcriptomic signature of the YBR238C KO strain should be done under both fermentative and respiratory conditions to understand the true gene expression signature associated with CLS and RLS. Throughout the manuscript, these two metabolic conditions and associated lifespan types (CLS vs. RLS) are not differentiated and treated as the same, probably causing the biggest confounding effect that resulted in the identification of a single yeast-specific gene.

We obtained the transcriptomic signature of the YBR238C KO strain from logarithmic phase cultures. This consistency was maintained to align with the Rapamycin Response Genes (RRGs) obtained from logarithmic cells treated with rapamycin. Detailed methodology and metabolic status information is provided in the method section and relevant figure legends.

To broaden the scope of our study, we conducted analyses on various phenotypes, including mitochondrial activity and oxidative stress, under both logarithmic phase (relevant to Replicative Lifespan, RLS) and stationary phase (relevant to Chronological Lifespan, CLS). We have now explicitly indicated the logarithmic phase/stationary phase conditions in the figure legends of the manuscript, specifying their relevance to RLS or CLS.

Results from these additional experiments have been incorporated into the revised manuscript as supplementary figures (S3E-S3I). We believe that these clarifications and the inclusion of additional experimental details enhance the robustness and validity of our findings. We trust that these explanations effectively address the concerns raised by the reviewer and contribute to the overall improvement of our manuscript.

YBR238C gene KO effect on mitochondrial function missing comprehensive characterization. Whether the improved mito function caused by increased mtDNA copy number and/or increased mitochondrial number could be easily tested by analyzing normalizing RNAseq reads from mtDNA genes to reads from nucDNA genes. Data could be further combined with western blot specific to mito membrane proteins to analyze mito copy number.

Thank you for your insightful comments and suggestions. Following your recommendation, we conducted an assessment of relative mitochondrial content (see Figure S3F) and observed significantly higher mtDNA content in the ybr238c∆ compared to the wild type (see Figure S3F). Additionally, we have incorporated the methodology for mitochondrial DNA copy number analysis in the methods section.

The two paralogous gene interaction is an interesting observation. However, in yeast, it is known that deletion of one of the paralogous genes causes copy number amplification of the certain chromosome that the other paralogous gene is located, causing aneuploid chromosome. Many of the observed phenotypes can be associated with increased chromosome copy number and should be carefully tested. However, the authors did not consider this important point. Simply, using RNA seq data normalized read/per chromosome could be plotted to analyze the karyotype of YBR238C and RMD9 KO cells.

We appreciate your thoughtful consideration of our work and the suggestion to investigate chromosome copy number variations. While we did not directly test the chromosome copy, we want to highlight that our study extensively explores the impact of YBR238C on cellular lifespan through an RMD9-dependent mechanism (Figure 5). Deletion of YBR238C increases, whereas overexpression of YBR238C decreases the expression of its paralog, RMD9 (Figure 5F). Furthermore, this phenotype is associated with the lifespan of YBR238C-deleted and overexpressed cells. In our study, we have thoroughly investigated this aspect.

Author Response

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

We appreciate the care and the detail shown by the Reviewers. Their comments have made our article more focused and more accessible to a general audience.

We would like to begin with a comment about the last sentence of the “eLife assessment”. The evolution of metamorphosis in insects was a major triumph in animal evolution that subsequently impacted almost every aspect of plant and animal evolution in the terrestrial and freshwater aquatic biospheres. Unlike the metamorphoses of most other groups, whose evolutions are lost in time, insect evolution arose relatively recently (~400 mya) and insect orders have branched off at various points in this evolution and have persisted to modern times. Although these “relic” groups also have undergone millions of years of evolution and specialization, they still provide us with windows into how this progression may have come about. The study of these groups provides a unique opportunity to explore the mechanisms that underlie major life history shifts and should be of interest to anyone interested in evolution – not just entomologists.

Reviewer #1 (Public Review):

Summary:

This paper provides strong evidence for the roles of JH in an ametabolous insect species. In particular, it demonstrates that:

• JH shifts embryogenesis from a growth mode to a differentiation mode and is responsible for terminal differentiation during embryogenesis. This, and other JH roles, are first suggested as correlations, based on the timing of JH peaks, but then experimentally demonstrated using JH antagonists and rescue thereof with JH mimic. This is a robust approach and the experimental results are very convincing.

• JH redirects ecdysone-induced molting to direct formation of a more mature cuticle

• Kr-h1 is downstream of JH in Thermobia, as it is in other insects, and is a likely mediator of many JH effects

• The results support the proposed model that an ancestral role of JH in promoting and maintaining differentiation was coopted during insect radiations to drive the evolution of metamorphosis. However, alternate evolutionary scenarios should also be considered.

Strengths:

Overall, this is a beautiful, in-depth student. The paper is well-written and clear. The background places the work in a broad context and shows its importance in understanding fundamental questions about insect biology. The researchers are leaders in the field, and a strength of this manuscript is their use of a variety of different approaches (enzymatic assays, gene expression, agonists & antagonists, analysis of morphology using different types of microscopy and detection, and more) to attack their research questions. The experimental data is clearly presented and carefully executed with appropriate controls and attention to detail. The 'multi-pronged' approach provides support for the conclusions from different angles, strengthening conclusions. In sum, the data presented are convincing and the conclusions about experimental outcomes are well-justified based on the results obtained.

Weaknesses:

This paper provides more detail than is likely needed for readers outside the field but also provides sufficient depth for those in the field. This is both a strength and a weakness. I would suggest the authors shorten some aspects of their text to make it more accessible to a broader audience. In particular, the discussion is very long and accompanied by two model figures. The discussion could be tightened up and much of the text used for a separate review article (perhaps along with Figure 11) that would bring more attention to the proposed evolution of JH roles.

We appreciate the comments about the strengths and weaknesses of the paper. To deal with the weaknesses, we have condensed some of the Results to make them less cumbersome and the Discussion has been completely revised, keeping a sharp focus on the actions of JH in Thermobia embryos and how these actions relate to the status quo functions of JH in insects with metamorphosis. As part of the revision of the Discussion, we have replaced Figures 10 and 11.

Reviewer #1 (Recommendations For The Authors):

In keeping with my public review, this paper is very strong and I have very few suggestions for improvement. They are:

(1) Thermobia are extant insects and are not ancestral insects. It is likely that they retain features found in an insect ancestor. However, these insects have been evolving for a very long time, and for any one feature, many changes may have occurred, both gain and loss of gene function and morphology. Further, even for morphological features present in an extant species that are the same as an ancestor, genetic pathways regulating this feature may have changed over time (see for examples papers from the Haag and Pick labs). Although I realize this is a small, possibly almost semantic point, I feel it is important to be precise here. For example, in the title, "before" is speculative as there could have been a different role in the ancestor with the role in embryogenesis arising in lineages leading to Thermobia; similarly in the abstract, "this ancestral role of JH' is an overstatement since we cannot actually measure the ancestral role.

Since the title has already been cited in a Perspectives review, we decided to keep the title as is.

(2) I don't understand the results in Met and myo in Fig. 3B. Perhaps include them in the explanation of Fig.3 and not after the description of Fig. 4 and explain them in more detail (or perhaps not include them at all?). I don't really understand the statistical analysis of these panels either.

We have revised the figure legends to explain the statistics.

(3) Another point regarding language - talking about the embryo being "able" to go through a developmental stage implies decision-making. I would suggest dropping that wording (e.g, in the description of Fig. 5C). Similarly, in explaining Fig. 6B, it would be more correct to say "JH treatment no longer inhibited" than as written "could no longer inhibit" (implying 'no matter how hard it tried, it still couldn't do it')

We have removed the “can’t” wording. Figure 6 has been revised

Reviewer #2 (Public Review):

The authors have studied in detail the embryogenesis of the ametabolan insect Thermobia domestica. They have also measured the levels of the two most important hormones in insect development: juvenile hormone (JH) and ecdysteroids. The work then focuses on JH, whose occurrence concentrates in the final part (between 70 and 100%) of embryo development. Then, the authors used a precocene compound (7-ethoxyprecocene, or 7EP) to destroy the JH producing tissues in the embryo of the firebrat T. domestica, which allowed to unveil that this hormone is critically involved in the last steps of embryogenesis. The 7EP-treated embryos failed to resorb the extraembryonic fluid and did not hatch. More detailed observations showed that processes like the maturational growth of the eye, the lengthening of the foregut and posterior displacement of the midgut, and the detachment of the E2 cuticle, were impaired after the 7EP treatment. Importantly, a treatment with a JH mimic subsequent to the 7EP treatment restored the correct maturation of both the eye and the gut. It is worth noting that the timing of JH mimic application was essential for correcting the defects triggered by the treatment with 7EP.

This is a relevant result in itself since the role of JH in insect embryogenesis is a controversial topic. It seems to have an important role in hemimetabolan embryogenesis, but not so much in holometabolans. Intriguingly, it appears important for hatching, an observation made in hemimetabolan and in holometabolan embryos. Knowing that this role was already present in ametabolans is relevant from an evolutionary point of view, and knowing exactly why embryos do not hatch in the absence of JH, is relevant from the point of view of developmental biology.

The unique and intriguing aspect of juvenile hormone is its status quo action in the control of metamorphosis. Our reason for dealing with an insect group that branched off from the line of insects that eventually evolved metamorphosis, was to gain insight into the ancestral functions of this hormone. Our data from Thermobia as well as that from grasshoppers and crickets indicate that the developmental actions of JH were originally confined to embryogenesis where it promoted the terminal differentiation of the embryo. Its actions in promoting differentiation also included suppressing morphogenesis. This latter function was not pronounced during embryogenesis because JH only appeared after morphogenesis was essentially completed. However, it was a preadaptation that proved useful in more derived insects that delayed aspects of morphogenesis into the postembryonic realm. JH was then used postembryonically to inhibit morphogenesis until late in juvenile growth when JH disappears, and this inhibition is released.

Then, the authors describe a series of experiments applying the JH mimic in early embryogenesis, before the natural peak of JH occurs, and its effects on embryo development. Observations were made under different doses of JHm, and under different temporal windows of treatment. Higher doses triggered more severe effects, as expected, and different windows of application produced different effects. The most used combination was 1 ng JHm applied 1.5 days AEL, checking the effects 3 days later. Of note, 1.5 days AEL is about 15% embryonic development, whereas the natural peak of JH occurs around 85% embryonic development. In general, the ectopic application of JHm triggered a diversity of effects, generally leading to an arrest of development. Intriguingly, however, a number of embryos treated with 1 ng of JHm at 1.5 days AEL showed a precocious formation of myofibrils in the longitudinal muscles. Also, a number of embryos treated in the same way showed enhanced chitin deposition in the E1 procuticle and showed an advancement of at least a day in the deposition of the E2 cuticle.

While the experiments and observations are done with great care and are very exhaustive, I am not sure that the results reveal genuine JH functions. The effects triggered by a significant pulse of ectopic JHm when the embryo is 15% of the development will depend on the context: the transcriptome existing at that time, especially the cocktail of transcription factors. This explains why different application times produce different effects. This also explains why the timing of JHm application was essential for correcting the effects of 7EP treatment. In this reasoning, we must consider that the context at 85% development, when the JH peaks in natural conditions and plays its genuine functions, must be very different from the context at 15% development, when the JHm was applied in most of the experiments. In summary, I believe that the observations after the application of JHm reveal effects of the ectopic JHm, but not necessarily functions of the JH. If so, then the subsequent inferences made from the premise that these ectopic treatments with JHm revealed JH functions are uncertain and should be interpreted with caution.

We disagree with the reviewer. An analogous situation would be in exploring gene function in which both gain-of-function and loss-of-function experiments often provide complementary insights into how a gene functions. We see JH effects only when its receptor, Met, is present and JH can induce its main effector protein, Kr-h1. The latter gives us confidence that we are looking at bona fide JH effects. We have also kept in mind, though, that the nature of the responding tissues is changing through time. Nevertheless, we see a consistent pattern of responses in the embryo and these can be related to its postembryonic effects in metamorphic insects.

Those inferences affect not only the "JH and the progressive nature of embryonic molts" section, but also, the "Modifications in JH function during the evolution of hemimetabolous and holometabolous life histories" section, and the entire "Discussion". In addition to inferences built on uncertain functions, the sections mentioned, especially the Discussion, I think suffer from too many poorly justified speculations. I love speculation in science, it is necessary and fruitful. But it must be practiced within limits of reasonableness, especially when expressed in a formal journal.

We have tried to dial back the speculation.

Finally, In the section "Modifications in JH function during the evolution of hemimetabolous and holometabolous life", it is not clear the bridge that connects the observations on the embryo of Thermobia and the evolution of modified life cycles, hemimetabolan and holometabolan.

Our Figure 12 should put this into perspective.

Reviewer #2 (Recommendations For The Authors):

Main points

(1) Please, reduce the level of overinterpretation of ectopic treatment experiments with JHm, since the resulting observations represent effects, but not necessarily functions of JH.

We have revised this section to indicate that the “effects” of ectopic treatments provide insights into the function of JH. Using a genetic analogy, both “loss-of-function” and “gain-of-function” experiments provide insights into a given gene. (see response to Public Comments)

(2) Especially in the sections "JH and the progressive nature of embryonic molts" and "Modifications in JH function during the evolution of hemimetabolous and holometabolous life histories", and the entire "Discussion", please keep the level of speculation within reasonable limits, avoiding especially the inference of conclusions on the basis of speculation, itself based on previous speculation.

We have toned down some of the speculation and provided reasons why it is worth suggesting.

(3) Please revisit the argued roles of myoglianin in the story, in light of its effects as an inhibitor of JH production, repressing the expression of JHAMT, as has been reliably demonstrated in hemimetabolan species (DOI: 10.1073/pnas.1600612113 and DOI: 10.1096/ fj.201801511R).

Our appreciation to the reviewer. We are more explicit about the relationship between JH and myo.

Minor points

(4) Please keep the consistency of the scientific binomial nomenclature for the species mentioned. For example, read "Manduca sexta" (in italics) at the first mention, and then "M. sexta" (in italics) in successive mentions (instead of reading "Manduca" on page 17, and then "Manduca sexta" on page 18, for example). The same for "Drosophila" ("Drosophila melanogaster" first, and then "D. melanogaster"), "Thermobia" ("Thermobia domestica" first, and then "T. domestica"), etc. In the figure legends, I recommend using the complete name: Thermobia domestica, in the main heading.

Where there is no possibility of confusion, we intend to use Thermobia, rather than T. domestica, etc. We think that it is easier for a non-specialist to read and it is commonly done in endocrine papers.

(5) There is no purpose in evolution and biological processes. Thus, I suggest avoiding expressions that have a teleological aftertaste. For example (capitals are mine), on p. 3 "appears to have been extended into postembryonic life where it acts TO antagonize morphogenic and allow the maintenance of a juvenile state".

We have tried to avoid teleological wording.

(6) The title "The embryonic role of juvenile hormone in the firebrat, Thermobia domestica, reveals its function before its involvement in metamorphosis" contains a redundancy ("role" and "function"), and an apparent obviousness ("before its involvement in metamorphosis"). I suggest a more straightforward title. Something like "Juvenile hormone plays developmental functions in the embryo of the firebrat Thermobia domestica, which predate its status quo action in metamorphosis".

As noted above, we are retaining the title since it has already been cited.

(7) Page 2. "The transition from larva to adult then occurred through a transitional stage, the pupa, thereby providing the three-part life history diagnostic of the "complete metamorphosis" exhibited by holometabolous insects (reviews: Jindra, 2019; Truman & Riddiford, 2002, 2019)". I suggest adding the reference ISBN: 9780128130209 9 7 8 - 0 - 1 2 - 8 1 3 0 2 0 - 9, as the most comprehensive and recent review on complete metamorphosis.

Done

(8) Page 3. "These severe developmental effects suggest that the developmental role of JH in insects was initially CONFINED to the embryonic domain" (capitals are mine). This appears contradictory with the observations of Watson, 1967, on the relationships between the apparition of scales and JH, mentioned shortly before by the authors.

This is explained in the Discussion. Although JH can suppress scale appearance in the J4 stage, we have not been able to show that scales appearance is caused by changes in the juvenile JH titer.

(9) Page 4. "we measured JH III levels during Thermobia embryogenesis at daily intervals starting at 5 d AEL". Why not before, like in the case of ecdysteroids? The authors might perhaps argue that the levels of Kr-h1 expression are consistently low from the very beginning, according to Fernandez-Nicolas et al, 2022 (reference cited later in the manuscript).

(10) Page 4. "Ecdysteroid titers through embryogenesis and the early juvenile instars were measured using the enzyme immunoassay method (Porcheron et al., 1989) that is optimized for detecting 20-hydroxyecdysone (20E)". The antibody generated by Porcheron (and now sold by Cayman) recognizes ecdysone and 20-hydroxyecdysone alike. But that's not relevant here. I would refer to "ecdysteroids" when mentioning measurements. Also in figure 2B (and "juvenile hormone III" without the formula, in Panel A, for harmonization). And I would not expand on specifications, like those at the beginning of page 5, or towards the end of page

We thank the reviewer for this important correction.

(12) ("the fact that we detected only a slight rise in ecdysteroids at this time (Fig 2B) is likely due to the assay that we used being designed to detect 20E rather than ecdysone").

Omitted.

(11) Page 5. "Low levels of Kr-h1 transcripts were present at 12 hr after egg deposition, but then were not detected until about 6 d AEL when JH-III first appeared". There is a very precise Kr-h1 pattern in Fernandez-Nicolas et al. 2023 (reference mentioned later in the manuscript).

(12) Page 5. "notably myoglianin (myo), have become prominent as agents that promote the competence and execution of metamorphosis in holometabolous and hemimetabolous insects (He et al., 2020; Awasaki et al., 2011)". See my note 3 above.

The myoglianin issue has been revised.

(13) Page 5. "a drug that suppresses JH production". Rather, "a drug that destroys the JH producing tissues". Why the way, do the authors know when the CA are formed in T. domestica embryo development?

We prefer to keep our original wording. There have been some cases in which precocene has blocked JH production but did not kill the CA cells. We do not have observations that show that 7EP kills the CA cells in Thermobia embryos.

(14) Page 5. "subsequent treatment with a JHm". I would say here that the JHm is pyriproxyfen, not on page 6 or page 7. Thus, to be consistent, after the first mention of "pyriproxyfen (JHm)" on page 5, I'd consistently use the abbreviation "JHm".

(15) Page 9. "Limb loss in such embryos was often STOCHASTIC, i.e., in a given embryo some limbs were completely lost while others were maintained in a reduced state" (capitals are mine). The meaning of "stochastic" is random, involving a random variable; it is a concept usually associated to probability theory and related fields. I suggest using the less specialized word "variable", since to ascertain that the values are really stochastic would require specific mathematical approaches.

We are still using stochastic because the loss is random.

(16) Page 10. "9E). Indeed, the JH treatment redirects the molt to be more like that to the J2 stage, rather than to the E2 (= J1) stage". Probably too assertive given the evidence available (see my points 1 and 2 above).

We do not see a problem with our conclusion. In response to the JHm treatment, the embryo produced a smooth, rather than a “pebbly” cuticle, failed to make the J1-specific egg tooth, and attempted to make cuticular lenses (a J2 feature). This ability of premature JH exposure to cause embryos to “skip” a stage is also seen in locusts (Truman & Riddiford, 1999) and crickets (Erezyilmaz et al., 2004). The JHm treatment resulted in the production of smooth cuticle, lack of a hatching tooth, and an attempt to make cuticular lenses.

(17) Page 11. "early JHM treatment", read "early JHm treatment".

Corrected

(18) Page 11. "likely. A target of JH, and likely Kr-h1, in Thermobia is myoglianin...". Please see my notes 1, 2, and especially 3, above.

This has been revised

(19) Page 13. "the locust, Locusta americana (Aboulafia-Baginshy et al.,1984)". Please read "the locust, Locusta migratoria (Aboulafia-Baginshy et al.,1984)".

Corrected

(20) Page 13 "Acheta domesticus" three times. The correct name now is "Acheta domestica", after harmonizing the declension of the specific name with the generic one. See additionally my note 4 above.

Acheta domesticus has been used in hundreds (thousands?) of papers since it was originally named by Linnaeus. We will continue to use it.

(21) Page 15, "(also called the vermiform larva (Bernays, 1971) redirects embryonic development to form an embryo with proportions, cuticular pigmentation, cuticular sculpturing and bristles characteristic of a nymph, while pronymph modifications, such as the cuticular surface sculpturing (Bernays, 1971)". The reference "Bernays, 1971" is indeed "Bergot et al., 1971".

There was a mistake in the references. The Bernays reference was omitted from the revised Discussion

(22) Page 16. "Since JH also induces Kr-h1 in embryos of many insects, including Thermobia". I'm not sure that this has been studied in many insects. In any case, any reference would be useful.

(23) Page 17. "Tribolium casteneum". Please read "Tribolium castaneum".

Changed

(24) Page 17. "...results in a permanent larva that continues to molt well after it has surpassed its critical weight (He et al., 2019)". The paper of He et al., 2019 is preceded by two key papers that previously demonstrate (and in hemimetabolan insects) that myoglianin is a determining factor in the preparation for metamorphosis: DOI: 10.1073/pnas.1600612113 and DOI: 10.1096/ fj.201801511R). See my note 3 above.

Corrected in revision

(25) Page 18. "These persisting embryonic primordia join the wing primordia in delaying their morphogenesis into postembryonic life". This reader does not understand this sentence.

Made clearer in the revision.

(26) Page 18. "is first possible in the commercial silkworm (Daimon et al., 2015)". Please mention the scientific Latin name of the species, Bombyx mori.

(27) Page 19. "The functioning of farnesol derivatives in growth versus differentiation control extends deep into the eukaryotes.../... this capacity was eventually exploited by the insects to provide the hormonal system that regulates their metamorphosis". This information appears quite out of place.

We have retained this point.

(28) Page 21. Heading "Hormones". I suggest using the heading "Bioactive compounds", as neither pyriproxyfen nor 7-ethoxyprecocene are hormones.

Done

(29) Page 29, legend of figure 1. "Photomicrographs" is somewhat redundant. The technical word is "micrographs". "Thermobia domestica" appears in the explanation of panel C, but this is not necessary, as the name appears in the main heading of the legend.

Done

(30) Page 30, legend of figure 2. Panel B, see my comment 10 above. Why embryonic age is expressed in % embryo development in panel C (and in days in panels A and B)?

All have been converted to days AEL

(31) Page 35, legend of figure 5. "Photomicrograph" see my note 28 above.

Done

(32) Page 40, figure 10. In panel A, the indication of the properties of JH is misleading. The arrow going to promoting differentiation and maturation is OK, but the repression sign that indicates suppression of morphogenetic growth and cell determination seems to suggest that JH has retroactive effects. In panel B, I suggest to label "Flies" instead of "Higher Diptera", which is an old-fashioned term. In any case, see my general comments 1 and 2, above, about speculation.

Figure has been completely revised

(33) Figure 11. See my general comments 1 and 2, above, about speculation.

Figure has been revised

Reviewer #3 (Public Review):

Summary:

In this manuscript, the authors use inhibitors and mimetics of juvenile hormone (JH) to demonstrate that JH has a key role in late embryonic development in Thermobia, specifically in gut and eye development but also resorption of the extraembryonic fluid and hatching. They then exogenously apply JH early in development (when it is not normally present) to examine the biological effects of JH at these stages. This causes a plethora of defects including developmental arrest, deposition of chitin, limb development, and enhanced muscle differentiation. The authors interpret these early effects on development as JH being important for the shift from morphogenetic growth to differentiation - a role that they speculate may have facilitated the evolution of metamorphosis (hemi- and holo-metaboly). This paper will be of interest to insect evo-devo researchers, particularly those with interests in the evolution of metamorphosis.

Strengths:

The experiments are generally conducted very well with appropriate controls and the authors have included a very detailed analysis of the phenotypes.

The manuscript significantly advances our understanding of Thermobia development and the role of JH in Thermobia development.

The authors interpret this data to present some hypotheses regarding the role of JH in the evolution of metamorphosis, some aspects of which can be addressed by future studies.

Weaknesses:

The results are based on using inhibitors and mimetics of JH and there was no attempt to discern immediate effects of JH from downstream effects. The authors show, for instance, that the transcription of myoglianin is responsive to JH levels, it would have been interesting to see if any of the phenotypic effects are due to myoglianin upregulation/suppression (using RNAi for example). These kinds of experiments will be necessary to fully work out if and how the JH regulatory network has been co-opted into metamorphosis.

We agree completely and should be a feature of future work.

The results generally support the authors' conclusions. However, the discussion contains a lot of speculation and some far-reaching conclusions are made about the role of JH and how it became co-opted into controlling metamorphosis. There are some interesting hypotheses presented and the author's speculations are consistent with the data presented. However, it is difficult to make evolutionary inferences from a single data point as although Thermobia is a basally branching insect, the lineage giving rise to Thermobia diverged from the lineages giving rise to the holo- and hemimetabolous insects approx.. 400 mya and it is possible that the effects of JH seen in Thermobia reflect lineage-specific effects rather than the 'ancestral state'. The authors ignore the possibility that there has been substantial rewiring of the networks that are JH responsive across these 400 my. I would encourage the authors to temper some of the discussion of these hypotheses and include some of the limitations of their inferences regarding the role of JH in the evolution of metamorphosis in their discussion.

We have tried to be less all-encompassing in the Discussion. The strongest comparisons can be made between ametabolous and hemimetabolous insects and we have focused most of the Discussion on the role of JH in that transition. We still include some discussion of holometabolous insects because the ancestral embryonic functions of JH may be somehow related to the unusual reappearance of JH in the prepupal period. We have reduced this discussion to only a few sentences.

Reviewer #3 (Recommendations For The Authors):

(1) The overall manuscript is very long (especially the discussion), and the main messages of the manuscript get lost in some of the details. I would suggest that the authors move some of the results to the supplementary material (e.g. it might be possible to put a lot of the detail of Thermobia embryogenesis into the supplementary text if the authors feel it is appropriate). The discussion contains a lot of speculation and I suggest the authors make this more concise. One example: At the moment there is a large section on the modification in JH function during the evolution of holo and hemi-metabolous life history strategies. There are some interesting ideas in this section and the authors do a good job of integrating their findings with the literature - but I would encourage the authors to limit the bulk of their discussion to the specific things that their results demonstrate. E.g. The first half of p17 contains too much detail, and the focus should be on the relationship with Thermobia (as at the bottom of p17).

Section has been revised and is more focused

(2) I would also suggest a thorough proofread of the manuscript, I have highlighted some of the errors/points of confusion that I found in the list below - but this list is unlikely to be exhaustive . We appreciate catching the errors. Hopefully the final version is better proofed.

(3) It might be me, but I found the wording in the second half of the abstract a bit confusing. Particularly the statement about the redeployment of morphogen systems - could this be stated more clearly?

Abstract has been revised.

(4) Introduction

a. "powered flight" rather than 'power flight'

Done

b. 'brought about a hemimetabolous lifecycle' implies causality which hasn't been shown and directionality to evolution - suggest 'facilitated the evolution of a hemi...". Similar comment for 'subsequent step to complete metamorphosis'.

c. Bottom of p2 - unclear whether you are referring to hemi- holo- or both

d. Suggest removing sentence beginning "besides its effects..." as the relevance of the role of JH in caste isn't clear.

Kept sentence but removed initial clause

e. State that Thermoia is a Zygentoma.

Done

f. Throughout - full species names on first usage only, T. domestica on subsequent usages.

We will continue to use genus names for the reason given above.

Gene names e.g. kr-h1 in italics.

g. 'antagonise morphogens"? rather than 'antagonise morphoentic'.

Done

(5) Results

a. Unclear why drawings are provided rather than embryonic images in Fig. 1A

We think that the points can be made better with diagrams.

b. Top of p4, is 'slot' the correct word?

Corrected

c. Unclear why the measurements of JHIII weren't measured before 5 days AEL, especially given that many of the manipulative experiments are at earlier time points than this. I appreciate that, based on kr-h1, levels that JHIII is also likely to be low.

d. Reference for the late embryonic peak of 20E being responsible for the J2 cuticle?

Clarified that this is an assumption

e. Clarify "some endocrine related transcripts" why were these ones in particular picked? Kr-h1 is a good transcriptional proxy for JH and Met is the JH-receptor, why myoglianin and not some of the other transcriptional proxies of neuroendocrine signalling?

Hopefully, the choice is clearer.

f. Fig 2C rather than % embryo development for the gene expression data please represent this in days (to be consistent with your other figures).

It is now consistent with other parts of figure.

g. In Fig. 3 the authors do t-tests, because there are three groups there needs to be some correction for multiple testing (e.g. Bonferroni) can the authors add this to the relevant methods section?

We think that pair-wise comparisons are appropriate.

h. Fig. 3 legend: you note that you treat stage 2 juveniles with 7EP - I couldn't tell what AEL this corresponded to.

This is after hatching so AEL does not apply.

i. Top of p7 'deformities' rather than 'derangements'?

Done

j. Regarding the dosage effects of embryonic abnormalities - it would be good to include these in the supp material, as it convinces the reader that the effects you have seen aren't just due to toxicity.

It is not clear what the objection is.

k. Bottom of p7 'problematic' not 'problematical'

Done

l. P8 Why are the clusters of Its important? - provide a bit more interpretation for the reader here.

This is clear in the revised version.

m. P9 Why is the modulation of transcription of kr-h1, met, and myo important in this context

Explained

n. P9 'fig. 7F'? there is no Fig. 5F

Thanks for catching the typo.

o. Fig. 7B add to the legend which treatment the dark and light points correspond to.

We think it is obvious from the labeling on Fig 7B.

(6) Discussion:

a. What do we know about how terminal differentiation is controlled in non-insect arthropods? Most of the discussion is focused on insects (which makes sense as JH is an insect-specific molecule), but if the authors are arguing the ancestral role of JH it would be useful to know how their findings relate to non-insect arthropods.

We have not been able to find any information about systemic signals being involved in non-insect arthropods.

b. There is no Fig. 5E (are they referring to 7E?)

Yes, it should have been Fig. 7E.

c. Is myoglianin a direct target of JH in other species?

Other reports are in postembryonic stages and show that myoglianin suppresses JH production. Our paper is the first examination in embryos and we find that the opposite is true – i.e., that JH treatment suppresses myoglianin production. We suspect that these two signaling systems are mutually inhibitory. It would be interesting to see whether treatment of a post-critical weight larva with JH (which would induce a supernumerary larval molt) would also suppress myoglianin production (as we see in Thermobia embryos).

d. P12 What is the evidence that JH interacts with the first 20E peak to alter the embryonic cuticle?

We are not sure what the issue is. The experimental fact is that treatment with JH before the E1 ecdysteroid peak causes the production of an altered E1 cuticle. We are faced with the question of why is this molt sensitive to JH when the latter will not appear until 3 or 4 days later? A possible answer is that the ecdysone response pathway has a component that has inherent JH sensitivity. The mosquito data suggest that Taiman provides another link between JH and ecdysone action

e. Top of p13 - this paragraph can be cut down substantially. Although this is evidence that JH can alter ecdysteriods - it is in a species that is 400 my derived from the target species. Is it likely to be the exact same mechanism? I would encourage the authors to distil and retain the most important points.

This paragraph has been shortened and focused.

f. Bottom of p13 - what does this study add to this knowledge?

The response of Thermobia embryos to JH treatment is qualitatively the same as seen in other short germband embryos. This similarity supports the assumption that the same responses would have been seen in their last common ancestor.

g. P19 the last paragraph in the conclusions is really peripherally relevant to the paper and is a bit of a stretch, I would encourage the authors to leave this section out.

We agree that it is a stretch. JH and its precursor MF are the only sesquiterpene hormones. How did they come about to acquire this function? We think it is worth pointing out the farnesol metabolites have been associated with promoting differentiation in various eukaryotes. An ancient feature of these molecules in promoting (maintaining?) differentiation may have been exploited by the insects to develop a unique class of hormones. It is worth putting the idea out to be considered.

h. P19 "conclusions" rather than 'concluding speculations'.

Changed as suggested.

Methods:

It is standard practice to include at least two genes as reference genes for RT-qPCR analysis (https://doi.org/10.1186/gb-2002-3-7-research0034, https://doi.org/10.1373/clinchem.2008.112797) If there are large-scale differences in the tissues being compared (e.g. as there are here during development) then more than two reference genes may be required and a reference gene study (such as https://doi.org/10.3390%2Fgenes12010021) is appropriate. Have the authors confirmed that rp49 is stably expressed during the stages of Thermobia development that they assay here?

We have explained our choice in the Methods.

Author Response

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

This work describes a new method for sequence-based remote homology detection. Such methods are essential for the annotation of uncharacterized proteins and for studies of protein evolution.

Strengths:

The main strength and novelty of the proposed approach lies in the idea of combining stateof-the-art sequence-based (HHpred and HMMER) and structure-based (Foldseek) homology detection methods with recent developments in the field of protein language models (the ESM2 model was used). The authors show that features extracted from high-dimensional, information-rich ESM2 sequence embeddings can be suitable for efficient use with the aforementioned tools.

The reduced features take the form of amino acid occurrence probability matrices estimated from ESM2 masked-token predictions, or structural descriptors predicted by a modified variant of the ESM2 model. However, we believe that these should not be called "embeddings" or "representations". This is because they don't come directly from any layer of these networks, but rather from their final predictions.

We agree that there is some room for discussion about whether the amino acid probabilities returned by pre-trained ESM-2 and the 3Di sequences returned by ESM-2 3B 3Di can be properly referred to as “embeddings”. The term “embedding” doesn’t have a formal definition, other than some kind of alternative vector representation of the input data which, preferably, makes the input data more suitable for some downstream task. In that simple sense of the word “embedding”, amino acid probabilities and 3Di sequences output by our models are, indeed, types of embeddings. We posed the question on Twitter (https://twitter.com/TrichomeDoctor/status/1715051012162220340) and nobody responded, so we are left to conclude that the community is largely ambivalent about the precise definition of “embedding”.

We’ve added language in our introduction to make it more clear that this is our working definition of an “embedding”, and why that definition can apply to profile HMMs and 3Di sequences.

The benchmarks presented suggest that the approach improves sensitivity even at very low sequence identities <20%. The method is also expected to be faster because it does not require the computation of multiple sequence alignments (MSAs) for profile calculation or structure prediction.

Weaknesses:

The benchmarking of the method is very limited and lacks comparison with other methods. Without additional benchmarks, it is impossible to say whether the proposed approach really allows remote homology detection and how much improvement the discussed method brings over tools that are currently considered state-of-the-art.

We thank the reviewer for the comment. To address the question, we’ve expanded the results by adding a new benchmark and added a new figure, Figure 4. In this new content, we use the SCOPe40 benchmark, originally proposed in the Foldseek paper (van Kempen et al., 2023), to compare our best method, ESM-2 3B 3Di coupled to Foldseek, with several other recent methods. We find our method to be competitive with the other methods.

We are hesitant to claim that any of our proposed methods are state-of-the-art because of the lack of a widely accepted standard benchmark for remote homology detection, and because of the rapid pace of advancement of the field in recent years, with many groups finding innovative uses of pLMs and other neural-network models for protein annotation and homology detection.

Reviewer #2 (Public Review):

Summary:

The authors present a number of exploratory applications of current protein representations for remote homology search. They first fine-tune a language model to predict structural alphabets from sequence and demonstrate using these predicted structural alphabets for fast remote homology search both on their own and by building HMM profiles from them. They also demonstrate the use of residue-level language model amino acid predicted probabilities to build HMM profiles. These three implementations are compared to traditional profile-based remote homology search.

Strengths:

• Predicting structural alphabets from a sequence is novel and valuable, with another approach (ProstT5) also released in the same time frame further demonstrating its application for the remote homology search task.

• Using these new representations in established and battle-tested workflows such as MMSeqs, HMMER, and HHBlits is a great way to allow researchers to have access to the state-of-the-art methods for their task.

• Given the exponential growth of data in a number of protein resources, approaches that allow for the preparation of searchable datasets and enable fast search is of high relevance.

Weaknesses:

• The authors fine-tuned ESM-2 3B to predict 3Di sequences and presented the fine-tuned model ESM-2 3B 3Di with a claimed accuracy of 64% compared to a test set of 3Di sequences derived from AlphaFold2 predicted structures. However, the description of this test set is missing, and I would expect repeating some of the benchmarking efforts described in the Foldseek manuscript as this accuracy value is hard to interpret on its own.

The preparation of training and test sets are described in the methods under the heading “Fine tuning ESM-2 3B to convert amino acid sequences into 3Di sequences”. Furthermore, there is code in our github repository to reproduce the splits, and the entire model training process: https://github.com/seanrjohnson/esmologs#train-esm-2-3b-3di-starting-from-the-esm-2-3bpre-trained-weights

We didn’t include the training/validation/test splits in the Zenodo repository because they are very large: train 33,924,764; validation 1,884,709; test 1,884,710 sequences, times 2 because there are both amino acid and 3Di sequences. It comes out to about 30 Gb total, and is easily rebuilt from the same sources we built it from.

We’ve added the following sentence to the main text to clarify:

“Training and test sets were derived from a random split of the Foldseek AlphaFold2 UniProt50 dataset (Jumper et al., 2021; van Kempen et al., 2023; Varadi et al., 2022), a reducedredundancy subset of the UniProt AlphaFold2 structures (see Methods for details).”

To address the concern about comparing to Foldseek using the same benchmark, we’ve expanded the results section and added a new figure, Figure 4 using the SCOPe40 benchmark originally presented in the Foldseek paper, and subsequently in the ProstT5 paper to compare Foldseek with ESM-2 3B 3Di to Foldseek with ProstT5, AlphaFold2, and experimental structures.

• Given the availability of predicted structure data in AFDB, I would expect to see a comparison between the searches of predicted 3Di sequences and the "true" 3Di sequences derived from these predicted structures. This comparison would substantiate the innovation claimed in the manuscript, demonstrating the potential of conducting new searches solely based on sequence data on a structural database.

See response above. We’ve now benchmarked against both ProstT5 and AF2.

• The profile HMMs built from predicted 3Di appear to perform sub-optimally, and those from the ESM-2 3B predicted probabilities also don't seem to improve traditional HMM results significantly. The HHBlits results depicted in lines 5 and 6 in the figure are not discussed at all, and a comparison with traditional HHBlits is missing. With these results and presentation, the advantages of pLM profile-based searches are not clear, and more justification over traditional methods is needed.

We thank the reviewer for pointing out the lack of clarity in the discussion of lines 5 and 6.

We’ve re-written that section of the discussion, and reformatted Figure 3 to enhance clarity.

We agree, a comparison to traditional HHBlits could be interesting, but we don’t expect to see stronger performance from the pLM-predicted profiles than from traditional HHBlits, just as we don’t see stronger performance from pLM-hmmscan or pLM-Foldseek than from the traditional variants. We think that the advantages of pLM based amino acid hmm searches are primarily speed. There are many variables that can influence speed of generating an MSA and HMM profile, but in general we expect that it will be much slower than generating an HMM profile from a pLM.

We don’t know why making profiles of 3Di sequences doesn’t improve search sensitivity, we just think it’s an interesting result that is worth presenting to the community. Perhaps someone can figure out how to make it work better.

• Figure 3 and its associated text are hard to follow due to the abundance of colors and abbreviations used. One figure attempting to explain multiple distinct points adds to the confusion. Suggestion: Splitting the figure into two panels comparing (A) Foldseek-derived searches (lines 7-10) and (B) language-model derived searches (line 3-6) to traditional methods could enhance clarity. Different scatter markers could also help follow the plots more easily.

We thank the reviewer for this helpful comment. We’ve reformatted Figure 3 as suggested, and we think it is much easier to read now.

• The justification for using Foldseek without amino acids (3Di-only mode) is not clear. Its utility should be described, or it should be omitted for clarity.

To us, the use of 3Di-only mode is of great theoretical interest. From our perspective, this is one of our most significant results. Previous methods, such as pLM-BLAST and related methods, have made use of very large positional embeddings to achieve sensitive remote homology search. We show that with the right embedding, you don’t need very many bits per position to get dramatically improved search sensitivity from Smith-Waterman, compared to amino acid searches. We also doubt that predicted 3Di sequences are the optimal small encoding for remote homology detection. This result and observation opens up an exciting avenue for future research in developing small, learned positional embeddings that are optimal for remote homology detection and amenable to SIMD-optimized pre-filtering and Smith-Waterman alignment steps.

We’ve expanded the discussion, explaining why we are excited about this result.

• Figure 2 is not described, unclear what to read from it.

It's just showing that ESM-2-derived amino acid probabilities closely resemble amino acid frequencies in MSAs. We think it gives readers some visual intuition about why predicted profile HMMs perform as well as they do. We’ve added some additional explanation of it in the text.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

The paper would mainly benefit from a more comprehensive benchmark:

We suggest that the authors extend the benchmark by including the reference methods (HHpred and Foldseek) run with their original representations, i.e., MSAs obtained with 2-3 iterations of hhblits (for HHpred) and experimental or predicted structures (for Foldseek). HHpred profile-profile comparisons and Foldseek structure-structure comparisons would be important reference points for assessing the applicability of the proposed approach in distant homology detection. It is also essential to compare the method with other emerging tools such as EBA (DOI: 10.1101/2022.12.13.520313), pLM-BLAST (DOI: 10.1101/2022.11.24.517862), DEDAL (DOI: 10.1038/s41592-022-01700-2), etc.

We also suggest using an evolutionary-oriented database for the benchmark, such as ECOD or CATH (these databases classify protein domains with known structures, which is important in the context of including Foldseek in the benchmark). We ran a cursory benchmark using the ECOD database and generated HH-suite .hhm files (using the single_seq_to_hmm.py and hhsearch_multiple.py scripts). Precision and recall appear to be significantly lower compared to "vanilla" hhsearch runs with MSA-derived profiles. It would also be interesting to see benchmarks for speed and alignment quality.

The pLM-based methods for homology detection are an emerging field, and it would be important to evaluate them in the context of distinguishing between homology and analogy. In particular, the predicted Foldseek representations may be more likely to capture structural similarity than homology. This could be investigated, for example, using the ECOD classification (do structurally similar proteins from different homology groups produce significant matches?) and/or resources such as MALISAM that catalog examples of analogy.

We’ve added the SCOPe40 benchmark, which we think at least partially addresses these comments, adding a comparison to pLM-BLAST, ProstT5, and AF2 followed by Foldseek. The question of Analogy vs homology is an interesting one. It could be argued that the SCOPe40 benchmark addresses this in the difference between Superfamily (distant homology) and Fold (analogy, or very distant homology).

Our focus is on remote homology detection applications rather than alignment quality, so we don’t benchmark alignment quality, although we agree that those benchmarks would be interesting.

Page 2, lines 60-67. This paragraph would benefit from additional citations and explanations to support the superiority of the proposed approach. The fact that flattened embeddings are not suitable for annotating multidomain proteins seems obvious. Also, the claim that "current search implementations are slow compared to other methods" should be supported (tools such as EBA or pLM-BLAST have been shown to be faster than standard MSA-based methods). Also, as we mentioned in the main review, we believe that the generated pseudo-profiles and fine-tuned ESM2 predictions should not be called "smaller positional embeddings".

Discriminating subdomains was a major limitation of the influential and widely-cited PfamN paper (Bileschi et al., 2022), we’ve added a citation to that paper in that paragraph for readers interested in diving deeper.

To address the question of speed, we’ve included data preparation and search benchmarks as part of our presentation of the SCOPe40 benchmark.

Finally, we were not sure why exactly every 7th residue is masked in a single forward pass. Traditionally, pseudo-log likelihoods are generated by masking every single token and predicting probabilities from logits given the full context - e.g. https://arxiv.org/pdf/1910.14659.pdf. Since this procedure is crucial in the next steps of the pipeline, it would be important to either experiment with this hyperparameter or explain the logic used to choose the mask spacing.

We’ve added discussion of the masking distance to the Methods section.

Reviewer #2 (Recommendations For The Authors):

• While the code and data for the benchmark are available, the generation of searchable databases using the methods described for a popular resource such as Pfam, AFDB, SCOP/CATH which can be used by the community would greatly boost the impact of this work.

3Di sequences predicted by ESM-2 3B 3Di can easily be used as queries against any Foldseek database, such as PDB, AFDB, etc. We’ve added Figure 4E to demonstrate this possibility, and added some related discussion.

• Minor: In line 114, the text should likely read "compare lines 7 and 8" instead of "compare lines 6 and 7."

We’ve clarified the discussion of Figure 3.

Author Response

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

Reviewer #1 (Public Review):

The current manuscript focuses on the adenine phosphoribosyltransferase (Aprt) and how the lack of its function affects nervous system function. It puts it into the context of Lesch-Nyhan disease, a rare hereditary disease linked to hypoxanthine-guanine phosphoribosyltransferase (HGPRT). Since HGPRT appears absent in Drosophila, the study focuses initially on Aprt and shows that aprt mutants have a decreased life-span and altered uric acid levels (the latter can be attenuated by allopurinol treatment). Moreover, aprt mutants show defects in locomotor reactivity behaviors. A comparable phenotype can be observed when specifically knocking down aprt in dopaminergic cells. Interestingly, also glia-specific knock-down caused a similar behavioral defect, which could not be restored when re-expressing UAS-aprt, while neuronal re-expression did restore the mutant phenotype. Moreover, mutants, pan-neuronal and pan-neuronal plus glia RNAi for aprt caused sleep-defects. Based on immunostainings Dopamine levels are increased; UPLC shows that adenosine levels are reduced and PCR showed in increase of Ent2 levels are increased (but not AdoR). Moreover, aprt mutants display seizure-like behaviors, which can be partly restored by purine feeding (adenosine and N6methyladenosine). Finally, expression of the human HGPRT also causes locomotor defects.

The authors provide a wide range of genetic experimental data to assess behavior and some molecular assessment on how the defects may emerge. It is clearly written, and the arguments follow the experimental evidence that is provided. The findings provide a new example of how manipulating specific genes in the fruit fly allows the study of fundamental molecular processes that are linked to a human disease.

We thank the reviewer for his clear understanding and positive assessment of our work.

Reviewer #2 (Public Review):

The manuscript by Petitgas et al demonstrates that loss of function for the only enzyme responsible for the purine salvage pathway in fruit-flies reproduces the metabolic and neurologic phenotypes of human patients with Lesch-Nyhan disease (LND). LND is caused by mutations in the enzyme HGPRT, but this enzyme does not exist in fruit-flies, which instead only have Aprt for purine recycling. They demonstrate that mutants lacking the Aprt enzyme accumulate uric acid, which like in humans can be rescued by feeding flies allopurinol, and have decreased longevity, locomotion and sleep impairments and seizures, with striking resemblance to HGPRT loss of function in humans. They demonstrate that both loss of function throughout development or specifically in the adult ubiquitously or in all neurons, or dopaminergic neurons, mushroom body neurons or glia, can reproduce the phenotypes (although knock-down in glia does not affect sleep). They show that the phenotypes can be rescued by over-expressing a wild-type form of the Aprt gene in neurons. They identify a decrease in adenosine levels as the cause underlying these phenotypes, as adenosine is a neurotransmitter functioning via the purinergic adenosine receptor in neurons. In fact, feeding flies throughout development and in the adult with either adenosine or m6A could prevent seizures. They also demonstrate that loss of adenosine caused a secondary up-regulation of ENT nucleoside transporters and of dopamine levels, that could explain the phenotypes of decreased sleep and hyperactivity and night. Finally, they provide the remarkable finding that over-expression of the human mutant HGPRT gene but not its wild-type form in neurons impaired locomotion and induced seizures. This means that the human mutant enzyme does not simply lack enzymatic activity, but it is toxic to neurons in some gain-of-function form. Altogether, these are very important and fundamental findings that convincingly demonstrate the establishment of a Drosophila model for the scientific community to investigate LND, to carry out drug testing screens and find cures.

We thank the reviewer for his clear understanding and positive assessment of our work.

The experiments are conducted with great rigour, using appropriate and exhaustive controls, and on the whole the evidence does convincingly or compellingly support the claims. The exception is an instance when authors mention 'data not shown' and here data should either be provided, or claims removed: "feeding flies with adenosine or m6A did not rescue the SING phenotype of Aprt mutants (data not shown)". It is important to show these data (see below).

As recommended by the reviewer, these results are now shown in the new Figure S15.

Sleep is used to refer to lack of movement of flies to cross a beam for more than 5 minutes. However, lack of movement does not necessarily mean the flies are asleep, as they could be un-motivated to move (which could reflect abnormal dopamine levels) or engaged in incessant grooming instead. These differences are important for future investigation into the neural circuits affect by LND.

We agree that the method we used could overestimate sleep duration because flies that don't move do not necessarily sleep either, as it is the case with brain-dopamine deficient flies (Riemensperger et al., PNAS 2011). To address this issue, we have recorded video data showing that after 5 min of inactivity, wild-type and Aprt5 mutant flies are less sensitive to stimulation, indicating that they were indeed asleep. This is now shown in the new Figure S10 and mentioned on page 17, lines 338-339 in the main text. In addition, in this work we report that Aprt mutant flies have a nocturnal insomnia phenotype. Sleep overestimation is not, therefore, an issue that could challenge these results.

The authors claim that based on BLAST genome searchers, there are no HPRTI (encoding HGPRT) homologues in Drosophila. However, such a claim would require instead structure-based searches that take into account structural conservation despite high sequence divergence, as this may not be detected by regular BLAST.

To reinforce our conclusions about the lack of homologue of the human HPRT1 gene in Drosophila, we have now added a Results section about the evolution of HGPRT proteins on pages 6-7, lines 122150, and two phylogenetic analyses as new Figures S2 and S3 with more details in legends. We have also carried out structural similarity searches against the RCSB PDB repository. The structural analysis did not identify any relevant similarity with HGPRT 3D structures in Insecta (mentioned lines 146-150). We hope these new analyses address the Reviewer's concerns. Furthermore, as shown in Table S2, no enzymatic HGPRT activity could be detected in extracts of wild-type Drosophila. A protein that would be structurally similar to human HGPRT but with a divergent sequence could not be involved in purine recycling without expressing HGPRT-like activity. In contrast, enzymatic Aprt activity could be easily detected in this organism (Figure S4 and Table S1).

This work raises important questions that still need resolving. For example, the link between uric acid accumulation, reduced adenosine levels, increased dopamine and behavioural neurologic consequences remain unresolved. It is important that they show that restoring uric acid levels does not rescue locomotion nor seizure phenotypes, as this means that this is not the cause of the neurologic phenotypes.

We agree with the reviewer about the potential importance of our results and the need to resolve the exact origin of the neurological phenotypes. This would need to be addressed in further studies in our opinion. The fact that allopurinol treatment did not improve the locomotor ability of Aprt5 mutant flies is now shown in Figure 1D, E to emphasize this result. Results showing that allopurinol does not rescue the bang-sensitivity phenotype of Aprt-deficient mutants are shown in Figure S14.

Instead, their data indicate adenosine deficiency is the cause. However, one weakness is that for the manipulations they test some behaviours but not all. The authors could attempt to improve the link between mechanism and behaviour by testing whether over-expression of Aprt in neurons or glia, throughout development or in the adult, and feeding with adenosine and m6A can rescue each of the behavioural phenotypes handled: lifespan, SING, sleep and seizures. The authors could also attempt to knock-down dopamine levels concomitantly with feeding with adenosine or m6A to see if this rescues the phenotypes of SING and sleep.

The reviewer is right. However, carrying out all these experiments properly with enough repeats will require about two more years of work. Because of that, they could not be included in the revision of the present article. Here we show that Aprt overexpression in neurons, but not in glia, rescues the SING phenotype of Aprt5 mutants (Figure 2B and 2E). We have also added in the revised article the new result that Aprt overexpression reduces transcript levels of DTH1, which codes for the neural form of the dopamine-synthesizing enzyme tyrosine hydroxylase (new Figure 5F).

Visualising the neural circuits that express the adenosine receptor could reveal why the deficit in adenosine can affect distinct behaviours differentially, and which neurologic phenotypes are primary and which secondary consequences of the mutations. This would allow them to carry out epistasis analysis by knocking-down AdoR in specific circuits, whilst at the same time feeding Aprt mutants with Adenosine.

Deciphering the specific circuits involved in the various effects of adenosine would indeed be extremely interesting. Unfortunately very few is currently known about the neural circuits that express AdoR in flies. No antibody is available to detect this receptor in situ and mutated AdoR gene coding for a tagged form of the receptor has not been engineered yet to our knowledge.

The revelation that the mutant form of human HGPRT has toxic effects is very intriguing and important and it invites the community to investigate this further into the future.

To conclude, this is a fundamental piece of work that opens the opportunity for the broader scientific community to use Drosophila to investigate LND.

We sincerely thank the reviewer for his thoughtful and positive comments on our work.

Reviewer #3 (Public Review):

The study attempts to develop a Drosophila model for the human disease of LND. The issue here, and the main weakness of this study, is that Drosophila does not express the enzyme, HGPRT, which when mutated causes LND. The authors, instead, mutate the functionally-related Drosophila Aprt enzyme. However, it is unknown whether Aprt is also a structural homologue. Because of this, it will likely not be possible to identify pharmacological compounds that rescue HGPRT activity via a direct interaction (unless modelling predicts high conservation of substrate binding pocket between the two enzymes, etc).

As stated in our Provisional Responses prior to revision of the Reviewed Preprint, the enzymes APRT and HGPRT are actually known to be functionally and structurally related. We apologize for not providing this information in the original submission. This point is now made clearer in the revised article on page 39, lines 785-792. Indeed, both human APRT and HGPRT belong to the type I PRTases family identified by a conserved phosphoribosyl pyrophosphate (PRPP) binding motif, which is used as a substrate to transfer phosphoribosyl to purines. This binding motif is only found in PRTases from the nucleotide synthesis and salvage pathways (see: Sinha and Smith (2001) Curr Opin Struct Biol 11(6):733-9, doi: 10.1016/s0959-440x(01)00274-3). The purine substrates adenine, hypoxanthine and guanine share the same chemical skeleton and APRT can bind hypoxanthine, indicating that APRT and HGPRT also share similarities in their substrate binding sites (Ozeir et al. (2019) J Biol Chem. 294(32):11980-11991, doi: 10.1074/jbc.RA119.009087). Moreover, Drosophila Aprt and Human APRT are closely related as the amino acid sequences of APRT proteins have been highly conserved throughout evolution (see Figure S5B in our paper).

An additional weakness is that the study does not identify a molecule that may act as a lead compound for further development for treating LND. Rather, the various rescues reported are selective for only a subset of the disease-associated phenotypes. Thus, whilst informative, this first section of the study does not meet the study ambitions.

In this study, we identify adenosine and N6-methyladenosine as rescuers of the epileptic behavior in Aprt mutant flies (shown in Figure 7E, F). Interestingly, the same molecules have been found to rescue the viability of fibroblasts and neural stem cells derived from iPSCs of LND patients, in which de novo purine synthesis was prevented (discussed on page 38, lines 747-753). This suggests that the Drosophila model reported here could help to identify new genetic targets and pharmacological compounds capable to rescue HGPRT mutations in humans.

The second approach adopted is to express a 'humanised mutated' form of HGPRT in Drosophila, which holds more promise for the development of a pharmacological screen. In particular, the locomotor defect is recapitulated but the seizure-like activity, whilst reported as being recapitulated, is debatable. A recovery time of 2.3 seconds is very much less than timings for typical seizure mutants. Nevertheless, the SING behaviour could be sufficient to screen against. However, this is not explored.

We agree with the reviewer that it would be very interesting to do a pharmacological screen in this second LND model. However, we did not have the possibility to carry out such a screen yet.

In summary, this is a largely descriptive study reporting the behavioural effects of an Aprt loss-offunction mutation. RNAi KD and rescue expression studies suggest that a mix of neuronal (particularly dopaminergic and possibly adenosinergic signalling pathways) and glia are involved in the behavioural phenotypes affecting locomotion, sleep and seizure. There is insufficient evidence to have confidence that the Arpt fly model will prove valuable for understanding / treating LND.

Here we report many common phenotypes between the Aprt fly model and the symptoms of LND patients (reduced longevity, locomotor problems, sleep defects, overproduction of uric acid that is rescued by allopurinol treatment…). Moreover, APRT and HGPRT enzymes are both functional and structural homologues, as explained in our answers. We also found that the same drugs can rescue the seizure-like phenotype in Aprt-deficient flies and the viability of LND fibroblasts and neural stem cells, derived from iPSCs of LND patients, in which de novo purine synthesis is prevented (Figure 7E, F). In many respects, our results therefore suggest that Aprt mutant flies could be useful to better understand LND, and potentially to screen for new therapeutic compounds.

From the Reviewing Editor:

(1) How are the pathways of purine catabolism different between flies and mammals? How does the absence of HGPRT and presence of only AGPRT affect purine catabolism? When did HGPRT appear in evolution?

Purine catabolism is quite similar in flies and mammals, except for the lack of urate oxidase in primates, as described in Figure S1. We added words in the revised article about purine anabolism/catabolism pathways lines 123-126 (see below our detailed response to Reviewer 1’s Recommandations). HGPRT is present in Bacteria, Archea and Eukaryota, and nearly all animal phyla. However, BLAST search indicates that HGPRT homologues cannot be found in most insect species, such as Drosophila. To reinforce our conclusions about the lack of homologue of the human HPRT1 gene in Drosophila melanogaster, we have now added a Results section about the evolution of HGPRT proteins on pages 6-7, lines 122-150, and two phylogenetic analyses as new Figures S2 and S3 with details in legends.

In addition to BLAST a structural based modelling method should be used to establish the loss of HGPRT in Drosophila.

In agreement with the phylogenetic analyses, we have confirmed that no HGPRT enzymatic activity can be detected in wild-type Drosophila extract (Table S2). To complete these observations, as recommended by reviewer #2, we have carried out 3D structure-based searches in the RCSB Protein Data Bank. This enabled us to compare human HGPRT with all currently available protein structures. W found no Drosophila protein with a divergent sequence showing relevant structural similarity to human HGPRT. In contrast, this search identified proteins similar to human HGPRT in many other species of Eukaryota, Archea and Bacteria. This is now mentioned on page 7, lines 146-150 in the revised article.

(2) Of the three biochemical changes reported the change in dopamine levels should be validated by other methods given the unreliable nature of IHC.

As recommended by Reviewer #1, we have added the results of new experiments carried out by RTqPCR and Western blotting, which confirm the effect of Aprt mutation on brain dopamine levels. In addition, we added the consistent result that Aprt overexpression reduces transcript levels of DTH1. The results are shown in the new panels E to H of Figure 5 and mentioned in the text on page 20, lines 385-389.

(3) As suggested by reviewer 2 it would be helpful to clearly identify which of the three biochemical changes (DA, uric acid, adenosine) are responsible for the numerous behaviours tested. This is important because it is relevant for developing any therapeutic strategy arising from this study.

We agree that it would be very interesting to decipher the relationship between the different behaviors observed in mutant flies and the biochemical changes (dopamine, uric acid or adenosine). However, this would require a large amount of new experiments and it would probably double the size of our paper, which already includes many original data. In our opinion, such a detailed study should logically be the purpose of another article.

(4) There is concern regarding the robustness of the seizure data. Reviewer 3 has suggestions on how to address this.

See our answers to Reviewer 3’s recommendations below.

(5) Editorial corrections and changes suggested by reviewers 2 and 3 need to be addressed.

As indicated in our answers, we have taken into account and when possible addressed the corrections and changes suggested by the reviewers.

(6) It is recommended that the authors tone down the relevance of this model for LND, particularly in the abstract. The focus should be on stating what is actually delivered.

As recommended by the reviewing editor, and to take in account the reserved comments of reviewer #3, we have toned down our affirmation that our new fly models are relevant for LND in the last sentences of the Abstract and Discussion, and also added a question mark in the subtitle of the Discussion on line 777. As mentioned in our provisional responses to the Public Reviews, we would like to emphasize, however, that reviewers #1 and #2 expressed more confidence than reviewer #3 in the potential usefulness of our work. Reviewer #1 indeed stated that: “The findings provide a new example of how manipulating specific genes in the fruit fly allows the study of fundamental molecular processes that are linked to a human disease”, and reviewer #2 further wrote: "Altogether, these are very important and fundamental findings that convincingly demonstrate the establishment of a Drosophila model for the scientific community to investigate LND, to carry out drug testing screens and find cures”, and added: “To conclude, this is a fundamental piece of work that opens the opportunity for the broader scien2fic community to use Drosophila to inves2gate LND”.

Reviewer #1 (Recommendations For The Authors):

• An important prerequisite for the current study is that there appears to be no HGPRT "activity" in Drosophila. It is initially stated that there was previously no "HGPRT activity observed" in two papers form the 70ies. It would be important to corroborate this notion and provide some background on the <br /> /catabolism pathways. How shared or divergent are these pathways between Drosophila and mammals?

In agreement with the pioneering studies of Becker (1974a, b), we have confirmed in this work that no HGPRT enzymatic activity can be detected in wild-type Drosophila extracts, as mentioned in Results on page 6, lines 127-130 and reported in Table S2. Purine catabolism is quite similar in flies and mammals, except for the lack of urate oxidase in primates, as shown in Figure S1. All the enzymes involved in purine anabolism/catabolim or recycling in humans have been conserved in Drosophila and humans, with the notorious exception of HPRT1.

If there is no HGPRT gene, but only the APRT ortholog, what would this mean for the metabolites? Our enzymatic assays on Drosophila extracts indicated that hypoxanthine and guanine cannot be recycled into IMP and GMP, respectively, contrary to adenine which can be converted into AMP in flies. In the absence of HGPRT activity, GMP and IMP could be produced by de novo purine synthesis, or, alternatively, synthesized from AMP, which can be converted into IMP by the enzyme AMPD, and then IMP can be converted into GMP by the enzymes IMPDH and GMPS. These metabolic pathways are depicted in Figure S1A.

Is the lack of HGPRT specific for Drosophila, insects (generally in invertebrates)? I feel clarifying this would provide more insight into the motivation of the experimental approach.

As suggested by the Reviewer and the Reviewing Editor, we have addressed the evolution of HGPRT proteins more precisely in the revision. We have added a section on this subject in Results on pages 67, lines 122-150, and two phylogenetic analyses as Figures S2 and S3 with details in legends. A phylogenetic analysis was carried out a few years ago by Giorgio Matassi, who is now co-author of this paper. The most striking result was the great impact of horizontal gene transfer in the evolution of HGPRT in Insects (Figures S2 and S3). Our analysis of the phyletic distribution of HGPRT proteins revealed their striking rareness in Insecta, and in particular, their absence in Drosophilidae. The PSIBlast search detected however a significant hit in Drosophila immigrans (accession KAH8256851.1). Yet, this sequence is 100% identical to the HGPRT of the Gammaroteobacterium Serratia marcescens. Indeed, a phylogenetic analysis showed that D. immigrans HGPRT clusters with the Serratia genus (see Figure S3). This can be interpreted either a contamination of the sequenced sample, or as a very recent horizontal gene transfer event. The second scenario is more likely for the corresponding nucleotide sequences differ by 5 synonymous substitutions (out of 534 positions). A powerful approach to try to understand the "origin" of the D. immigrans protein would be to analyze whether horizontal gene transfer has affected its chromosomal neighbours. This approach, proposed previously by G. Matassi (BMC Evol Biol, 2017, 17:2, doi: 10.1186/s12862-016-0850-6), is highly demanding in terms of computing time and would require an ad hoc study. We hope that these new analyses address the Reviewer's concerns.

• On the mechanistic side on how the behavioral defects may arise, the authors show that dopaminergic neurons (and glia cells) are involved. One interesting finding is that dopamine immunostainings suggest increased dopamine levels. However, immunostainings are notorious for artifacts and do not provide a strong quantitative assessment. I feel it would be helpful to have an alternative technique to corroborate this finding.

We agree with the reviewer and we added the results of further confirmatory experiments in the four new panels E-H of Figure 5, showing that: 1) the transcript levels of DTH1 (encoding the neuronal isoform of the dopamine-synthesizing enzyme tyrosine hydroxylase in Drosophila) are increased in Aprt5 mutants compared to wild-type flies (new Figure 5E), 2) consistent with this, DTH1 transcript levels were found in contrast to be decreased when Aprt was overexpressed ubiquitously in flies (new Figure 5F), 3) Western blot experiments showed that DTH1 protein levels are also increased in Aprt5 mutant flies compared to controls (new Figure 5G-H).

Reviewer #2 (Recommendations For The Authors):

As mentioned in the public review, the behavioural phenotypes of decreased lifespan, SING, sleep and seizures could be tested for all manipulations: feeding with allopurinol, adenosine and m6A, and combining this with knock-down dopamine levels in PAMs or MBs. This could help dissect the relationship between mutations in Aprt and behaviour.

We thank the reviewer for these suggestions, and, indeed, we would have liked to do all these experiments. However, as mentioned in our responses to the Public Reviews, carrying out these experiments properly with sufficient repeats would require about two more years of work. We have already accumulated a large amount of data, so we have decided to publish our results at this stage in order to make our new fly models available to the scientific community. We are giving careful and due consideration to these experimental proposals and we hope to continue our investigation on this topic in the future.

It would also be helpful to find out which neurons and glia express AdoR. Perhaps there are already tools available the authors could test or at least check with the scRNAseq Fly Atlas (public Scope database).

Following the reviewer’s recommendation, we have checked the scRNAseq Fly Atlas for AdoR expression in the brain, compared to that of ple (encoding tyrosine hydroxylase) and Eaat1 (encoding the astrocytic glutamate transporter). As shown in the image below, the results are not very informative. AdoR appears to be expressed in rather widespread subsets of neurons and glial cells, that partly overlap with ple and Eaat1 expression. Further work would be required to identify more precisely the neurons and glial cells expressing AdoR in the brain.

Author response image 1.

Page 7, line 161: use of the word 'normalize'. "We tried to normalise uric acid content in flies..." would best to use 'rescue' instead, as normalisation in science has a different meaning.

We modified this word as suggested.

Page 9 line 203: 'genomic deficiencies that cover': the genetic term is 'uncover', as a deficiency for a locus reveals a phenotypes, thus it is said 'a gene uncovered by xx deficiency".

Thank you for this helpful remark. We corrected this in line 221.

Page 10, lines 206-208: 'allopurinol treatment did not improve the locomotor activity...". These are important observations that should be best presented within the main manuscript Figure 1.

As recommended, we have transferred the graphs of Figure S5 to new panels D and E of Figure 1.

Figure 4: please indicate genotypes in the figure, where no information is given that these are UASAprt-RNAi experiments.

We added the complete genotype in Figure 4G, and also in Figure S12C and D. Thank you for noting that.

Page 25 line 491: "None of these drugs was able to rescue the SING defects (data not shown)". Either provide the data or remove this claim.

We have added these data in the new Figure S15.

Statistical analyses: details are provided in the methods, but the name of test and multiple comparisons corrections should be also provided in the legends.

Thank you very much for the careful proofreading. This was an oversight and we have added the information in all legends of the revised article.

Reviewer #3 (Recommendations For The Authors):

This is a difficult manuscript to appreciate. The abstract and introduction suggest that the study is to identify novel treatments for a human disease (LND) by development of a Drosophila model. Much of the results, however, are focussed to describing the consequences to purine metabolism of the Aprt mutation. To my mind, a rewrite to focus on the latter would be beneficial. The potential applicability to LND would be best restricted to the discussion.

We apologize for not making our goals clearer. Our purpose was to find out if purine recycling deficiency could lead to metabolic and neurobehavioral disturbances in Drosophila, as it is the case in human LND patients when HGPRT is mutated. Interestingly, we observed that mutation of the only purine recycling enzyme in flies, Aprt, did induce defects in part comparable to that of LND in humans, including overproduction of uric acid that is rescued by allopurinol treatment, reduced longevity, and various neurobehavioral phenotypes including bang-sensitive seizure, sleep defects and locomotor impairments. We also identified adenosine and N6-methyladenosine as rescuers of the epileptic behavior in these mutants. These drugs were also identified as therapeutic candidates in screens based on iPSCs from LND patients. This suggests that Aprt deficiency in Drosophila could be used as a model to better understand this disease and find new therapeutic targets.

Regardless of the above comment, the concluding sentence of the abstract is inappropriate. This study does not show that Drosophila can be used to identify a cure for LND.

We agree with the Reviewer that the last sentence of the abstract was too affimative. As also recommended by the reviewing editor, we have modified this sentence in the abstract and other sentences in the text in order to tone down the affirmation that our new fly models are relevant for LND. See our answers to the Reviewing Editor above for details.

Indeed, I would challenge the premise that screening against a functional, but unknown if structural, homologue (Aprt) will ever provide an exploitable opportunity. To meet this statement, this study needs to identify a treatment that rescues all of the behavioural phenotypes associated with the Aprt mutation, in addition to rescuing the influences of the mis-expression of mutated HGPRT.

APRT and HGPRT are both functionally and structurally related. Both human APRT and HGPRT belong to the type I PRTases family identified by a conserved phosphoribosyl pyrophosphate (PRPP) binding motif, which is used as a substrate to transfer phosphoribosyl to purines. This binding motif is only found in PRTases from the nucleotide synthesis and salvage pathways (see: Sinha and Smith (2001) Curr Opin Struct Biol 11(6):733-9733-9, doi: 10.1016/s0959-440x(01)00274-3). The purine substrates adenine, hypoxanthine and guanine share the same chemical skeleton and APRT can bind hypoxanthine, indicating that APRT and HGPRT also share similarities in their substrate binding sites (Ozeir et al. (2019) J Biol Chem. 294(32): 11980-11991, doi: 10.1074/jbc.RA119.009087)). This point has been made clearer in the Discussion page 39, in lines 785-792.. Finally, Drosophila Aprt and Human APRT are closely related as the amino acid sequences of APRTs have been highly conserved throughout evolution (shown in Figure S5B).

With respect to expression of the mutated HGPRT: the short seizure recovery time of 2.3 seconds is not very convincing evidence of a seizure phenotype. This is far below the timings reported for typical BS mutations. Because of this, the authors should run a positive control (e.g. one of the wellestablished BS mutations: parabss, eas or jus) to validate their assay. Moreover, was the seizure induced by the Aprt mutation (17.3 secs - again a low value) rescued by prior exposure to an antiepileptic? Could this behaviour be, instead, related to the SING locomotor phenotype?

The assay we used to test for bang-sensitivity has been validated in previous articles from different laboratories. We agree that the recovery times we observed were shorter than those of the BS mutations mentioned by the reviewer. However, we could cite another Drosophila BS mutant, porin, that shows similarly short recovery times (2.5 and 6 sec, according to the porin alleles tested, Graham et al. J Biol Chem. 2010, doi: 10.1074/jbc.M109.080317). This is now mentioned on page 36 lines 717-720). In addition, the BS phenotype we observed with Aprt mutants was robust and highly significant compared to control flies (Figure 7). We did not try to rescue this phenotype by exposing the flies to an antiepileptic, but we do not think that it can be related to the SING phenotype. Indeed, providing adenosine or N6-methyladenosine to Aprt5 mutant flies was able to rescue the BS phenotype (Figure 7E, F), but did not rescue the locomotor defects (new Figure S15). Moreover, SING performances of Aprt5 mutant flies at 8 or 30 d a. E. are decreased nearly in almost identical way (Figure 1C), while we observed an effect on BS behavior at 30 d a. E., which implies that the SING and BS behaviors are most likely unrelated.

Line 731 states that 'Aprt mutants show a typical BS phenotype' - whilst accurate to some extent (e.g. the behaviour depicted in the supp videos), it should be made clear, it should be made clear that the recovery time is uncharacteristically short and thus differs from typical BS mutations.

We have corrected the sentence in the revised article to mention that (page 36, lines 717-718).

Line 732 stating that BS phenotype is often linked to neuronal activity - what other links would there be? Even if via glia or other tissues the final effect is via neurons.

We have modified this sentence (page 36, line 720).

The introduction and, particularly, the discussion are overly long and, in the case of the latter, repetitive of the results text. Pruning to make the paper more concise would be very beneficial. Removal of the extensive speculation about how DA and adenosine may interact would help in this regard (line 688 onwards). Indeed, in many places the discussion morphs into a review.

We agree with the reviewer on this point, and have therefore done our best to shorten the Introduction and Discussion, which are now 24% and 21% shorter, respectively, in the revised article compared to the original submission.

The applicability of using Drosophila Aprt mutations to screen for compounds that may treat LND is predicated on some degree of similarity in either enzyme structure or metabolic pathways. A discussion of how relevant, therefore, studying Aprt is needs to be included. Given the authors insights - where should potential new rugs be targeted to?

As stated above, we now mention in the article that APRT and HGPRT share similarities in their structure. In addition, the metabolic pathways between humans and Drosophila have been largely conserved (shown in Figure S1B).

Author Response

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

We thank the editors and reviewers for their tremendously helpful comments. We outline below changes we have made to the manuscript in response to each point. These include new analyses and a substantial rewrite to address the concerns about lack of clarity.

We believe the revisions strengthen the evidence for our conclusion that grid fields can be either anchored to or independent from a task reference frame, and that anchoring is selectively associated with successful path integration-dependent behaviour. Our additional analyses of non-grid cells indicate that while some are coherent with the grid population, many are not, suggesting cell populations within the MEC may implement grid-dependent and grid-independent computations in parallel.

We hope the reviewers will agree that our novel experimental strategy complements and avoids limitations of perturbation-based approaches, and by providing evidence to dissociate the two major hypotheses for whether and when grid cells contribute to behaviour our results are likely to have a substantial impact on the field.

Public Reviews:

Reviewer #1 (Public Review):

In this study, Clark et. al. uncovered an association between the positional encoding of grid cell activity with good performance in spatial navigation tasks that requires path integration, highlighting the contribution of grid firing to behaviour… The conclusions of this paper are mostly well supported by data, the finding about the association between grid cell encoding and behaviour in spatial memory tasks is important. However, some aspects of the analysis need to be clarified or extended.

Thankyou for the overview and constructive comments.

(1) While the current dataset aims to demonstrate a "correlation" between grid cell encoding and task performance, the other variables that could confound this correlation should be carefully examined.

(1.1) The exact breakdown of the fraction of beaconed/non-beaconed/probe trials is never shown. if the session makeup has a significant effect on the coding scheme or other results, this variable should be accounted for.

The lack of information about the trial organisation was a substantial oversight in our preparation of the first version of the manuscript. Session make up can not account for effects on grid stability and its relationship to behavioural outcome but this was not made at all clear.

In all sessions trial types were varied in a fixed repeating sequence. Therefore, continuous blocks of trials on which grid firing is anchored (or independent from) the track can not be explained by the mouse experiencing a particular trial type. We have revised the manuscript to make this clearer, e.g. p 5, ‘These switches could not be explained by variation between trials in the availability of cues or rewards, as these were interleaved in blocks that repeated throughout a session (see Methods), whereas periods in which grid cell activity was in a given mode extended across the repeating blocks (e.g. Figures 3D,E, 4A, 5E,F).’ and methods p 12, ‘Trials were delivered in repeating blocks throughout a recording session…’

(1.2) The manuscript did not provide information about whether individual mice experienced sessions with different combinations of the three trial types, and whether they show different preferences in position or distance encoding even in comparable sessions. This leads to the question of whether different behaviour and activity encoding were dominated by experimental or natural differences between individual mice. Presenting the data per mouse will be helpful.

As we note above, because trial types were interleaved in a fixed sequence, experience of a particular trial type can not account for switching between task-anchored and taskindependent firing modes. This was insufficiently clear in the first version of the manuscript.

We varied the proportions of trials of a particular type between sessions with the aim of maximising the number of non-beaconed and probe trials. This was necessary because we find that if we introduce too high a proportion of these trials early in training then mice appear to ‘lose interest’ in the task and their performance drops off. We therefore used an approach in which we increased the proportions of non-beaconed and probe trials over training days as mice became familiar with the task. This is now described in the methods (p 12).

Because the decision for when to vary the proportion of trial types was based on the previous day’s performance, the experimental design was not optimised for addressing the reviewer’s question about dissociating experimental from natural differences in mice. To provide some initial insight we have analysed the relationship between task anchored coding and proportion of beaconed trials in a session (Figure 3, Figure Supplement 7). While on average there is a higher proportion of trials in which grid fields are task-anchored in sessions with more beaconed trials, this effect is small and most of the variance is independent from the proportion of beaconed trials.

(1.3) Related to the above point, in Figure 5, the mice appeared to behave worse in probe trials than non-beaconed trials. If the mouse did not know if a trial is a probe or a non-beacon trial, they should behave equivalently until the reward location and thus should stop an equal amount. If this difference is because multiple probe trials are placed consecutively, did the mouse learn that it will not get a reward and then stop trying to get rewards? Did this affect switching between position and distance coding?

Thankyou for flagging this. This reflected an inconsistency arising from the way we detected stops that we have now corrected. Briefly, the temporal resolution of the processed location data against which the stop detection threshold was applied was insufficiently high. As a result, stops in the non-beaconed group were picked up, as they tended to be longer because mice remained still to consume rewards, whereas some stops in the probe group were missed because they were relatively short. We have corrected this by repeating the analyses on raw position data at the highest temporal resolution available. This analysis is now clearly described in the Methods (see p13 “A stop was registered in Blender3D if the speed of the mouse dropped below 4.7 cm/s. Speed was calculated on a rolling basis from the previous 100 ms at a rate of 60 Hz.”).

(1.4) It is not shown how the behaviours (e.g., running speed away from the reward zone, licking for reward) in beaconed/non-beaconed/probe trials were different and whether the difference in behaviours led to the different encoding schemes.

Because trial types were interleaved and repeated with a period less than the length of typical trial sequences during which grid cell activity remained either task-anchored or taskindependent, differences between trial types are unlikely to explain use of the different coding schemes. Hopefully, this is clarified by the comments above.

To further describe the relationship between behavioural outcomes, trial types and grid anchoring, we now also show running speed as a function of location for each combination of trial types and trial outcomes (Figure 6, Figure Supplement 1). This illustrates and replicates our previous findings (Tennant et al. 2018) that running speed profiles are similar for a given trial outcome regardless of trial type (Figure 6, Figure Supplement 1A), and further further shows that the behavioural profile for a given trial outcome and trial-type does not differ when grid cells are in task-anchored and task-independent modes (Figure 6, Figure Supplement 1B). This further argues against the possibility that difference in behaviours leads to the different encoding schemes.

(2) Regarding the behaviour and activity encoding on a trial-by-trial basis, did the behavioural change occur first, or did the encoding switch occur first, or did they happen within the same trial? This analysis will potentially determine whether the encoding is causal for the behaviour, or the other way around.

This is a good question but our experimental design lacks sufficient statistical power to address the timing of mode switches within a trial. This is because mode switching is relatively infrequent (so the n for switching is low) and only a subset of trials are uncued (making the relevant n even lower), while at a trial level the behavioural outcome is variable (increasing the required n for adequate power).

(3) The author determined that the grid cell coding schemes were limited to distance encoding and position encoding. However, there could be other schemes, such as switching between different position encodings (with clear spatial fields but at different locations), as indicated by Low et. al., 2021, and switching between different distant encodings (with different distance periods). If these other schemes indeed existed in the data, they might contribute to the variation of the behaviours.

Switching between position encoding schemes appears to be rare within our dataset and unlikely to contribute to variation in behaviour. In most sessions we did not observe switching between grid phases / position encodings (e.g. Figures 2A-B, 3B-E, 4A, 5C-D, F). In one session we found switching between different phases when grid cells were taskanchored. Because the grid period was unchanged, the spatial periodograms remained similar. We report this example in the revised manuscript (Figure 5E).

(4) The percentage of neurons categorised in each coding scheme was similar between nongrid and grid cells. This implies that non-grid cells might switch coding schemes in sync with grid cells, which would mean the whole MEC network was switching between distance and position coding. This raises the question of whether the grid cell coding scheme was important per se, or just the MEC network coding scheme.

We very much appreciate this suggestion. We note first that while the proportion of taskanchored grid and non-grid cells is similar, task-independent periodic firing of non-grid cells is much rarer than for grid cells (Figure 2E), suggesting a dissociation between the populations. To further address the question we have included additional analyses of nongrid cells (Figure 3, Figure Supplement 5). This shows that while some non-grid cells have anchoring that switches coherently with simultaneously recorded grid cells, others do not. Figures 4 and 5 now show examples of non-grid cell activity recorded simultaneously with grid cells.

Together, our data suggest that the MEC implements multiple coding schemes: one that is associated with the grid network and includes some non-grid cells; and one (or more) that can be independent from the grid network. This dissociation adds to the insights into MEC function that are provided by our study and is now highlighted in the abstract and discussion.

(5) In Figure 2 there are several cell examples that are categorised as distance or position coding but have a high fraction of the other coding scheme on a per-trial basis. Given this variation, the full session data in F should be interpreted carefully, since this included all cells and not just "stable" coding cells. It will be cleaner to show the activity comparison only between the stable cells.

We have now included examples in Figure 2A-C where the grid mode is stable throughout a session. As the view of activity at a session level is important, we have not updated Figure 2F, but have clarified the terminology to now clearly refer to classification at either season or trial levels. In addition, we have repeated the analyses shown in Figure 2F but after grouping cells according to whether their firing has a single mode on >85% of the trials (Figure 3 Figure Supplement 4). This analysis supports similar conclusions to those of Figure 2F.

(6) The manuscript is not well written. Throughout the manuscript, there are many unexplained concepts (especially in the introduction) and methods, mis-referenced figures, and unclear labels.

We very much appreciate the feedback and have substantially rewritten the manuscript. We have paid particular attention to explaining key concepts in the introduction and have carefully checked the figures. We welcome further feedback on whether this is now clearer.

Reviewer #2 (Public Review):

Clark and Nolan's study aims to test whether the stability of grid cell firing fields is associated with better spatial behaviour performance on a virtual task… This study is very timely as there is a pressing need to identify/delimitate the contribution of grid cells to spatial behaviours. More studies in which grid cell activity can be associated with navigational abilities are needed.

Thank you for the supportive comments and highlighting the importance of the question.

The link proposed by Clark and Nolan between "virtual position" coding by grid cells and navigational performance is a significant step toward better understanding how grid cell activity might support behaviour. It should be noted that the study by Clark and Nolan is correlative. Therefore, the effect of selective manipulations of grid cell activity on the virtual task will be needed to evaluate whether the activity of grid cells is causally linked to the behavioural performance on this task. In a previous study by the same research group, it was shown that inactivating the synaptic output of stellate cells of the medial entorhinal cortex affected mice's performance of the same virtual task (Tennant et al., 2018). Although this manipulation likely affects non-grid cells, it is still one of the most selective manipulations of grid cells that are currently available.

Again, thank you for the supportive comments. We recognise the previous version of the manuscript did not sufficiently clarify the motivation for our approach, or the benefits of capitalising on behavioural variable variability as a complementary strategy to perturbation approaches. We now make this clearer in the revised introduction (p 2, paragraphs 2 and 3).

When interpreting the "position" and "distance" firing mode of grid cells, it is important to appreciate that the "position" code likely involves estimating distance. The visual cues on the virtual track appear to provide mainly optic flow to the animal. Thus, the animal has to estimate its position on the virtual track by estimating the distance run from the beginning of the track (or any other point in the virtual world).

We appreciate the ambiguity here was confusing. We have re-named the groups to ‘taskanchored’, corresponding to when grid cells encode position on the track (as well as distance as the reviewer correctly points out), and ‘task-independent’, corresponding to the group we previously referred to as distance encoding.

It is also interesting to consider how grid cells could remain anchored to virtual cues. Recent work shows that grid cell activity spans the surface of a torus (Gardner et al., 2022). A run on the track can be mapped to a trajectory on the torus. Assuming that grid cell activity is updated primarily from self-motion cues on the track and that the grid cell period is unlikely to be an integer of the virtual track length, having stable firing fields on the virtual track likely requires a resetting mechanism taking place on each trial. The resetting means that a specific virtual track position is mapped to a constant position on the torus. Thus, the "virtual position" mode of grid cells may involve 1) a trial-by-trial resetting process anchoring the grid pattern to the virtual cues and 2) a path integration mechanism. Just like the "virtual position" mode of grid cell activity, successful behavioural performance on non-beaconed trials requires the animal to anchor its spatial behaviour to VR cues.

Reviewer #3 (Public Review):

This study addresses the major question of 'whether and when grid cells contribute to behaviour'. There is no doubt that this is a very important question. My major concern is that I'm not convinced that this study gives a significant contribution to this question, although this study is well-performed and potentially interesting. This is mainly due to the fact that the relation between grid cell properties and behaviour is exclusively correlative and entirely based on single cell activity, although the introduction mentions quite often the grid cell network properties and dynamics. In general, this study gives the impression that grid cells exclusively support the cognitive processes involved in this task. This problem is in part related to the text.

Thank you for the comments. We recognise now that the previous text was insufficiently clear. We have modified the introduction to clarify the value of an approach that takes advantage of behavioural variability. Importantly, this approach is complementary to perturbation strategies we and others have used previously. In particular it addresses critical limitations of perturbation strategies which can be confounded by off-target effects and possible adaptation, both of which are extremely difficult to fully rule out. We hope that with this additional clarification it is now clear that as for any important question multiple and complementary testing strategies are required to make progres, and second, that our study makes a new and important contribution by introducing a novel experimental approach and by following this up with careful analyses that clearly distinguish competing hypotheses.

However, it would be interesting to look at the population level (even beyond grid cells) to test whether at the network level, the link between behavioural performance and neural activity is more straightforward compared to the single-cell level. This approach could reconcile the present results with those obtained in their previous study following MEC inactivation.

We’re unclear here about what the reviewer means by ‘more straightforward’ as clear relationships between activity of single grid cells and populations of grid cells are well established (Gardner et al., 2021; Waaga et al., 2021; Yoon et al., 2013).

To give a clearer indication of the corresponding population level representations, as mentioned in response to Reviewer #1, we now include additional data showing many simultaneously recorded neurons, and analyses of non-grid as well as grid cells (Figures 4, 5, Figure 5 Figure Supplement 2).

To reconcile results with our previous study of MEC inactivation we have paid additional attention to the roles of non-grid cells (following suggestions by Reviewer #1). We show that while some non-grid cells show transitions between task-anchored and task-independent firing that are coherent with the grid population, many others have more stable firing that is independent of grid representations. This is consistent with the idea that the MEC supports localised behaviour in the cued and uncued versions of the task (Tennant et al., 2018), and suggests that while grid cells preferentially contribute when cues are absent, non-grid cells could also support the cued version. We make this additional implication clear in the revised abstract and discussion.

The authors used a statistical method based on the computation of the frequency spectrum of the spatial periodicity of the neural firing to classify grid cells as 'position-coding' (with fields anchored to the virtual track) and 'distance-coding' (with fields repeating at regular intervals across trials). This is an interesting approach that has nonetheless the default to be based exclusively on autocorrelograms. It would be interesting to compare with a different method based on the similarities between raw maps.

While our main analyses use a periodogram-based method to identify when grid cells are / are not anchored to the task environment, we validate these analyses by examination of the rate maps in each condition (Figures 2-4). For example, when grid cells are task-anchored, according to the periodogram analysis, the rate maps clearly show spatially aligned peaks, whereas when grid cells are not anchored the peaks in their rate maps are not aligned (Figure 2A vs 2B; Figure 3B-E; Figure 4C). We provide further validation by showing that spatial information (in the track reference frame) is substantially higher when grid cell activity is task-anchored vs task-independent (Figures 2F, 3G, 4F and Figure 3 Figure Supplement 4).

To further address this point we have carried out additional complementary analyses in which we identify task anchored vs task independent modes using a template matching method applied to the raw rate maps (Figure 6, Figure Supplement 2). These analyses support similar conclusions to our periodogram-based analyses.

Beyond this minor point, cell categorization is performed using all trial types.

Each trial type (i.e. beacon or non-beacon) is supposed to force mice to use different strategies and should induce different spatial representations within the entorhinal-hippocampal circuit (and not only in the grid cell system). In that context, since all trials are mixed, it is difficult to extrapolate general information.

We recognise that the description of the task design was insufficiently clear but are unsure why ‘it is difficult to extrapolate general information’. Before addressing this point, we should first be clear that mice are not ‘forced’ to adopt any particular strategy. Rather, on uncued trials a path integration strategy is the most efficient way to solve the task. However, mice could instead use a less efficient strategy, for example by stopping at short intervals they still obtain rewards. Detailed behavioural analyses indicate that such random stopping strategies are used by naive mice, while with training mice learn to use spatial stopping strategies (Tennant et al. 2018).

In terms of ‘extracting general information’ from the task, the following findings lead to general predictions: 1) Grid cells can exist in either task-anchored or task-independent periodic firing modes; 2) These modes can be stable across a session, but often modeswitching occurs within a session; 3) While some non-grid cells show task-independent periodic firing, this is much less common than for grid cells, which suggests a model in which many non-grid MEC neurons operate independently from the grid network; 4) When a marker cue is available mice locate a reward equally well when grid cells are in taskanchored versus task-independent modes, which argues against theories in which grid cells are a key part of a general system for localisation; 5) When markers cues are absent taskanchored grid firing is associated with successful reward localisation, which corroborates a key prediction of theories in which grid cells contribute to path integration.

In revising the manuscript we have attempted to improve the writing to make these advances clearer, and have clarified methodological details that made interpretation more challenging than it should have been. For example, as noted in our response to Reviewer #1, we have included additional details to clarify the organisation of trials and relationships between trials, behavioural outcomes and neural codes observed.

On page 5 the authors state that 'Since only position representations should reliably predict the reward location, ..., we reasoned that the presence of positional coding could be used to assess whether grid firing contributes to the ongoing behaviour'. I do not agree with this statement. First of all, position coding should be more informative only in a cue-guided trial. Second, distance coding could be as informative as position coding since at the network level may provide information relevant to the task (such as distance from the reward).

Again, this point perhaps reflects a lack of clarity on our part in writing the manuscript. When grid cells are anchored to the track reference frame (now called ‘tasked anchored’, previously ‘position encoding’), then the location of the rate peaks in grid firing is reliable from trial to trial. This is the case whether or not the trial is cued. When grid cells are independent of the track reference frame (now called ‘task independent’, previously ‘distance encoding’), then the location of the firing rate peaks vary from trial to trial. In the latter case, position can not be read out directly from trial to trial.

In principle, in the task-independent mode track position could be calculated by storing the grid network configuration at the start of the track, which would differ on each trial, and then implementing a mechanism to readout relative distance as mice move along the track. However, if mice do use this computation we would expect them to do so equally well on cued and uncued trials. By contrast, our results clearly show a dissociation between trial types in the relationship between grid firing and behavioural outcome. We highlight and discuss this possibility in the revised manuscript (p 10, ‘Alternatively, mice could in principle estimate track location with a system that utilises information about distance travelled obtained from task-independent grid representations’).

Third, position-coding is interpreted as more relevant because it predominates in correct trials. However, this does not imply that this coding scheme is indeed used to perform correct trials.

We have revised the manuscript to clarify our goal of distinguishing major hypotheses for the roles of grid cells in behaviour (Introduction, ‘On the one hand, theoretical arguments that grid cell populations can generate high capacity codes imply that they could in principle contribute to all spatial behaviours (Fiete et al., 2008; Mathis et al., 2012; Sreenivasan and Fiete, 2011). On the other hand, if the behavioural importance of grid cells follows from their hypothesised ability to generate position representations by integrating self-motion signals (McNaughton et al., 2006), then their behavioural roles may be restricted to tasks that involve path integration strategies.’

By showing that performance on cued trials is similar regardless of whether grid cells are task-anchored or not, we provide strong evidence against the idea that grid firing is in general necessary for location-based behaviours. By showing that task anchoring is associated with successful localisation when cues are absent we corroborate a key prediction of hypothesised roles for grid cells in path integration-dependent behaviour. Therefore, we substantially reduce the space of behaviours to which grid cells might contribute. Importantly, this space is much larger for the MEC, which is required for cued and uncued versions of the task. We have revised the introduction and discussion to make these points clearer.

While we believe our results add a key piece of evidence to the puzzle of when and where grid cells contribute to behaviour, we agree that further work will be required to develop and test more refined hypotheses. Alternative models also remain plausible, for example perhaps the behaviourally relevant computations are implemented elsewhere in the brain with grid anchoring to the track as an indirect consequence. Nevertheless, explanations of this kind are more difficult to reconcile with evidence that inactivation of stellate cells in the MEC impairs learning of the task, and other manipulations that modify grid firing impair performance on similar tasks. We now discuss these possibilities (discussion p 10, ‘mice could in principle estimate track location with a system that utilises information about distance travelled obtained from task-independent grid representations’).

It could be more informative to push forward the correlative analysis by looking at whether behavioural performance can be predicted by the coding scheme on a trial-by-trial basis.

The previous version of the manuscript showed these analyses (now in Figure 6). Thus, task anchored grid firing predicts more successful performance on uncued trials at the session level (Figure 6A-B) and at the trial level (Figure 6C-D).

Reviewer #1 (Recommendations For The Authors):

(1) The author particularly mentioned that the 1D tracks are different from the "cue-rich environments that are typically used to study grid cells". It is not clear what conclusions would hold for a cue-rich environment or a track, which may require relatively less path integration compared to the cue-sparse environment. This point should be discussed.

This is an important point that we did not pay sufficient attention to in the previous version of the manuscript. Our finding of successful localisation in the cued environment when grid cells are not task anchored implies that grid anchoring is not required to solve cued tasks. The implication here is that cue rich environments may then not be the most suitable for investigation of grid roles in behaviour as non-grid mechanisms may suffice, although this does not rule out the possibility that anchored grid codes may play important roles in learning about cue rich environments. We now address this point in the discussion (p 10, ‘An implication of this result is that cue rich tracks often used to investigate grid activity patterns may not engage behaviours that require anchored grid firing.’).

(2) It would be good to see the statistics for the number of different cells (stable position or distance encoding, and unstable cells) identified per mouse/session and the number of grid cells per session.

These are now added to Supplemental Data 2 and will also be accessible through code and datasets that we will make available alongside the version of record.

(3) Figure 2F: any explanation about why AG cells had high spatial information?

Previously the calculation used bits per spike and as aperiodic cells have low firing rates the spatial information was high. We have replaced this with bits per second, which provides a more intuitive measure and no longer implies high spatial information. We have amended this in the methods (p 15, ‘Spatial information was calculated in bits per second…’).

(4) The following methods sections should provide additional details:

(4.1) Details of the training protocol are largely left to reference papers. The reference papers give a general outline of the training protocol, but the details are not completely comparable given the single experiment performed on these mice. More details should be given on training stages and experience at the time of the experiment.

The task is more clearly described in the introduction (p 3), and additional details of the training protocol are now provided in the methods (p 12-13).

(4.2) The methods reference mean speed across sessions, but it is not clear where this was used.

This was very poor wording. We have now changed this to ‘For each session the mean speed was calculated for each trial outcome’.

(4.3) The calculation of the spatial autocorrelogram on a per-trial basis should be more explicitly stated. Is it the average of each 10 cm increment with the centre trial?

We have added additional information to the methods (p 16-18).

(4.4) 1D field detection is not sufficiently explained in Figure 1/S2. This information should also appear in the methods section.

This is now clarified on page 16 in section ‘Analysis of neural activity and behaviour during the location memory task’.

(5) The data in Figure 4A and B only shows speed vs. location for one example mouse. The combined per mouse or per session data should also be shown.

This is now shown in Figure 5A and Figure 5, Figure Supplemental 2

(6) Figure 5 is somewhat confusing. Why are A/B by session and C/D by trial? The methods imply that A/B are originally averaged by cell, but that duplicate cells in the same session are excluded because behaviour versus session type is identical. This method should be valid if all grid cells within a session are all "stable". This is likely given the synchrony of code-switching between grid cells, but not all co-active grid cells behaved identically.

It is understandable that C/D are performed by trial, but it should be made clear that it is not a comparable analysis to A/B. It is unclear what N refers to in C. The figure says by trial, but the legend says the error bar is by cell. If data is calculated by trial and then averaged by cell, this should be more clearly stated.

In Figure 6A/B (previously Figure 5A/B) we focus our analysis on sessions in which the mode of grid firing, either task-anchored or task-independent, was relatively stable on a trialto-trial basis (see Figure 3F for definitions). This enables us to then compare behaviour averaged across each session, with sessions categorised as task-anchored and task independent. This analysis has the advantage that it focuses on large blocks of time (whole sessions) in which the mode of grid firing is unambiguous, but the disadvantage is that it excludes many sessions in which grid firing switches between task-anchored and taskindependent modes.

Figure 6C/D (previously Figure 5C/D) addresses this limitation by carrying out similar analyses with behaviour sorted into task-anchored versus task-independent groups at the level of trials. A potential limitation for this analysis is that grid firing is somewhat variable on a trial-by-trial basis and so some trials may be mis-classified. We don’t expect this to lead to systematic bias, but it may make the data more noisy. Nevertheless, these analyses are important to include as they allow assessment of whether conclusions from 6A/B hold when all sessions are considered.

We have added additional clarification of the rationale for these analyses to the main text (p7-8, ‘’We addressed this by using additional trial-level comparisons’). We have also added clarification in the methods section for categorisation of task-anchored versus taskindependent trials when multiple grid cells were recorded simultaneously (p 17, ‘When assigning a common classification across a group of cells recorded simultaneously...’) and an explanation for the N in the figure legend. We also clarify that the analyses use a nested random effects design to account for dependencies at the levels of sessions and mice (methods, p 20, ‘Random effects had a nested structure to account for animals and sessions…’) .

(7) Panels E and F of Figure 5 are not explained in the main text.

This is now corrected (see p8, ‘Additional analyses…’).

(8) Figure 5: Since stable grid cells and all grid cells are shown, it will be better to show unstable cells, which can be compared with grid cells.

Given that the rationale for differences between Figure 6A/B and C/D (previously Figure 5AD) were not previously clear, the reason for focussing on stable grid cells here was likely also not clear (see point 6 above). We don’t show unstable grid cells in Figure 6A-B as the behaviour averaged at the level of a session would be a mix of trials when they are taskanchored and when they are task-independent. Therefore, the analysis would not test predictions about the relationship between task-anchored vs task-independent modes and behaviour. We hope this is now clear in the manuscript given the revisions introduced to address point 6 above.

(9) The methods describing the statistics for these experiments are also confusing. The methods section should be written more clearly, and it should be made clear in the text or figure legend whether this data is the "original" data or is processed in relation to the model, such as excluding duplicate grid cells within a session. The figure legend should also state that a GLMM was used to calculate the statistics.

We have revised the methods section with the goal of improving clarity, adding detail and removing ambiguity. This includes updates of the methods for the GLMM analysis, which are referred to within the Figure 6 legend. A clear definition of a stable session is now also added to the Figure 6 legend.

Reviewer #2 (Recommendations For The Authors):

When grid fields are anchored to the virtual world (position mode), there is probably small trialto-trial variability in the firing location of the firing fields. Is this trial-to-trial variability related to the variability in the stop location? This would provide a more direct link between path integration in grid cell networks and behaviour that depends on path integration.

When attempting to address this we find that the firing of individual grid cells is too variable to allow sufficiently precise decoding of their fields at a single trial level. This is expected given the Poisson statistics of spike generation and previous evaluations of grid coding (e.g. (Stemmler et al., 2015)).

The conclusion of the abstract is: "Our results suggest that positional anchoring of grid firing enhances the performance of tasks that require path integration." This statement is slightly confusing. The task requires 1) anchoring the behaviour to the visual cues presented at the start of the trial and 2) path integration from thereon to identify the rewarded location. The performance is higher when grid cells anchor to the visual cues presented at the start of the trial. What the results show is that the anchoring of grid firing fields to visual landmarks enhances the performance of tasks that require path integration from visual landmarks (i.e. grid cells being anchored to the reference frame that is behaviorally relevant).

To try to more clearly explain the logic and conclusion we have rewritten the abstract, including the final sentence.

Similar comment for the title of Figure 5: "Positional grid coding is not required for cued spatial localisation but promotes path integration-dependent localisation." Positional coding means that grid cells are anchored to the behaviorally relevant reference frame.

To address the lack of clarity we have modified the little of Figure 6 (previously Figure 5) to read ‘Anchoring of grid firing to the task reference frame promotes localisation by path integration but is not required for cued localisation’.

In Figure 1, there is a wide range of beaconed (40-80%) and non-beaconed (10-60%) trials given. It is not 100% clear whether these refer to the percentage of trials of a given type within the recording sessions. Was the proportion of non-beaconed trials manipulated? If so, was the likelihood of position and distance coding changing according to the percentage of nonbeaconed trials?

The ranges given refer to proportions across different behavioural sessions. Within any given behavioural session the proportion was constant. We now make this clear in the figure legend and in the results and methods sections.

We did not manipulate proportions of trial types during a session. Manipulations betweens sessions were carried out with the goal of maximising the numbers of uncued trials that the mice would carry out (see response to public comments above). While the effect of trial-type at the session level is not relevant to the hypotheses we aim to test here, we have included an additional analysis of the relationship between task anchoring and the proportions of trial types in a session (Figure 3, Figure Supplement 7)(also discussed above). As disentangling the effects of learning and motivation will be complex and likely require new experimental designs we have not drawn strong conclusions or pursued the analysis further..

I was not convinced that the labels "position" and "distance" were appropriate for the two grid cell firing modes. My understanding is that the "position" code also requires the grid cell network to estimate distance. It seems that the main difference between the "position" and "distance" modes is that when in the "position" mode, the activity on the torus is reset to a constant toroidal location when the animal reaches a clearly identifiable location on the virtual track. In the "distance" mode, this resetting does not take place.

As previously mentioned, we agree these terms weren’t the best and have since relabelled these as “task-anchored” and “task-independent”.

There are a few sections in the manuscript that implicitly suggest that a causal link between grid cell activity and behaviour was demonstrated. For instance: "It has been challenging to directly test whether and when grid cells contribute to behaviour.": The assumption here is that the manuscript overcomes this challenge, but the study is correlative.

We have modified the wording to be clear that we are introducing new tests of predictions made by hypotheses about causal relationships between grid coding and behaviour (introduction, p 1-2). We also clarify that our results argue against the hypothesis that grid cells provide a general coded for behaviour, but corroborate predictions of hypotheses in which they are specifically important for path integration (discussion, p 10).

We have modified the title abstract and main text to try to treat claims about causality with care. We now more thoroughly introduce and contrast the approach we report here with previous experiments that use perturbations (introduction, p2). While it is tempting to make stronger claims for causality with these approaches, there are also logical limitations with perturbation-based approaches, for example the challenges of fully excluding off target effects and adaptation. We now explain how these strategies are complementary. Our view is that both strategies will be required to develop strong arguments for whether and when grid cells contribute to behaviour. From this perspective, it is encouraging that our conclusions are in agreement with what are probably the most specific perturbations of grid cells reported to date (Gil et al. 2017), while perturbations that more generally affect MEC function appear to impair cued and path integration-dependent behaviours (Tennant et al. 2018). We now discuss these points more clearly (introduction, p 2).

I am slightly confused by the references to the panels in Figure 4.

"In some sessions, localization of the reward occurred almost exclusively when grid cells were anchored to position and not when they encoded distance (Figure 4C). Figure 4C only shows position coding.

"In other sessions, animals localised the reward when grid firing was anchored to position or distance, but overall performance was improved on positional trials (Figure 4D-E)." The reference should probably point to Figure 4E-F or just to 4E.

"In a few sessions, we observed spatial stopping behaviour comparable to cued trials, even when grid firing almost exclusively encoded distance rather than position (Figure 4F)." From Figure 4F, it seems that the performance on non-beaconed trials is better during "position" coding.

We have now updated Figure 5 (Figure 4 in the original manuscript) and references to the Figure in the text. Now Figure 5 shows the activity of cells recorded in stable and unstable task-anchored and task-independent sessions (see Figure 5C-F).

Minor issues:

Is this correct: (Figure 4A and Figure 4, Figure Supplement 1).

This has been corrected.

Figure 4B: There could be an additional label for position and distance.

Figure 4B from the original manuscript has now been removed.

Figure 4C-F. The panels on the right side should be explained in the Figure Legend.

Legends for Figure 5C-F (previously Figure 4C-F) have now been updated.

Reviewer #3 (Recommendations For The Authors):

Specific questions :

(1) Position coding reflects a coding scheme in which fields are spaced by a fixed distance; previous studies have shown that a virtual track grid map is a slice of the 2D classic grid. In that case, the fields are still anchored to the track but would produce a completely different map. Did the authors check whether it is the case at least for some cells? If not, what could explain such a major difference?

Το avoid confusion we now use the term ‘task-anchored’ rather than ‘position coding’ (see comments above). We should further clarify that our conclusions rest on whether or not the grid fields are anchored to the track. Task anchored firing does not require that grid fields maintain their spacing from 2D environments, only that fields are at the same track position on each trial. Thus, whether the spacing of the fields corresponds to a slice through a 2D grid makes no difference to the hypotheses we test here.

We agree that the relationship between 1D and 2D field organisation could be an interesting future direction, for example anchoring could involve resetting the grid phase while maintaining a stable period, or it could be achieved through local distortions in the grid period. However, since these outcomes would not help distinguish the hypotheses we test here we have not included analyses to address them.

(2) Previous studies have highlighted the role of grid cells in goal coding. Here there is an explicit reward in a particular area. Are there any grid modifications around this area? This question is not addressed in this study.

Again, we note that the hypotheses we test here relate to the firing mode of grid cells - taskanchored or task-independent - and interpretation of our results is independent from the specific pattern of grid fields on the track. This question nevertheless leads to an interesting prediction that if grid fields cluster in the goal area then this clustering should be apparent in the task-anchored but not the task-independent firing mode.

We test this by considering the average distribution of firing fields across all grid cells in each firing mode (Reviewer Figure 1). We find that when grid firing is task-anchored there is a clear peak around the reward zone, which is consistent with previous work by Butler et al. and Boccara et al. Consistent with our other prediction, this peak is reduced when grid cells are in the task-independent mode.

Author response image 1.

Plot shows the grid field distribution during stable grid cell session (> 85 % task-anchored or task-independent) (A) or during task-anchored and task-independent trials (B). Shaded regions in A and B represent standard error of the mean measured across sessions and epochs respectively.

(3) The behavioural procedure during recording is not fully explained. Do trial types alternate within the same session by blocks? How many trials are within a block? Is there any relation between trial alternation and the switch in the coding scheme observed in a large subset of the grid cells?

We agree this wasn’t sufficiently clear in the previous version of the manuscript. Trial types were interleaved in a fixed order within each session. We have updated the results and methods sections to provide details (see responses above).

(4) From the examples in Figure 2 it seems that firing fields tend to shift toward the start position. Is it the case in all cells? Could this reflect some reorganisation at the network level with cells signalling the starting as time progresses?

This is inconsistent between cells. To make this variability clear we have included additional examples of spiking profiles from different grid cells (Figure 2 - 5). Because quantification of the phenomena would not, so far as we can tell, help distinguish our core hypotheses we have not included further analyses here.

(5) Are grid cells with different coding properties recorded in different parts of the MEC? Are there any differences between these cell categories in the 2D map?

The recordings we made are from the dorsal region of the MEC (stated at the start of the results section). We don’t have data to speak to other parts of the MEC.

Minor:

There are very few grid cell examples that repeat in the different figures. I would suggest showing more examples both in the main text and supplementary material.

We have now provided multiple additional examples in Figures 2, 4 and 5. Grid cell examples repeat in the main figures twice, in both cases only when showing additional examples are shown from the same recording session (Figure 2A example #1 with Figure 5C, Figure 3E with Figure 4A). Further similar repeats are found in the supplemental figures (Figure 3D with Figure 5, Figure Supplement 2A, Figure 3C with Figure 5, Figure Supplement 2F).

Fig1 A-B shows the predictions in a 1D track based on distance or position coding. The A inset represents the modification of field distribution from a 2D arena to a 1D track, as performed in this study. The inset B is misleading since it represents the modifications expected from a circular track to a 1D track as in Jacob et al 2019, that is not what the authors studied. It would be better to present either the predictions based on the present study or the prediction based on previous studies. In that case, they should mention the possibility that the 1D map is a slice of the 2D map.

The goal of Figure 1A-B is to illustrate predictions (right) based on conclusions from previous studies (left). Figure 1A shows predicted 1D track firing given anchoring to the environment typically observed in grid cell studies in 2D arenas. Figure 1B shows predicted 1D track firing given the firing shifting firing patterns observed by Jacob et al. in a circular 2D track. To improve clarity, we have modified the legend to make clear that the schematics to the right are predictions given the previous evidence summarised to the left. As we outline above, the critical prediction relates to whether the representations anchor to the track. Whether the 1D representation is a perfect slice isn’t relevant to the hypotheses tested and so isn’t included in the schematic (see comments above).

Author Response

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

We thank the editors and reviewers for their tremendously helpful comments. We outline below changes we have made to the manuscript in response to each point. These include new analyses and a substantial rewrite to address the concerns about lack of clarity.

We believe the revisions strengthen the evidence for our conclusion that grid fields can be either anchored to or independent from a task reference frame, and that anchoring is selectively associated with successful path integration-dependent behaviour. Our additional analyses of non-grid cells indicate that while some are coherent with the grid population, many are not, suggesting cell populations within the MEC may implement grid-dependent and grid-independent computations in parallel.

We hope the reviewers will agree that our novel experimental strategy complements and avoids limitations of perturbation-based approaches, and by providing evidence to dissociate the two major hypotheses for whether and when grid cells contribute to behaviour our results are likely to have a substantial impact on the field.

Public Reviews:

Reviewer #1 (Public Review):

In this study, Clark et. al. uncovered an association between the positional encoding of grid cell activity with good performance in spatial navigation tasks that requires path integration, highlighting the contribution of grid firing to behaviour… The conclusions of this paper are mostly well supported by data, the finding about the association between grid cell encoding and behaviour in spatial memory tasks is important. However, some aspects of the analysis need to be clarified or extended.

Thankyou for the overview and constructive comments.

(1) While the current dataset aims to demonstrate a "correlation" between grid cell encoding and task performance, the other variables that could confound this correlation should be carefully examined.

(1.1) The exact breakdown of the fraction of beaconed/non-beaconed/probe trials is never shown. if the session makeup has a significant effect on the coding scheme or other results, this variable should be accounted for.

The lack of information about the trial organisation was a substantial oversight in our preparation of the first version of the manuscript. Session make up can not account for effects on grid stability and its relationship to behavioural outcome but this was not made at all clear.

In all sessions trial types were varied in a fixed repeating sequence. Therefore, continuous blocks of trials on which grid firing is anchored (or independent from) the track can not be explained by the mouse experiencing a particular trial type. We have revised the manuscript to make this clearer, e.g. p 5, ‘These switches could not be explained by variation between trials in the availability of cues or rewards, as these were interleaved in blocks that repeated throughout a session (see Methods), whereas periods in which grid cell activity was in a given mode extended across the repeating blocks (e.g. Figures 3D,E, 4A, 5E,F).’ and methods p 12, ‘Trials were delivered in repeating blocks throughout a recording session…’

(1.2) The manuscript did not provide information about whether individual mice experienced sessions with different combinations of the three trial types, and whether they show different preferences in position or distance encoding even in comparable sessions. This leads to the question of whether different behaviour and activity encoding were dominated by experimental or natural differences between individual mice. Presenting the data per mouse will be helpful.

As we note above, because trial types were interleaved in a fixed sequence, experience of a particular trial type can not account for switching between task-anchored and taskindependent firing modes. This was insufficiently clear in the first version of the manuscript.

We varied the proportions of trials of a particular type between sessions with the aim of maximising the number of non-beaconed and probe trials. This was necessary because we find that if we introduce too high a proportion of these trials early in training then mice appear to ‘lose interest’ in the task and their performance drops off. We therefore used an approach in which we increased the proportions of non-beaconed and probe trials over training days as mice became familiar with the task. This is now described in the methods (p 12).

Because the decision for when to vary the proportion of trial types was based on the previous day’s performance, the experimental design was not optimised for addressing the reviewer’s question about dissociating experimental from natural differences in mice. To provide some initial insight we have analysed the relationship between task anchored coding and proportion of beaconed trials in a session (Figure 3, Figure Supplement 7). While on average there is a higher proportion of trials in which grid fields are task-anchored in sessions with more beaconed trials, this effect is small and most of the variance is independent from the proportion of beaconed trials.

(1.3) Related to the above point, in Figure 5, the mice appeared to behave worse in probe trials than non-beaconed trials. If the mouse did not know if a trial is a probe or a non-beacon trial, they should behave equivalently until the reward location and thus should stop an equal amount. If this difference is because multiple probe trials are placed consecutively, did the mouse learn that it will not get a reward and then stop trying to get rewards? Did this affect switching between position and distance coding?

Thankyou for flagging this. This reflected an inconsistency arising from the way we detected stops that we have now corrected. Briefly, the temporal resolution of the processed location data against which the stop detection threshold was applied was insufficiently high. As a result, stops in the non-beaconed group were picked up, as they tended to be longer because mice remained still to consume rewards, whereas some stops in the probe group were missed because they were relatively short. We have corrected this by repeating the analyses on raw position data at the highest temporal resolution available. This analysis is now clearly described in the Methods (see p13 “A stop was registered in Blender3D if the speed of the mouse dropped below 4.7 cm/s. Speed was calculated on a rolling basis from the previous 100 ms at a rate of 60 Hz.”).

(1.4) It is not shown how the behaviours (e.g., running speed away from the reward zone, licking for reward) in beaconed/non-beaconed/probe trials were different and whether the difference in behaviours led to the different encoding schemes.

Because trial types were interleaved and repeated with a period less than the length of typical trial sequences during which grid cell activity remained either task-anchored or taskindependent, differences between trial types are unlikely to explain use of the different coding schemes. Hopefully, this is clarified by the comments above.

To further describe the relationship between behavioural outcomes, trial types and grid anchoring, we now also show running speed as a function of location for each combination of trial types and trial outcomes (Figure 6, Figure Supplement 1). This illustrates and replicates our previous findings (Tennant et al. 2018) that running speed profiles are similar for a given trial outcome regardless of trial type (Figure 6, Figure Supplement 1A), and further further shows that the behavioural profile for a given trial outcome and trial-type does not differ when grid cells are in task-anchored and task-independent modes (Figure 6, Figure Supplement 1B). This further argues against the possibility that difference in behaviours leads to the different encoding schemes.

(2) Regarding the behaviour and activity encoding on a trial-by-trial basis, did the behavioural change occur first, or did the encoding switch occur first, or did they happen within the same trial? This analysis will potentially determine whether the encoding is causal for the behaviour, or the other way around.

This is a good question but our experimental design lacks sufficient statistical power to address the timing of mode switches within a trial. This is because mode switching is relatively infrequent (so the n for switching is low) and only a subset of trials are uncued (making the relevant n even lower), while at a trial level the behavioural outcome is variable (increasing the required n for adequate power).

(3) The author determined that the grid cell coding schemes were limited to distance encoding and position encoding. However, there could be other schemes, such as switching between different position encodings (with clear spatial fields but at different locations), as indicated by Low et. al., 2021, and switching between different distant encodings (with different distance periods). If these other schemes indeed existed in the data, they might contribute to the variation of the behaviours.

Switching between position encoding schemes appears to be rare within our dataset and unlikely to contribute to variation in behaviour. In most sessions we did not observe switching between grid phases / position encodings (e.g. Figures 2A-B, 3B-E, 4A, 5C-D, F). In one session we found switching between different phases when grid cells were taskanchored. Because the grid period was unchanged, the spatial periodograms remained similar. We report this example in the revised manuscript (Figure 5E).

(4) The percentage of neurons categorised in each coding scheme was similar between nongrid and grid cells. This implies that non-grid cells might switch coding schemes in sync with grid cells, which would mean the whole MEC network was switching between distance and position coding. This raises the question of whether the grid cell coding scheme was important per se, or just the MEC network coding scheme.

We very much appreciate this suggestion. We note first that while the proportion of taskanchored grid and non-grid cells is similar, task-independent periodic firing of non-grid cells is much rarer than for grid cells (Figure 2E), suggesting a dissociation between the populations. To further address the question we have included additional analyses of nongrid cells (Figure 3, Figure Supplement 5). This shows that while some non-grid cells have anchoring that switches coherently with simultaneously recorded grid cells, others do not. Figures 4 and 5 now show examples of non-grid cell activity recorded simultaneously with grid cells.

Together, our data suggest that the MEC implements multiple coding schemes: one that is associated with the grid network and includes some non-grid cells; and one (or more) that can be independent from the grid network. This dissociation adds to the insights into MEC function that are provided by our study and is now highlighted in the abstract and discussion.

(5) In Figure 2 there are several cell examples that are categorised as distance or position coding but have a high fraction of the other coding scheme on a per-trial basis. Given this variation, the full session data in F should be interpreted carefully, since this included all cells and not just "stable" coding cells. It will be cleaner to show the activity comparison only between the stable cells.

We have now included examples in Figure 2A-C where the grid mode is stable throughout a session. As the view of activity at a session level is important, we have not updated Figure 2F, but have clarified the terminology to now clearly refer to classification at either season or trial levels. In addition, we have repeated the analyses shown in Figure 2F but after grouping cells according to whether their firing has a single mode on >85% of the trials (Figure 3 Figure Supplement 4). This analysis supports similar conclusions to those of Figure 2F.

(6) The manuscript is not well written. Throughout the manuscript, there are many unexplained concepts (especially in the introduction) and methods, mis-referenced figures, and unclear labels.

We very much appreciate the feedback and have substantially rewritten the manuscript. We have paid particular attention to explaining key concepts in the introduction and have carefully checked the figures. We welcome further feedback on whether this is now clearer.

Reviewer #2 (Public Review):

Clark and Nolan's study aims to test whether the stability of grid cell firing fields is associated with better spatial behaviour performance on a virtual task… This study is very timely as there is a pressing need to identify/delimitate the contribution of grid cells to spatial behaviours. More studies in which grid cell activity can be associated with navigational abilities are needed.

Thank you for the supportive comments and highlighting the importance of the question.

The link proposed by Clark and Nolan between "virtual position" coding by grid cells and navigational performance is a significant step toward better understanding how grid cell activity might support behaviour. It should be noted that the study by Clark and Nolan is correlative. Therefore, the effect of selective manipulations of grid cell activity on the virtual task will be needed to evaluate whether the activity of grid cells is causally linked to the behavioural performance on this task. In a previous study by the same research group, it was shown that inactivating the synaptic output of stellate cells of the medial entorhinal cortex affected mice's performance of the same virtual task (Tennant et al., 2018). Although this manipulation likely affects non-grid cells, it is still one of the most selective manipulations of grid cells that are currently available.

Again, thank you for the supportive comments. We recognise the previous version of the manuscript did not sufficiently clarify the motivation for our approach, or the benefits of capitalising on behavioural variable variability as a complementary strategy to perturbation approaches. We now make this clearer in the revised introduction (p 2, paragraphs 2 and 3).

When interpreting the "position" and "distance" firing mode of grid cells, it is important to appreciate that the "position" code likely involves estimating distance. The visual cues on the virtual track appear to provide mainly optic flow to the animal. Thus, the animal has to estimate its position on the virtual track by estimating the distance run from the beginning of the track (or any other point in the virtual world).

We appreciate the ambiguity here was confusing. We have re-named the groups to ‘taskanchored’, corresponding to when grid cells encode position on the track (as well as distance as the reviewer correctly points out), and ‘task-independent’, corresponding to the group we previously referred to as distance encoding.

It is also interesting to consider how grid cells could remain anchored to virtual cues. Recent work shows that grid cell activity spans the surface of a torus (Gardner et al., 2022). A run on the track can be mapped to a trajectory on the torus. Assuming that grid cell activity is updated primarily from self-motion cues on the track and that the grid cell period is unlikely to be an integer of the virtual track length, having stable firing fields on the virtual track likely requires a resetting mechanism taking place on each trial. The resetting means that a specific virtual track position is mapped to a constant position on the torus. Thus, the "virtual position" mode of grid cells may involve 1) a trial-by-trial resetting process anchoring the grid pattern to the virtual cues and 2) a path integration mechanism. Just like the "virtual position" mode of grid cell activity, successful behavioural performance on non-beaconed trials requires the animal to anchor its spatial behaviour to VR cues.

Reviewer #3 (Public Review):

This study addresses the major question of 'whether and when grid cells contribute to behaviour'. There is no doubt that this is a very important question. My major concern is that I'm not convinced that this study gives a significant contribution to this question, although this study is well-performed and potentially interesting. This is mainly due to the fact that the relation between grid cell properties and behaviour is exclusively correlative and entirely based on single cell activity, although the introduction mentions quite often the grid cell network properties and dynamics. In general, this study gives the impression that grid cells exclusively support the cognitive processes involved in this task. This problem is in part related to the text.

Thank you for the comments. We recognise now that the previous text was insufficiently clear. We have modified the introduction to clarify the value of an approach that takes advantage of behavioural variability. Importantly, this approach is complementary to perturbation strategies we and others have used previously. In particular it addresses critical limitations of perturbation strategies which can be confounded by off-target effects and possible adaptation, both of which are extremely difficult to fully rule out. We hope that with this additional clarification it is now clear that as for any important question multiple and complementary testing strategies are required to make progres, and second, that our study makes a new and important contribution by introducing a novel experimental approach and by following this up with careful analyses that clearly distinguish competing hypotheses.

However, it would be interesting to look at the population level (even beyond grid cells) to test whether at the network level, the link between behavioural performance and neural activity is more straightforward compared to the single-cell level. This approach could reconcile the present results with those obtained in their previous study following MEC inactivation.

We’re unclear here about what the reviewer means by ‘more straightforward’ as clear relationships between activity of single grid cells and populations of grid cells are well established (Gardner et al., 2021; Waaga et al., 2021; Yoon et al., 2013).

To give a clearer indication of the corresponding population level representations, as mentioned in response to Reviewer #1, we now include additional data showing many simultaneously recorded neurons, and analyses of non-grid as well as grid cells (Figures 4, 5, Figure 5 Figure Supplement 2).

To reconcile results with our previous study of MEC inactivation we have paid additional attention to the roles of non-grid cells (following suggestions by Reviewer #1). We show that while some non-grid cells show transitions between task-anchored and task-independent firing that are coherent with the grid population, many others have more stable firing that is independent of grid representations. This is consistent with the idea that the MEC supports localised behaviour in the cued and uncued versions of the task (Tennant et al., 2018), and suggests that while grid cells preferentially contribute when cues are absent, non-grid cells could also support the cued version. We make this additional implication clear in the revised abstract and discussion.

The authors used a statistical method based on the computation of the frequency spectrum of the spatial periodicity of the neural firing to classify grid cells as 'position-coding' (with fields anchored to the virtual track) and 'distance-coding' (with fields repeating at regular intervals across trials). This is an interesting approach that has nonetheless the default to be based exclusively on autocorrelograms. It would be interesting to compare with a different method based on the similarities between raw maps.

While our main analyses use a periodogram-based method to identify when grid cells are / are not anchored to the task environment, we validate these analyses by examination of the rate maps in each condition (Figures 2-4). For example, when grid cells are task-anchored, according to the periodogram analysis, the rate maps clearly show spatially aligned peaks, whereas when grid cells are not anchored the peaks in their rate maps are not aligned (Figure 2A vs 2B; Figure 3B-E; Figure 4C). We provide further validation by showing that spatial information (in the track reference frame) is substantially higher when grid cell activity is task-anchored vs task-independent (Figures 2F, 3G, 4F and Figure 3 Figure Supplement 4).

To further address this point we have carried out additional complementary analyses in which we identify task anchored vs task independent modes using a template matching method applied to the raw rate maps (Figure 6, Figure Supplement 2). These analyses support similar conclusions to our periodogram-based analyses.

Beyond this minor point, cell categorization is performed using all trial types.

Each trial type (i.e. beacon or non-beacon) is supposed to force mice to use different strategies and should induce different spatial representations within the entorhinal-hippocampal circuit (and not only in the grid cell system). In that context, since all trials are mixed, it is difficult to extrapolate general information.

We recognise that the description of the task design was insufficiently clear but are unsure why ‘it is difficult to extrapolate general information’. Before addressing this point, we should first be clear that mice are not ‘forced’ to adopt any particular strategy. Rather, on uncued trials a path integration strategy is the most efficient way to solve the task. However, mice could instead use a less efficient strategy, for example by stopping at short intervals they still obtain rewards. Detailed behavioural analyses indicate that such random stopping strategies are used by naive mice, while with training mice learn to use spatial stopping strategies (Tennant et al. 2018).

In terms of ‘extracting general information’ from the task, the following findings lead to general predictions: 1) Grid cells can exist in either task-anchored or task-independent periodic firing modes; 2) These modes can be stable across a session, but often modeswitching occurs within a session; 3) While some non-grid cells show task-independent periodic firing, this is much less common than for grid cells, which suggests a model in which many non-grid MEC neurons operate independently from the grid network; 4) When a marker cue is available mice locate a reward equally well when grid cells are in taskanchored versus task-independent modes, which argues against theories in which grid cells are a key part of a general system for localisation; 5) When markers cues are absent taskanchored grid firing is associated with successful reward localisation, which corroborates a key prediction of theories in which grid cells contribute to path integration.

In revising the manuscript we have attempted to improve the writing to make these advances clearer, and have clarified methodological details that made interpretation more challenging than it should have been. For example, as noted in our response to Reviewer #1, we have included additional details to clarify the organisation of trials and relationships between trials, behavioural outcomes and neural codes observed.

On page 5 the authors state that 'Since only position representations should reliably predict the reward location, ..., we reasoned that the presence of positional coding could be used to assess whether grid firing contributes to the ongoing behaviour'. I do not agree with this statement. First of all, position coding should be more informative only in a cue-guided trial. Second, distance coding could be as informative as position coding since at the network level may provide information relevant to the task (such as distance from the reward).

Again, this point perhaps reflects a lack of clarity on our part in writing the manuscript. When grid cells are anchored to the track reference frame (now called ‘tasked anchored’, previously ‘position encoding’), then the location of the rate peaks in grid firing is reliable from trial to trial. This is the case whether or not the trial is cued. When grid cells are independent of the track reference frame (now called ‘task independent’, previously ‘distance encoding’), then the location of the firing rate peaks vary from trial to trial. In the latter case, position can not be read out directly from trial to trial.

In principle, in the task-independent mode track position could be calculated by storing the grid network configuration at the start of the track, which would differ on each trial, and then implementing a mechanism to readout relative distance as mice move along the track. However, if mice do use this computation we would expect them to do so equally well on cued and uncued trials. By contrast, our results clearly show a dissociation between trial types in the relationship between grid firing and behavioural outcome. We highlight and discuss this possibility in the revised manuscript (p 10, ‘Alternatively, mice could in principle estimate track location with a system that utilises information about distance travelled obtained from task-independent grid representations’).

Third, position-coding is interpreted as more relevant because it predominates in correct trials. However, this does not imply that this coding scheme is indeed used to perform correct trials.

We have revised the manuscript to clarify our goal of distinguishing major hypotheses for the roles of grid cells in behaviour (Introduction, ‘On the one hand, theoretical arguments that grid cell populations can generate high capacity codes imply that they could in principle contribute to all spatial behaviours (Fiete et al., 2008; Mathis et al., 2012; Sreenivasan and Fiete, 2011). On the other hand, if the behavioural importance of grid cells follows from their hypothesised ability to generate position representations by integrating self-motion signals (McNaughton et al., 2006), then their behavioural roles may be restricted to tasks that involve path integration strategies.’

By showing that performance on cued trials is similar regardless of whether grid cells are task-anchored or not, we provide strong evidence against the idea that grid firing is in general necessary for location-based behaviours. By showing that task anchoring is associated with successful localisation when cues are absent we corroborate a key prediction of hypothesised roles for grid cells in path integration-dependent behaviour. Therefore, we substantially reduce the space of behaviours to which grid cells might contribute. Importantly, this space is much larger for the MEC, which is required for cued and uncued versions of the task. We have revised the introduction and discussion to make these points clearer.

While we believe our results add a key piece of evidence to the puzzle of when and where grid cells contribute to behaviour, we agree that further work will be required to develop and test more refined hypotheses. Alternative models also remain plausible, for example perhaps the behaviourally relevant computations are implemented elsewhere in the brain with grid anchoring to the track as an indirect consequence. Nevertheless, explanations of this kind are more difficult to reconcile with evidence that inactivation of stellate cells in the MEC impairs learning of the task, and other manipulations that modify grid firing impair performance on similar tasks. We now discuss these possibilities (discussion p 10, ‘mice could in principle estimate track location with a system that utilises information about distance travelled obtained from task-independent grid representations’).

It could be more informative to push forward the correlative analysis by looking at whether behavioural performance can be predicted by the coding scheme on a trial-by-trial basis.

The previous version of the manuscript showed these analyses (now in Figure 6). Thus, task anchored grid firing predicts more successful performance on uncued trials at the session level (Figure 6A-B) and at the trial level (Figure 6C-D).

Reviewer #1 (Recommendations For The Authors):

(1) The author particularly mentioned that the 1D tracks are different from the "cue-rich environments that are typically used to study grid cells". It is not clear what conclusions would hold for a cue-rich environment or a track, which may require relatively less path integration compared to the cue-sparse environment. This point should be discussed.

This is an important point that we did not pay sufficient attention to in the previous version of the manuscript. Our finding of successful localisation in the cued environment when grid cells are not task anchored implies that grid anchoring is not required to solve cued tasks. The implication here is that cue rich environments may then not be the most suitable for investigation of grid roles in behaviour as non-grid mechanisms may suffice, although this does not rule out the possibility that anchored grid codes may play important roles in learning about cue rich environments. We now address this point in the discussion (p 10, ‘An implication of this result is that cue rich tracks often used to investigate grid activity patterns may not engage behaviours that require anchored grid firing.’).

(2) It would be good to see the statistics for the number of different cells (stable position or distance encoding, and unstable cells) identified per mouse/session and the number of grid cells per session.

These are now added to Supplemental Data 2 and will also be accessible through code and datasets that we will make available alongside the version of record.

(3) Figure 2F: any explanation about why AG cells had high spatial information?

Previously the calculation used bits per spike and as aperiodic cells have low firing rates the spatial information was high. We have replaced this with bits per second, which provides a more intuitive measure and no longer implies high spatial information. We have amended this in the methods (p 15, ‘Spatial information was calculated in bits per second…’).

(4) The following methods sections should provide additional details:

(4.1) Details of the training protocol are largely left to reference papers. The reference papers give a general outline of the training protocol, but the details are not completely comparable given the single experiment performed on these mice. More details should be given on training stages and experience at the time of the experiment.

The task is more clearly described in the introduction (p 3), and additional details of the training protocol are now provided in the methods (p 12-13).

(4.2) The methods reference mean speed across sessions, but it is not clear where this was used.

This was very poor wording. We have now changed this to ‘For each session the mean speed was calculated for each trial outcome’.

(4.3) The calculation of the spatial autocorrelogram on a per-trial basis should be more explicitly stated. Is it the average of each 10 cm increment with the centre trial?

We have added additional information to the methods (p 16-18).

(4.4) 1D field detection is not sufficiently explained in Figure 1/S2. This information should also appear in the methods section.

This is now clarified on page 16 in section ‘Analysis of neural activity and behaviour during the location memory task’.

(5) The data in Figure 4A and B only shows speed vs. location for one example mouse. The combined per mouse or per session data should also be shown.

This is now shown in Figure 5A and Figure 5, Figure Supplemental 2

(6) Figure 5 is somewhat confusing. Why are A/B by session and C/D by trial? The methods imply that A/B are originally averaged by cell, but that duplicate cells in the same session are excluded because behaviour versus session type is identical. This method should be valid if all grid cells within a session are all "stable". This is likely given the synchrony of code-switching between grid cells, but not all co-active grid cells behaved identically.

It is understandable that C/D are performed by trial, but it should be made clear that it is not a comparable analysis to A/B. It is unclear what N refers to in C. The figure says by trial, but the legend says the error bar is by cell. If data is calculated by trial and then averaged by cell, this should be more clearly stated.

In Figure 6A/B (previously Figure 5A/B) we focus our analysis on sessions in which the mode of grid firing, either task-anchored or task-independent, was relatively stable on a trialto-trial basis (see Figure 3F for definitions). This enables us to then compare behaviour averaged across each session, with sessions categorised as task-anchored and task independent. This analysis has the advantage that it focuses on large blocks of time (whole sessions) in which the mode of grid firing is unambiguous, but the disadvantage is that it excludes many sessions in which grid firing switches between task-anchored and taskindependent modes.

Figure 6C/D (previously Figure 5C/D) addresses this limitation by carrying out similar analyses with behaviour sorted into task-anchored versus task-independent groups at the level of trials. A potential limitation for this analysis is that grid firing is somewhat variable on a trial-by-trial basis and so some trials may be mis-classified. We don’t expect this to lead to systematic bias, but it may make the data more noisy. Nevertheless, these analyses are important to include as they allow assessment of whether conclusions from 6A/B hold when all sessions are considered.

We have added additional clarification of the rationale for these analyses to the main text (p7-8, ‘’We addressed this by using additional trial-level comparisons’). We have also added clarification in the methods section for categorisation of task-anchored versus taskindependent trials when multiple grid cells were recorded simultaneously (p 17, ‘When assigning a common classification across a group of cells recorded simultaneously...’) and an explanation for the N in the figure legend. We also clarify that the analyses use a nested random effects design to account for dependencies at the levels of sessions and mice (methods, p 20, ‘Random effects had a nested structure to account for animals and sessions…’) .

(7) Panels E and F of Figure 5 are not explained in the main text.

This is now corrected (see p8, ‘Additional analyses…’).

(8) Figure 5: Since stable grid cells and all grid cells are shown, it will be better to show unstable cells, which can be compared with grid cells.

Given that the rationale for differences between Figure 6A/B and C/D (previously Figure 5AD) were not previously clear, the reason for focussing on stable grid cells here was likely also not clear (see point 6 above). We don’t show unstable grid cells in Figure 6A-B as the behaviour averaged at the level of a session would be a mix of trials when they are taskanchored and when they are task-independent. Therefore, the analysis would not test predictions about the relationship between task-anchored vs task-independent modes and behaviour. We hope this is now clear in the manuscript given the revisions introduced to address point 6 above.

(9) The methods describing the statistics for these experiments are also confusing. The methods section should be written more clearly, and it should be made clear in the text or figure legend whether this data is the "original" data or is processed in relation to the model, such as excluding duplicate grid cells within a session. The figure legend should also state that a GLMM was used to calculate the statistics.

We have revised the methods section with the goal of improving clarity, adding detail and removing ambiguity. This includes updates of the methods for the GLMM analysis, which are referred to within the Figure 6 legend. A clear definition of a stable session is now also added to the Figure 6 legend.

Reviewer #2 (Recommendations For The Authors):

When grid fields are anchored to the virtual world (position mode), there is probably small trialto-trial variability in the firing location of the firing fields. Is this trial-to-trial variability related to the variability in the stop location? This would provide a more direct link between path integration in grid cell networks and behaviour that depends on path integration.

When attempting to address this we find that the firing of individual grid cells is too variable to allow sufficiently precise decoding of their fields at a single trial level. This is expected given the Poisson statistics of spike generation and previous evaluations of grid coding (e.g. (Stemmler et al., 2015)).

The conclusion of the abstract is: "Our results suggest that positional anchoring of grid firing enhances the performance of tasks that require path integration." This statement is slightly confusing. The task requires 1) anchoring the behaviour to the visual cues presented at the start of the trial and 2) path integration from thereon to identify the rewarded location. The performance is higher when grid cells anchor to the visual cues presented at the start of the trial. What the results show is that the anchoring of grid firing fields to visual landmarks enhances the performance of tasks that require path integration from visual landmarks (i.e. grid cells being anchored to the reference frame that is behaviorally relevant).

To try to more clearly explain the logic and conclusion we have rewritten the abstract, including the final sentence.

Similar comment for the title of Figure 5: "Positional grid coding is not required for cued spatial localisation but promotes path integration-dependent localisation." Positional coding means that grid cells are anchored to the behaviorally relevant reference frame.

To address the lack of clarity we have modified the little of Figure 6 (previously Figure 5) to read ‘Anchoring of grid firing to the task reference frame promotes localisation by path integration but is not required for cued localisation’.

In Figure 1, there is a wide range of beaconed (40-80%) and non-beaconed (10-60%) trials given. It is not 100% clear whether these refer to the percentage of trials of a given type within the recording sessions. Was the proportion of non-beaconed trials manipulated? If so, was the likelihood of position and distance coding changing according to the percentage of nonbeaconed trials?

The ranges given refer to proportions across different behavioural sessions. Within any given behavioural session the proportion was constant. We now make this clear in the figure legend and in the results and methods sections.

We did not manipulate proportions of trial types during a session. Manipulations betweens sessions were carried out with the goal of maximising the numbers of uncued trials that the mice would carry out (see response to public comments above). While the effect of trial-type at the session level is not relevant to the hypotheses we aim to test here, we have included an additional analysis of the relationship between task anchoring and the proportions of trial types in a session (Figure 3, Figure Supplement 7)(also discussed above). As disentangling the effects of learning and motivation will be complex and likely require new experimental designs we have not drawn strong conclusions or pursued the analysis further..

I was not convinced that the labels "position" and "distance" were appropriate for the two grid cell firing modes. My understanding is that the "position" code also requires the grid cell network to estimate distance. It seems that the main difference between the "position" and "distance" modes is that when in the "position" mode, the activity on the torus is reset to a constant toroidal location when the animal reaches a clearly identifiable location on the virtual track. In the "distance" mode, this resetting does not take place.

As previously mentioned, we agree these terms weren’t the best and have since relabelled these as “task-anchored” and “task-independent”.

There are a few sections in the manuscript that implicitly suggest that a causal link between grid cell activity and behaviour was demonstrated. For instance: "It has been challenging to directly test whether and when grid cells contribute to behaviour.": The assumption here is that the manuscript overcomes this challenge, but the study is correlative.

We have modified the wording to be clear that we are introducing new tests of predictions made by hypotheses about causal relationships between grid coding and behaviour (introduction, p 1-2). We also clarify that our results argue against the hypothesis that grid cells provide a general coded for behaviour, but corroborate predictions of hypotheses in which they are specifically important for path integration (discussion, p 10).

We have modified the title abstract and main text to try to treat claims about causality with care. We now more thoroughly introduce and contrast the approach we report here with previous experiments that use perturbations (introduction, p2). While it is tempting to make stronger claims for causality with these approaches, there are also logical limitations with perturbation-based approaches, for example the challenges of fully excluding off target effects and adaptation. We now explain how these strategies are complementary. Our view is that both strategies will be required to develop strong arguments for whether and when grid cells contribute to behaviour. From this perspective, it is encouraging that our conclusions are in agreement with what are probably the most specific perturbations of grid cells reported to date (Gil et al. 2017), while perturbations that more generally affect MEC function appear to impair cued and path integration-dependent behaviours (Tennant et al. 2018). We now discuss these points more clearly (introduction, p 2).

I am slightly confused by the references to the panels in Figure 4.

"In some sessions, localization of the reward occurred almost exclusively when grid cells were anchored to position and not when they encoded distance (Figure 4C). Figure 4C only shows position coding.

"In other sessions, animals localised the reward when grid firing was anchored to position or distance, but overall performance was improved on positional trials (Figure 4D-E)." The reference should probably point to Figure 4E-F or just to 4E.

"In a few sessions, we observed spatial stopping behaviour comparable to cued trials, even when grid firing almost exclusively encoded distance rather than position (Figure 4F)." From Figure 4F, it seems that the performance on non-beaconed trials is better during "position" coding.

We have now updated Figure 5 (Figure 4 in the original manuscript) and references to the Figure in the text. Now Figure 5 shows the activity of cells recorded in stable and unstable task-anchored and task-independent sessions (see Figure 5C-F).

Minor issues:

Is this correct: (Figure 4A and Figure 4, Figure Supplement 1).

This has been corrected.

Figure 4B: There could be an additional label for position and distance.

Figure 4B from the original manuscript has now been removed.

Figure 4C-F. The panels on the right side should be explained in the Figure Legend.

Legends for Figure 5C-F (previously Figure 4C-F) have now been updated.

Reviewer #3 (Recommendations For The Authors):

Specific questions :

(1) Position coding reflects a coding scheme in which fields are spaced by a fixed distance; previous studies have shown that a virtual track grid map is a slice of the 2D classic grid. In that case, the fields are still anchored to the track but would produce a completely different map. Did the authors check whether it is the case at least for some cells? If not, what could explain such a major difference?

Το avoid confusion we now use the term ‘task-anchored’ rather than ‘position coding’ (see comments above). We should further clarify that our conclusions rest on whether or not the grid fields are anchored to the track. Task anchored firing does not require that grid fields maintain their spacing from 2D environments, only that fields are at the same track position on each trial. Thus, whether the spacing of the fields corresponds to a slice through a 2D grid makes no difference to the hypotheses we test here.

We agree that the relationship between 1D and 2D field organisation could be an interesting future direction, for example anchoring could involve resetting the grid phase while maintaining a stable period, or it could be achieved through local distortions in the grid period. However, since these outcomes would not help distinguish the hypotheses we test here we have not included analyses to address them.

(2) Previous studies have highlighted the role of grid cells in goal coding. Here there is an explicit reward in a particular area. Are there any grid modifications around this area? This question is not addressed in this study.

Again, we note that the hypotheses we test here relate to the firing mode of grid cells - taskanchored or task-independent - and interpretation of our results is independent from the specific pattern of grid fields on the track. This question nevertheless leads to an interesting prediction that if grid fields cluster in the goal area then this clustering should be apparent in the task-anchored but not the task-independent firing mode.

We test this by considering the average distribution of firing fields across all grid cells in each firing mode (Reviewer Figure 1). We find that when grid firing is task-anchored there is a clear peak around the reward zone, which is consistent with previous work by Butler et al. and Boccara et al. Consistent with our other prediction, this peak is reduced when grid cells are in the task-independent mode.

Author response image 1.

Plot shows the grid field distribution during stable grid cell session (> 85 % task-anchored or task-independent) (A) or during task-anchored and task-independent trials (B). Shaded regions in A and B represent standard error of the mean measured across sessions and epochs respectively.

(3) The behavioural procedure during recording is not fully explained. Do trial types alternate within the same session by blocks? How many trials are within a block? Is there any relation between trial alternation and the switch in the coding scheme observed in a large subset of the grid cells?

We agree this wasn’t sufficiently clear in the previous version of the manuscript. Trial types were interleaved in a fixed order within each session. We have updated the results and methods sections to provide details (see responses above).

(4) From the examples in Figure 2 it seems that firing fields tend to shift toward the start position. Is it the case in all cells? Could this reflect some reorganisation at the network level with cells signalling the starting as time progresses?

This is inconsistent between cells. To make this variability clear we have included additional examples of spiking profiles from different grid cells (Figure 2 - 5). Because quantification of the phenomena would not, so far as we can tell, help distinguish our core hypotheses we have not included further analyses here.

(5) Are grid cells with different coding properties recorded in different parts of the MEC? Are there any differences between these cell categories in the 2D map?

The recordings we made are from the dorsal region of the MEC (stated at the start of the results section). We don’t have data to speak to other parts of the MEC.

Minor:

There are very few grid cell examples that repeat in the different figures. I would suggest showing more examples both in the main text and supplementary material.

We have now provided multiple additional examples in Figures 2, 4 and 5. Grid cell examples repeat in the main figures twice, in both cases only when showing additional examples are shown from the same recording session (Figure 2A example #1 with Figure 5C, Figure 3E with Figure 4A). Further similar repeats are found in the supplemental figures (Figure 3D with Figure 5, Figure Supplement 2A, Figure 3C with Figure 5, Figure Supplement 2F).

Fig1 A-B shows the predictions in a 1D track based on distance or position coding. The A inset represents the modification of field distribution from a 2D arena to a 1D track, as performed in this study. The inset B is misleading since it represents the modifications expected from a circular track to a 1D track as in Jacob et al 2019, that is not what the authors studied. It would be better to present either the predictions based on the present study or the prediction based on previous studies. In that case, they should mention the possibility that the 1D map is a slice of the 2D map.

The goal of Figure 1A-B is to illustrate predictions (right) based on conclusions from previous studies (left). Figure 1A shows predicted 1D track firing given anchoring to the environment typically observed in grid cell studies in 2D arenas. Figure 1B shows predicted 1D track firing given the firing shifting firing patterns observed by Jacob et al. in a circular 2D track. To improve clarity, we have modified the legend to make clear that the schematics to the right are predictions given the previous evidence summarised to the left. As we outline above, the critical prediction relates to whether the representations anchor to the track. Whether the 1D representation is a perfect slice isn’t relevant to the hypotheses tested and so isn’t included in the schematic (see comments above).