Dialog between Evolution and the Philosopher's brain

Brain: Do I know everything there is to know my own working, philosophically?

Evolution: No you don't. That's why Descartes got things so wrong. He knew nothing about his own working but thought he knew everything.

Brain: Can I get it please?

Evolution: No you can't. It's not worth it. Philosophy doesn't pay the bills.

Brain: I'm surprised that you said I don't know everything I need to know in order to do philosophy of my self. I thought I had everything I needed.

Evolution: Because you never got a meta-metacognition. Without it, you don't know what metacognition is missing, so you think you have everything you need.

Brain: Why can't I have it?

Evolution: Suppose module A is useful, well you'll get it. Suppose module B isn't useful, well you won't get it. Lamenting or being aware that module B is missing is not worth it. Imagine that you have an eye that not only has the R, G, B recepter cells, but also a meta-blindness cell that does nothing except keep sending a signal meaning "By the way, I can't see in infrared or ultraviolet". Do you think it's useful, or not?

Brain: No. If it were useful, I'd have the cells. If it were not useful, then complaining about the lack of it is even less useful.

Evolution: You got it. Meta-cognition really doesn't pay the bills!

Brain: Last question. Why do I have metacognition, including the awareness of what I don't know, but not meta-metacognition?

Evolution: You are aware of what you don't know when you can know it, and when knowing it is useful. Thus, you are aware of when you don't know what the weather is, or what your friends are doing -- both are things that matter for your survival, and both are things you can fix. But if you don't have the capacity to see in infrared, that is forever. You are born with it, and you will die with it, so why be aware of it? Similarly, if you don't know how many lobes you have, then that ignorance is forever, because short of growing a whole new circuit diagram, or trepanning, you can't know it, so why be aware of it?

Brain: So that's why we keep hallucinating souls, free wills, desires, and other unnatural phenomena that not only are not science, but are not even written in the same grammar as science. Not knowing how we work, and not knowing that we don't know, we hallucinate all those structures that work magically, not causally, without gears, levers, or electrons. We are all buttons, and no wires; all GUI, and no code. Souls are superficial, and neurons are deep...

Dialog between Evolution and the Philosopher's brain

Brain: Do I know everything there is to know my own working, philosophically?

Evolution: No you don't. That's why Descartes got things so wrong. He knew nothing about his own working but thought he knew everything.

Brain: Can I get it please?

Evolution: No you can't. It's not worth it. Philosophy doesn't pay the bills.

Brain: I'm surprised that you said I don't know everything I need to know in order to do philosophy of my self. I thought I had everything I needed.

Evolution: Because you never got a meta-metacognition. Without it, you don't know what metacognition is missing, so you think you have everything you need.

Brain: Why can't I have it?

Evolution: Suppose module A is useful, well you'll get it. Suppose module B isn't useful, well you won't get it. Lamenting or being aware that module B is missing is not worth it. Imagine that you have an eye that not only has the R, G, B recepter cells, but also a meta-blindness cell that does nothing except keep sending a signal meaning "By the way, I can't see in infrared or ultraviolet". Do you think it's useful, or not?

Brain: No. If it were useful, I'd have the cells. If it were not useful, then complaining about the lack of it is even less useful.

Evolution: You got it. Meta-cognition really doesn't pay the bills!

Brain: So that's why we keep hallucinating souls, free wills, desires, and other unnatural phenomena that not only are not science, but are not even written in the same grammar as science. Not knowing how we work, and not knowing that we don't know, we hallucinate all those structures that work magically, not causally, without gears, levers, or electrons. We are all buttons, and no wires; all GUI, and no code. Souls are superficial, and neurons are deep...

This is a test comment

Je ne comprends pas à quoi sert la balise si on a déjà une balise <!DOCTYPE html> qui est déjà censée indiquer qu'on code en html.

Japanese Language Pack for Visual Studio Code が正式名称のようです。 https://marketplace.visualstudio.com/items?itemName=MS-CEINTL.vscode-language-pack-ja

Make supports visible whenever possible.

This should be a regular paragraph rather than a quote block.

Delete the sentence about the time limit.

If using the code command to open an R script, then this sentence can be deleted.

You can't see this in the screenshot and people might not know where this is.

It may be better the instruct people to run

code R/example.R

from the terminal - this has the advantage of putting the script in a sensible place and opening it for editing straight away.

I see questions of power and structural inequality raised in section 6.01. This section describes a social worker's responsibility to advocate for improved living conditions and promote social justice. This section could go into more depth about how power dynamics and inequalities impact these living conditions. For example, the code could provide more detailed guidance on recognizing and addressing systemic issues such as racism, socioeconomic differences, and other forms of oppression that are deeply imbedded in our society. The code could also provide strategies to social workers to better confront the power imbalances they encounter. The NABSW Code of Ethics offers a valuable perspective to enrich the practicum learning experience by applying its commitment to addressing racism, oppression, and discrimination. Social workers can apply this principle in their practicum experience to identify inequalities within their practicum setting/organization. A social worker could assess the organization's policies and identify practices that may contribute to racial or social inequalities and take action towards creating a more equal environment.

Use the Subversion command update to update your local copy with the latest changes by the R Core Team.

"In a bash terminal, change to the source directory"

The R Core Team commit changes to the development version of R sometimes multiple times a day. It's a good idea to update our local copy of the source code from time to time, especially before creating a patch.

"N. Download the source code for the recommended packages

To build R with the recommended packages, we need to run the tools/rsync-recommended script from the source directory to download the source code for these packages:

$TOP_SRCDIR/tools/rsync-recommended "

Note this just downloads the source code which is not in the main svn repo, the packages are then built and installed when R is built.

-> " * After we change directory, we must run the configure script from the source directory.

$TOP_SRCDIR/configure

This step takes ~1 minute on the codespace. "

I think we should just document the "with recommended packages" workflow as this is what we do in the R Dev Guide. So we can drop the --without-recommended-packages option here and add in the step to get the source code for the recommended packages.

I tested the build without the --enable-R-shlib option and it works fine in VSCode. We will need to add this back in if we provide RStudio as an alternative IDE.

Drop the "* Command" bullet and put the code straight after the previous text.

Drop the "* Command" bullet and put the code straight after the previous text.

->"* BUILDDIR defines the build directory: /workspaces/r-dev-env/build/r-devel * TOP_SRCDIR defines the source directory: /workspaces/r-dev-env/svn/r-devel "

The screenshot needs to be updated.

-> "Configure the build"

-> "To keep the source directory clean, we change to a build directory to configure and build R."

Author response:

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

Reviewer #2 (Public Review):

Weaknesses:

The comparison of affinity predictions derived from AlphaFold2 and H3-opt models, based on molecular dynamics simulations, should have been discussed in depth. In some cases, there are huge differences between the estimations from H3-opt models and those from experimental structures. It seems that the authors obtained average differences of the real delta, instead of average differences of the absolute value of the delta. This can be misleading, because high negative differences might be compensated by high positive differences when computing the mean value. Moreover, it would have been good for the authors to disclose the trajectories from the MD simulations.

Thanks for your careful checks. We fully understand your concerns about the large differences when calculating affinity. To understand the source of these huge differences, we carefully analyzed the trajectories of the input structures during MD simulations. We found that the antigen-antibody complex shifted as it transited from NVT to NPT during pre-equilibrium, even when restraints are used to determine the protein structure. To address this issue, we consulted the solution provided on Amber's mailing list (http://archive.ambermd.org/202102/0298.html) and modified the top file ATOMS_MOLECULE item of the simulation system to merge the antigen-antibody complexes into one molecule. As a result, the number of SOLVENT_POINTERS was also adjusted. Finally, we performed all MD simulations and calculated affinities of all complexes.

We have corrected the “Afterwards, a 25000-step NVT simulation with a time step of 1 fs was performed to gradually heat the system from 0 K to 100 K. A 250000-step NPT simulation with a time step of 2 fs was carried out to further heat the system from 100 K to 298 K.” into “Afterwards, a 400-ps NVT simulation with a time step of 2 fs was performed to gradually heat the system from 0 K to 298 K (0–100 K: 100 ps; 100-298 K: 200 ps; hold 298 K: 100 ps), and a 100-ps NPT simulation with a time step of 2 fs was performed to equilibrate the density of the system. During heating and density equilibration, we constrained the antigen-antibody structure with a restraint value of 10 kcal×mol-1×Å-2.” and added the following sentence in the Method section of our revised manuscript: “The first 50 ns restrains the non-hydrogen atoms of the antigen-antibody complex, and the last 50 ns restrains the non-hydrogen atoms of the antigen, with a constraint value of 10 kcal×mol-1×Å-2”

In addition, we have corrected the calculation of mean deltas using absolute values and have demonstrated that the average affinities of structures predicted by H3-OPT were closer to those of experimentally determined structures than values obtained through AF2. These results have been updated in the revised manuscript. However, significant differences still exist between the estimations of H3-OPT models and those derived from experimental structures in few cases. We found that antibodies moved away from antigens both in AF2 and H3-OPT predicted complexes during simulations, resulting in RMSDbackbone (RMSD of antibody backbone) exceeding 20 Å. These deviations led to significant structural changes in the complexes and consequently resulted in notable differences in affinity calculations. Thus, we removed three samples (PDBID: 4qhu, 6flc, 6plk) from benchmark because these predicted structures moved away from the antigen structure during MD simulations, resulting in huge energy differences from the native structures.

Author response table 1.

We also appreciate your reminder, and we have calculated all RMSDbackbone during production runs (SI Fig. 5).

Author response image 1.

Reviewer #3 (Public Review):

Weaknesses:

The proposed method lacks of a confidence score or a warning to help guiding the users in moderate to challenging cases.

We were sorry for our mistakes. We have updated our GitHub code and added following sentences to clarify how we train this confidence score module in Method Section: “Confidence score prediction module

We apply an MSE loss for confidence prediction, label error was calculated as the Cα deviation of each residue after alignment. The inputs of this module are the same as those used for H3-OPT, and it generates a confidence score ranging from 0 to 100. The dropout rates of H3-OPT were set to 0.25. The learning rate and weight decay of Adam optimizer are set to 1 × 10−5 and 1 × 10−4, respectively.”

Reviewer #2 (Recommendations For The Authors):

I would strongly suggest that the authors deepen their discussion on the affinity prediction based on Molecular Dynamics. In particular, why do the authors think that some structures exhibit huge differences between the predictions from the experimental structure and the predicted by H3-opt? Also, please compute the mean deltas using the absolute value and not the real value; the letter can be extremely misleading and hidden very high differences in different directions that are compensating when averaging.

I would also advice to include graphical results of the MD trajectories, at least as Supp. Material.

We gratefully thank you for your feedback and fully understand your concerns. We found the source of these huge differences and solved this problem by changing method of MD simulations. Then, we calculated all affinities and corrected the mean deltas calculation using the absolute value. The RMSDbackbone values were also measured to enable accurate affinity predictions during production runs (SI Fig. 5). There are still big differences between the estimations of H3-OPT models and those from experimental structures in some cases. We found that antibodies moved away from antigens both in AF2 and H3-OPT predicted complexes during simulations, resulting in RMSDbackbone exceeding 20 Å. These deviations led to significant structural changes in the complexes and consequently resulted in notable differences in affinity calculations. Thus, we removed three samples (PDBID: 4qhu, 6flc, 6plk) from benchmark.

Thanks again for your professional advice.

Reviewer #3 (Recommendations For The Authors):

(1) I am pleased with the most of the answers provided by the authors to the first review. In my humble opinion, the new manuscript has greatly improved. However, I think some answers to the reviewers are worth to be included in the main text or supporting information for the benefit of general readers. In particular, the requested statistics (i.e. p-values for Cα-RMSD values across the modeling approaches, p-values and error bars in Fig 5a and 5b, etc.) should be introduced in the manuscript.

We sincerely appreciate your advice. We have added the statistics values to Fig. 4 and Fig. 5 to our manuscript.

Author response image 2.

Author response image 3.

(2) Similarly, authors state in the answers that "we have trained a separate module to predict the confidence score of the optimized CDR-H3 loops". That sounds a great improvement to H3-OPT! However, I couldn't find any reference of that new module in the reviewed version of the manuscript, nor in the available GitHub code. That is the reason for me to hold the weakness "The proposed method lacks of a confidence score".

We were really sorry for our careless mistakes. Thank you for your reminding. We have updated our GitHub code and added following sentences to clarify how we train this confidence score module in Method Section:

“Confidence score prediction module

We apply an MSE loss for confidence prediction, label error was calculated as the Cα deviation of each residue after alignment. The inputs of this module are the same as those used for H3-OPT, and it generates a confidence score ranging from 0 to 100. The dropout rates of H3-OPT were set to 0.25. The learning rate and weight decay of Adam optimizer are set to 1 × 10−5 and 1 × 10−4, respectively.”

(3) I acknowledge all the efforts made for solving new mutant/designed nanobody structures. Judging from the solved structures, mutants Y95F and Q118N seems critical to either crystallographic or dimerization contacts stabilizing the CDR-H3 loop, hence preventing the formation of crystals. Clearly, solving a molecular structure is a challenge, hence including the following comment in the manuscript is relevant for readers to correctly asset the magnitude of the validation: "The sequence identities of the VH domain and H3 loop are 0.816 and 0.647, respectively, comparing with the best template. The CDR-H3 lengths of these nanobodies are both 17. According to our classification strategy, these nanobodies belong to Sub1. The confidence scores of these AlphaFold2 predicted loops were all higher than 0.8, and these loops were accepted as the outputs of H3-OPT by CBM."

We appreciate your kind recommendations and have revised “Although Mut1 (E45A) and Mut2 (Q14N) shared the same CDR-H3 sequences as WT, only minor variations were observed in the CDR-H3. H3-OPT generated accurate predictions with Cα-RMSDs of 1.510 Å, 1.541 Å and 1.411 Å for the WT, Mut1, and Mut2, respectively.” into “Although Mut1 (E45A) and Mut2 (Q14N) shared the same CDR-H3 sequences as WT (LengthCDR-H3 = 17), only minor variations were observed in the CDR-H3. H3-OPT generated accurate predictions with Cα-RMSDs of 1.510 Å, 1.541 Å and 1.411 Å for the WT, Mut1, and Mut2, respectively (The confidence scores of these AlphaFold2 predicted loops were all higher than 0.8, and these loops were accepted as the outputs of H3-OPT by CBM). ”. In addition, we have added following sentence in the legend of Figure 4 to ensure that readers can appropriately evaluate the significance and reliability of our validations: “The sequence identities of the VH domain and H3 loop are 0.816 and 0.647, respectively, comparing with the best template.”.

(4) As pointed out in the first review, I think the work https://doi.org/10.1021/acs.jctc.1c00341 is worth acknowledging in section "2.2 Molecular dynamics (MD) simulations could not provide accurate CDR-H3 loop conformations" of supplementary material, as it constitutes a clear reference (and probably one of the few) to the MD simulations that authors pretend to perform. Similarly, the work https://doi.org/10.3390/molecules28103991 introduces a former benchmark on AI algorithms for predicting antibody and nanobody structures that readers may find interest to contrast with the present work. Indeed, this later reference is used by authors to answer a reviewer comment.

Thanks a lot for your valuable comments. We have added these references in the proper positions in our manuscript.

Reviewer #2 (Public Review):

This work provides a new tool (H3-Opt) for the prediction of antibody and nanobody structures, based on the combination of AlphaFold2 and a pre-trained protein language model, with a focus on predicting the challenging CDR-H3 loops with enhanced accuracy than previously developed approaches. This task is of high value for the development of new therapeutic antibodies. The paper provides an external validation consisting of 131 sequences, with further analysis of the results by segregating the test sets in three subsets of varying difficulty and comparison with other available methods. Furthermore, the approach was validated by comparing three experimentally solved 3D structures of anti-VEGF nanobodies with the H3-Opt predictions

Strengths:

The experimental design to train and validate the new approach has been clearly described, including the dataset compilation and its representative sampling into training, validation and test sets, and structure preparation. The results of the in silico validation are quite convincing and support the authors' conclusions.

The datasets used to train and validate the tool and the code are made available by the authors, which ensures transparency and reproducibility, and allows future benchmarking exercises with incoming new tools.

Compared to AlphaFold2, the authors' optimization seems to produce better results for the most challenging subsets of the test set.

Weaknesses:

None

Config enabled code

Author response:

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

eLife assessment

This important study explores infants' attention patterns in real-world settings using advanced protocols and cutting-edge methods. The presented evidence for the role of EEG theta power in infants' attention is currently incomplete. The study will be of interest to researchers working on the development and control of attention.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

The paper investigates the physiological and neural processes that relate to infants' attention allocation in a naturalistic setting. Contrary to experimental paradigms that are usually employed in developmental research, this study investigates attention processes while letting the infants be free to play with three toys in the vicinity of their caregiver, which is closer to a common, everyday life context. The paper focuses on infants at 5 and 10 months of age and finds differences in what predicts attention allocation. At 5 months, attention episodes are shorter and their duration is predicted by autonomic arousal. At 10 months, attention episodes are longer, and their duration can be predicted by theta power. Moreover, theta power predicted the proportion of looking at the toys, as well as a decrease in arousal (heart rate). Overall, the authors conclude that attentional systems change across development, becoming more driven by cortical processes.

Strengths:

I enjoyed reading the paper, I am impressed with the level of detail of the analyses, and I am strongly in favour of the overall approach, which tries to move beyond in-lab settings. The collection of multiple sources of data (EEG, heart rate, looking behaviour) at two different ages (5 and 10 months) is a key strength of this paper. The original analyses, which build onto robust EEG preprocessing, are an additional feat that improves the overall value of the paper. The careful consideration of how theta power might change before, during, and in the prediction of attention episodes is especially remarkable. However, I have a few major concerns that I would like the authors to address, especially on the methodological side.

Points of improvement

(1) Noise

The first concern is the level of noise across age groups, periods of attention allocation, and metrics. Starting with EEG, I appreciate the analysis of noise reported in supplementary materials. The analysis focuses on a broad level (average noise in 5-month-olds vs 10-month-olds) but variations might be more fine-grained (for example, noise in 5mos might be due to fussiness and crying, while at 10 months it might be due to increased movements). More importantly, noise might even be the same across age groups, but correlated to other aspects of their behaviour (head or eye movements) that are directly related to the measures of interest. Is it possible that noise might co-vary with some of the behaviours of interest, thus leading to either spurious effects or false negatives? One way to address this issue would be for example to check if noise in the signal can predict attention episodes. If this is the case, noise should be added as a covariate in many of the analyses of this paper. 

We thank the reviewer for this comment. We certainly have evidence that even the most state-of-the-art cleaning procedures (such as machine-learning trained ICA decompositions, as we applied here) are unable to remove eye movement artifact entirely from EEG data (Haresign et al., 2021; Phillips et al., 2023). (This applies to our data but also to others’ where confounding effects of eye movements are generally not considered.) Importantly, however, our analyses have been designed very carefully with this explicit challenge in mind. All of our analyses compare changes in the relationship between brain activity and attention as a function of age, and there is no evidence to suggest that different sources of noise (e.g. crying vs. movement) would associate differently with attention durations nor change their interactions with attention over developmental time. And figures 5 and 7, for example, both look at the relationship of EEG data at one moment in time to a child’s attention patterns hundreds or thousands of milliseconds before and after that moment, for which there is no possibility that head or eye movement artifact can have systematically influenced the results.

Moving onto the video coding, I see that inter-rater reliability was not very high. Is this due to the fine-grained nature of the coding (20ms)? Is it driven by differences in expertise among the two coders? Or because coding this fine-grained behaviour from video data is simply too difficult? The main dependent variable (looking duration) is extracted from the video coding, and I think the authors should be confident they are maximising measurement accuracy.

We appreciate the concern. To calculate IRR we used this function (Cardillo G. (2007) Cohen's kappa: compute the Cohen's kappa ratio on a square matrix. http://www.mathworks.com/matlabcentral/fileexchange/15365). Our “Observed agreement” was 0.7 (std= 0.15). However, we decided to report the Cohen's kappa coefficient, which is generally thought to be a more robust measure as it takes into account the agreement occurring by chance. We conducted the training meticulously (refer to response to Q6, R3), and we have confidence that our coders performed to the best of their abilities.

(2) Cross-correlation analyses

I would like to raise two issues here. The first is the potential problem of using auto-correlated variables as input for cross-correlations. I am not sure whether theta power was significantly autocorrelated. If it is, could it explain the cross-correlation result? The fact that the cross-correlation plots in Figure 6 peak at zero, and are significant (but lower) around zero, makes me think that it could be a consequence of periods around zero being autocorrelated. Relatedly: how does the fact that the significant lag includes zero, and a bit before, affect the interpretation of this effect? 

Just to clarify this analysis, we did include a plot showing autocorrelation of theta activity in the original submission (Figs 7A and 7B in the revised paper). These indicate that theta shows little to no autocorrelation. And we can see no way in which this might have influenced our results. From their comments, the reviewer seems rather to be thinking of phasic changes in the autocorrelation, and whether the possibility that greater stability in theta during the time period around looks might have caused the cross-correlation result shown in 7E. Again though we can see no way in which this might be true, as the cross-correlation indicates that greater theta power is associated with a greater likelihood of looking, and this would not have been affected by changes in the autocorrelation.

A second issue with the cross-correlation analyses is the coding of the looking behaviour. If I understand correctly, if an infant looked for a full second at the same object, they would get a maximum score (e.g., 1) while if they looked at 500ms at the object and 500ms away from the object, they would receive a score of e.g., 0.5. However, if they looked at one object for 500ms and another object for 500ms, they would receive a maximum score (e.g., 1). The reason seems unclear to me because these are different attention episodes, but they would be treated as one. In addition, the authors also show that within an attentional episode theta power changes (for 10mos). What is the reason behind this scoring system? Wouldn't it be better to adjust by the number of attention switches, e.g., with the formula: looking-time/(1+N_switches), so that if infants looked for a full second, but made 1 switch from one object to the other, the score would be .5, thus reflecting that attention was terminated within that episode? 

We appreciate this suggestion. This is something we did not consider, and we thank the reviewer for raising it. In response to their comment, we have now rerun the analyses using the new measure (looking-time/(1+N_switches), and we are reassured to find that the results remain highly consistent. Please see Author response image 1 below where you can see the original results in orange and the new measure in blue at 5 and 10 months.

Author response image 1.

(3) Clearer definitions of variables, constructs, and visualisations

The second issue is the overall clarity and systematicity of the paper. The concept of attention appears with many different names. Only in the abstract, it is described as attention control, attentional behaviours, attentiveness, attention durations, attention shifts and attention episode. More names are used elsewhere in the paper. Although some of them are indeed meant to describe different aspects, others are overlapping. As a consequence, the main results also become more difficult to grasp. For example, it is stated that autonomic arousal predicts attention, but it's harder to understand what specific aspect (duration of looking, disengagement, etc.) it is predictive of. Relatedly, the cognitive process under investigation (e.g., attention) and its operationalization (e.g., duration of consecutive looking toward a toy) are used interchangeably. I would want to see more demarcation between different concepts and between concepts and measurements.

We appreciate the comment and we have clarified the concepts and their operationalisation throughout the revised manuscript.

General Remarks

In general, the authors achieved their aim in that they successfully showed the relationship between looking behaviour (as a proxy of attention), autonomic arousal, and electrophysiology. Two aspects are especially interesting. First, the fact that at 5 months, autonomic arousal predicts the duration of subsequent attention episodes, but at 10 months this effect is not present. Conversely, at 10 months, theta power predicts the duration of looking episodes, but this effect is not present in 5-month-old infants. This pattern of results suggests that younger infants have less control over their attention, which mostly depends on their current state of arousal, but older infants have gained cortical control of their attention, which in turn impacts their looking behaviour and arousal.

We thank the reviewer for the close attention that they have paid to our manuscript, and for their insightful comments.

Reviewer #2 (Public Review):

Summary:

This manuscript explores infants' attention patterns in real-world settings and their relationship with autonomic arousal and EEG oscillations in the theta frequency band. The study included 5- and 10-month-old infants during free play. The results showed that the 5-month-old group exhibited a decline in HR forward-predicted attentional behaviors, while the 10-month-old group exhibited increased theta power following shifts in gaze, indicating the start of a new attention episode. Additionally, this increase in theta power predicted the duration of infants' looking behavior.

Strengths:

The study's strengths lie in its utilization of advanced protocols and cutting-edge techniques to assess infants' neural activity and autonomic arousal associated with their attention patterns, as well as the extensive data coding and processing. Overall, the findings have important theoretical implications for the development of infant attention.

Weaknesses:

Certain methodological procedures require further clarification, e.g., details on EEG data processing. Additionally, it would be beneficial to eliminate possible confounding factors and consider alternative interpretations, e,g., whether the differences observed between the two age groups were partly due to varying levels of general arousal and engagement during the free play.

We thank the reviewer for their suggestions and have addressed them in our point-by-point responses below.

Reviewer #3 (Public Review):

Summary:

Much of the literature on attention has focused on static, non-contingent stimuli that can be easily controlled and replicated--a mismatch with the actual day-to-day deployment of attention. The same limitation is evident in the developmental literature, which is further hampered by infants' limited behavioral repertoires and the general difficulty in collecting robust and reliable data in the first year of life. The current study engages young infants as they play with age-appropriate toys, capturing visual attention, cardiac measures of arousal, and EEG-based metrics of cognitive processing. The authors find that the temporal relations between measures are different at age 5 months vs. age 10 months. In particular, at 5 months of age, cardiac arousal appears to precede attention, while at 10 months of age attention processes lead to shifts in neural markers of engagement, as captured in theta activity.

Strengths:

The study brings to the forefront sophisticated analytical and methodological techniques to bring greater validity to the work typically done in the research lab. By using measures in the moment, they can more closely link biological measures to actual behaviors and cognitive stages. Often, we are forced to capture these measures in separate contexts and then infer in-the-moment relations. The data and techniques provide insights for future research work.

Weaknesses:

The sample is relatively modest, although this is somewhat balanced by the sheer number of data points generated by the moment-to-moment analyses. In addition, the study is cross-sectional, so the data cannot capture true change over time. Larger samples, followed over time, will provide a stronger test for the robustness and reliability of the preliminary data noted here. Finally, while the method certainly provides for a more active and interactive infant in testing, we are a few steps removed from the complexity of daily life and social interactions.

We thank the reviewer for their suggestions and have addressed them in our point-by-point responses below.

Reviewer #1 (Recommendations For The Authors):

Here are some specific ways in which clarity can be improved:

A. Regarding the distinction between constructs, or measures and constructs:

i. In the results section, I would prefer to mention looking at duration and heart rate as metrics that have been measured, while in the introduction and discussion, a clear 1-to-1 link between construct/cognitive process and behavioural or (neuro)psychophysical measure can be made (e.g., sustained attention is measured via looking durations; autonomic arousal is measured via heart-rate). 

The way attention and arousal were operationalised are now clarified throughout the text, especially in the results.

ii. Relatedly, the "attention" variable is not really measuring attention directly. It is rather measuring looking time (proportion of looking time to the toys?), which is the operationalisation, which is hypothesised to be related to attention (the construct/cognitive process). I would make the distinction between the two stronger.

This distinction between looking and paying attention is clearer now in the reviewed manuscript as per R1 and R3’s suggestions. We have also added a paragraph in the Introduction to clarify it and pointed out its limitations (see pg.5).

B. Each analysis should be set out to address a specific hypothesis. I would rather see hypotheses in the introduction (without direct reference to the details of the models that were used), and how a specific relation between variables should follow from such hypotheses. This would also solve the issue that some analyses did not seem directly necessary to the main goal of the paper. For example:

i. Are ACF and survival probability analyses aimed at proving different points, or are they different analyses to prove the same point? Consider either making clearer how they differ or moving one to supplementary materials.

We clarified this in pg. 4 of the revised manuscript.

ii. The autocorrelation results are not mentioned in the introduction. Are they aiming to show that the variables can be used for cross-correlation? Please clarify their role or remove them.

We clarified this in pg. 4 of the revised manuscript.

C. Clarity of cross-correlation figures. To ensure clarity when presenting a cross-correlation plot, it's important to provide information on the lead-lag relationships and which variable is considered X and which is Y. This could be done by labelling the axes more clearly (e.g., the left-hand side of the - axis specifies x leads y, right hand specifies y leads x) or adding a legend (e.g., dashed line indicates x leading y, solid line indicates y leading x). Finally, the limits of the x-axis are consistent across plots, but the limits of the y-axis differ, which makes it harder to visually compare the different plots. More broadly, the plots could have clearer labels, and their resolution could also be improved. 

This information on what variable precedes/ follows was in the caption of the figures. However, we have edited the figures as per the reviewer’s suggestion and added this information in the figures themselves. We have also uploaded all the figures in higher resolution.

D. Figure 7 was extremely helpful for understanding the paper, and I would rather have it as Figure 1 in the introduction. 

We have moved figure 7 to figure 1 as per this request.

E. Statistics should always be reported, and effects should always be described. For example, results of autocorrelation are not reported, and from the plot, it is also not clear if the effects are significant (the caption states that red dots indicate significance, but there are no red dots. Does this mean there is no autocorrelation?).

We apologise – this was hard to read in the original. We have clarified that there is no autocorrelation present in Fig 7A and 7D.

And if so, given that theta is a wave, how is it possible that there is no autocorrelation (connected to point 1)? 

We thank the reviewer for raising this point. In fact, theta power is looking at oscillatory activity in the EEG within the 3-6Hz window (i.e. 3 to 6 oscillations per second). Whereas we were analysing the autocorrelation in the EEG data by looking at changes in theta power between consecutive 1 second long windows. To say that there is no autocorrelation in the data means that, if there is more 3-6Hz activity within one particular 1-second window, there tends not to be significantly more 3-6Hz activity within the 1-second windows immediately before and after.

F. Alpha power is introduced later on, and in the discussion, it is mentioned that the effects that were found go against the authors' expectations. However, alpha power and the authors' expectations about it are not mentioned in the introduction. 

We thank the reviewer for this comment. We have added a paragraph on alpha in the introduction (pg.4).

Minor points:

1. At the end of 1st page of introduction, the authors state that: 

“How children allocate their attention in experimenter-controlled, screen-based lab tasks differs, however, from actual real-world attention in several ways (32-34). For example, the real-world is interactive and manipulable, and so how we interact with the world determines what information we, in turn, receive from it: experiences generate behaviours (35).”

I think there's more to this though - Lab-based studies can be made interactive too (e.g., Meyer et al., 2023, Stahl & Feigenson, 2015). What remains unexplored is how infants actively and freely initiate and self-structure their attention, rather than how they respond to experimental manipulations.

Meyer, M., van Schaik, J. E., Poli, F., & Hunnius, S. (2023). How infant‐directed actions enhance infants' attention, learning, and exploration: Evidence from EEG and computational modeling. Developmental Science, 26(1), e13259.

Stahl, A. E., & Feigenson, L. (2015). Observing the unexpected enhances infants' learning and exploration. Science, 348(6230), 91-94.

We thank the reviewer for this suggestion and added their point in pg. 4.

(2) Regarding analysis 4:

a. In analysis 1 you showed that the duration of attentional episodes changes with age. Is it fair to keep the same start, middle, and termination ranges across age groups? Is 3-4 seconds "middle" for 5-month-olds? 

We appreciate the comment. There are many ways we could have run these analyses and, in fact, in other papers we have done it differently, for example by splitting each look in 3, irrespective of its duration (Phillips et al., 2023).

However, one aspect we took into account was the observation that 5-month-old infants exhibited more shorter looks compared to older infants. We recognized that dividing each into 3 parts, regardless of its duration, might have impacted the results. Presumably, the activity during the middle and termination phases of a 1.5-second look differs from that of a look lasting over 7 seconds.

Two additional factors that provided us with confidence in our approach were: 1) while the definition of "middle" was somewhat arbitrary, it allowed us to maintain consistency in our analyses across different age points. And, 2) we obtained a comparable amount of observations across the two time points (e.g. “middle” at 5 months we had 172 events at 5 months, and 194 events at 10 months).

b. It is recommended not to interpret lower-level interactions if more complex interactions are not significant. How are the interaction effects in a simpler model in which the 3-way interaction is removed? 

We appreciate the comment. We tried to follow the same steps as in (Xie et al., 2018). However, we have re-analysed the data removing the 3-way interaction and the significance of the results stayed the same. Please see Author response image 2 below (first: new analyses without the 3-way interactions, second: original analyses that included the 3-way interaction).

Author response image 2.

(3) Figure S1: there seems to be an outlier in the bottom-right panel. Do results hold excluding it? 

We re-run these analyses as per this suggestion and the results stayed the same (refer to SM pg. 2).

(4) Figure S2 should refer to 10 months instead of 12.

We thank the reviewer for noticing this typo, we have changed it in the reviewed manuscript (see SM pg. 3). 

(5) In the 2nd paragraph of the discussion, I found this sentence unclear: "From Analysis 1 we found that infants at both ages showed a preferred modal reorientation rate". 

We clarified this in the reviewed manuscript in pg10

(6) Discussion: many (infant) studies have used theta in anticipation of receiving information (Begus et al., 2016) surprising events (Meyer et al., 2023), and especially exploration (Begus et al., 2015). Can you make a broader point on how these findings inform our interpretation of theta in the infant population (go more from description to underlying mechanisms)? 

We have extended on this point on interpreting frequency bands in pg13 of the reviewed manuscript and thank the reviewer for bringing it up.

Begus, K., Gliga, T., & Southgate, V. (2016). Infants' preferences for native speakers are associated with an expectation of information. Proceedings of the National Academy of Sciences, 113(44), 12397-12402.

Meyer, M., van Schaik, J. E., Poli, F., & Hunnius, S. (2023). How infant‐directed actions enhance infants' attention, learning, and exploration: Evidence from EEG and computational modeling. Developmental Science, 26(1), e13259.

Begus, K., Southgate, V., & Gliga, T. (2015). Neural mechanisms of infant learning: differences in frontal theta activity during object exploration modulate subsequent object recognition. Biology letters, 11(5), 20150041.

(7) 2nd page of discussion, last paragraph: "preferred modal reorientation timer" is not a neural/cognitive mechanism, just a resulting behaviour. 

We agree with this comment and thank the reviewer for bringing it out to our attention. We clarified this in in pg12 and pg13 of the reviewed manuscript.

Reviewer #2 (Recommendations For The Authors):

I have a few comments and questions that I think the authors should consider addressing in a revised version. Please see below:

(1) During preprocessing (steps 5 and 6), it seems like the "noisy channels" were rejected using the pop_rejchan.m function and then interpolated. This procedure is common in infant EEG analysis, but a concern arises: was there no upper limit for channel interpolation? Did the authors still perform bad channel interpolation even when more than 30% or 40% of the channels were identified as "bad" at the beginning with the continuous data? 

We did state in the original manuscript that “participants with fewer than 30% channels interpolated at 5 months and 25% at 10 months made it to the final step (ICA) and final analyses”. In the revised version we have re-written this section in order to make this more clear (pg. 17).

(2) I am also perplexed about the sequencing of the ICA pruning step. If the intention of ICA pruning is to eliminate artificial components, would it be more logical to perform this procedure before the conventional artifacts' rejection (i.e., step 7), rather than after? In addition, what was the methodology employed by the authors to identify the artificial ICA components? Was it done through manual visual inspection or utilizing specific toolboxes? 

We agree that the ICA is often run before, however, the decision to reject continuous data prior to ICA was to remove the very worst sections of data (where almost all channels were affected), which can arise during times when infants fuss or pull the caps. Thus, this step was applied at this point in the pipeline so that these sections of really bad data were not inputted into the ICA. This is fairly widespread practice in cleaning infant data.

Concerning the reviewer’s second question, of how ICA components were removed – the answer to this is described in considerable detail in the paper that we refer to in that setion of the manuscript. This was done by training a classifier specially designed to clean naturalistic infant EEG data (Haresign et al., 2021) and has since been employed in similar studies (e.g. Georgieva et al., 2020; Phillips et al., 2023).

(3) Please clarify how the relative power was calculated for the theta (3-6Hz) and alpha (6-9Hz) bands. Were they calculated by dividing the ratio of theta or alpha power to the power between 3 and 9Hz, or the total power between 1 (or 3) and 20 Hz? In other words, what does the term "all frequency bands" refer to in section 4.3.7? 

We thank the reviewer for this comment, we have now clarified this in pg. 22.

(4) One of the key discoveries presented in this paper is the observation that attention shifts are accompanied by a subsequent enhancement in theta band power shortly after the shifts occur. Is it possible that this effect or alteration might be linked to infants' saccades, which are used as indicators of attention shifts? Would it be feasible to analyze the disparities in amplitude between the left and right frontal electrodes (e.g., Fp1 and Fp2, which could be viewed as virtual horizontal EOG channels) in relation to theta band power, in order to eliminate the possibility that the augmentation of theta power was attributable to the intensity of the saccades? 

We appreciate the concern. Average saccade duration in infants is about 40ms (Garbutt et al., 2007). Our finding that the positive cross-correlation between theta and look duration is present not only when we examine zero-lag data but also when we examine how theta forwards-predicts attention 1-2 seconds afterwards seems therefore unlikely to be directly attributable to saccade-related artifact. Concerning the reviewer’s suggestion – this is something that we have tried in the past. Unfortunately, however, our experience is that identifying saccades based on the disparity between Fp1 and Fp2 is much too unreliable to be of any use in analysing data. Even if specially positioned HEOG electrodes are used, we still find the saccade detection to be insufficiently reliable. In ongoing work we are tracking eye movements separately, in order to be able to address this point more satisfactorily.

(5) The following question is related to my previous comment. Why is the duration of the relationship between theta power and moment-to-moment changes in attention so short? If theta is indeed associated with attention and information processing, shouldn't the relationship between the two variables strengthen as the attention episode progresses? Given that the authors themselves suggest that "One possible interpretation of this is that neural activity associates with the maintenance more than the initiation of attentional behaviors," it raises the question of (is in contradiction to) why the duration of the relationship is not longer but declines drastically (Figure 6). 

We thank the reviewer for raising this excellent point. Certainly we argue that this, together with the low autocorrelation values for theta documented in Fig 7A and 7D challenge many conventional ways of interpreting theta. We are continuing to investigate this question in ongoing work.

(6) Have the authors conducted a comparison of alpha relative power and HR deceleration durations between 5 and 10-month-old infants? This analysis could provide insights into whether the differences observed between the two age groups were partly due to varying levels of general arousal and engagement during free play.

We thank the reviewer for this suggestion. Indeed, this is an aspect we investigated but ultimately, given that our primary emphasis was on the theta frequency, and considering the length of the manuscript, we decided not to incorporate. However, we attached Author response image 3 below showing there was no significant interaction between HR and alpha band.

Author response image 3.

Reviewer #3 (Recommendations For The Authors):

(1) In reading the manuscript, the language used seems to imply longitudinal data or at the very least the ability to detect change or maturation. Given the cross-sectional nature of the data, the language should be tempered throughout. The data are illustrative but not definitive. 

We thank the reviewer for this comment. We have now clarified that “Data was analysed in a cross-sectional manner” in pg15.

(2) The sample size is quite modest, particularly in the specific age groups. This is likely tempered by the sheer number of data points available. This latter argument is implied in the text, but not as explicitly noted. (However, I may have missed this as the text is quite dense). I think more notice is needed on the reliability and stability of the findings given the sample. 

We have clarified this in pg16.

(3) On a related note, how was the sample size determined? Was there a power analysis to help guide decision-making for both recruitment and choosing which analyses to proceed with? Again, the analytic approach is quite sophisticated and the questions are of central interest to researchers, but I was left feeling maybe these two aspects of the study were out-sprinting the available data. The general impression is that the sample is small, but it is not until looking at table s7, that it is in full relief. I think this should be more prominent in the main body of the study.

We have clarified this in pg16.

(4) The devotes a few sentences to the relation between looking and attention. However, this distinction is central to the design of the study, and any philosophical differences regarding what take-away points can be generated. In my reading, I think this point needs to be more heavily interrogated. 

This distinction between looking and paying attention is clearer now in the reviewed manuscript as per R1 and R3’s suggestions. We have also added a paragraph in the Introduction to clarify it and pointed out its limitations (see pg.5).

(5) I would temper the real-world attention language. This study is certainly a great step forward, relative to static faces on a computer screen. However, there are still a great number of artificial constraints that have been added. That is not to say that the constraints are bad--they are necessary to carry out the work. However, it should be acknowledged that it constrains the external validity. 

We have added a paragraph to acknowledged limitations of the setup in pg. 14.

(6) The kappa on the coding is not strong. The authors chose to proceed nonetheless. Given that, I think more information is needed on how coders were trained, how they were standardized, and what parameters were used to decide they were ready to code independently. Again, with the sample size and the kappa presented, I think more discussion is needed regarding the robustness of the findings. 

We appreciate the concern. As per our answer to R1, we chose to report the most stringent calculator of inter-rater reliability, but other calculation methods (i.e., percent agreement) return higher scores (see response to R1).

As per the training, we wrote an extensively detailed coding scheme describing exactly how to code each look that was handed to our coders. Throughout the initial months of training, we meet with the coders on a weekly basis to discuss questions and individual frames that looked ambiguous. After each session, we would revise the coding scheme to incorporate additional details, aiming to make the coding process progressively less subjective. During this period, every coder analysed the same interactions, and inter-rater reliability (IRR) was assessed weekly, comparing their evaluations with mine (Marta). With time, the coders had fewer questions and IRR increased. At that point, we deemed them sufficiently trained, and began assigning them different interactions from each other. Periodically, though, we all assessed the same interaction and meet to review and discuss our coding outputs.

Figure 1 should be viewed full-size, in order to understand exactly how codes can be arranged into different categories, as the basis for developing descriptive themes.

The code in this case is "bad food=nice, good food=awful"

Yeah, this course was really good at introducing me to coding concepts, as a person who has never coded before. I am able to now understand most basic code, and edit accordingly. It also has peaked my interest and I may try to learn to code more in the summer!

-> "Restart VSCode in the r-dev-env directory with the command: "

Author response:

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

eLife assessment

In this potentially useful study, the authors attempt to use comparative meta-analysis to advance our understanding of life history evolution. Unfortunately, both the meta-analysis and the theoretical model is inadequate and proper statistical and mechanistic descriptions of the simulations are lacking. Specifically, the interpretation overlooks the effect of well-characterised complexities in the relationship between clutch size and fitness in birds.

Public Reviews:

We would like to thank the reviewers for their helpful comments, which have been considered carefully and have been valuable in progressing our manuscript. The following bullet points summarise the key points and our responses, though our detailed responses to specific comments can be found below:<br /> - Two reviewers commented that our data was not made available. Our data was provided upon submission and during the review process, however was not made accessible to the reviewers. Our data and code are available at https://doi.org/10.5061/dryad.q83bk3jnk.

- The reviewers have highlighted that some of our methodology was unclear and we have added all the requested detail to ensure our methods can be easily understood.

- The reviewers highlight the importance of our conclusions, but also suggest some interpretations might be missing and/or are incomplete. To make clear how we objectively interpreted our data and the wider consequences for life-history theory we provide a decision tree (Figure 5). This figure makes clear where we think the boundaries are in our interpretation and how multiple lines of evidence converge to the same conclusions.

Reviewer #1 (Public Review):

This paper falls in a long tradition of studies on the costs of reproduction in birds and its contribution to understanding individual variation in life histories. Unfortunately, the meta-analyses only confirm what we know already, and the simulations based on the outcome of the meta-analysis have shortcomings that prevent the inferences on optimal clutch size, in contrast to the claims made in the paper.

There was no information that I could find on the effect sizes used in the meta-analyses other than a figure listing the species included. In fact, there is more information on studies that were not included. This made it impossible to evaluate the data-set. This is a serious omission, because it is not uncommon for there to be serious errors in meta-analysis data sets. Moreover, in the long run the main contribution of a meta-analysis is to build a data set that can be included in further studies.

It is disappointing that two referees comment on data availability, as we supplied a link to our full dataset and the code we used in Dryad with our submitted manuscript. We were also asked to supply our data during the review process and we again supplied a link to our dataset and code, along with a folder containing the data and code itself. We received confirmation that the reviewers had been given our data and code. We support open science and it was our intention that our dataset should be fully available to reviewers and readers. Our data and code are at https://doi.org/10.5061/dryad.q83bk3jnk.

The main finding of the meta-analysis of the brood size manipulation studies is that the survival costs of enlarging brood size are modest, as previously reported by Santos & Nakagawa on what I suspect to be mostly the same data set.

We disagree that the main finding of our paper is the small survival cost of manipulated brood size. The major finding of the paper, in our opinion, is that the effect sizes for experimental and observational studies are in opposite directions, therefore providing the first quantitative evidence to support the influential theoretical framework put forward by van Noordwijk and de Jong (1986), that individuals differ in their optimal clutch size and are constrained to reproducing at this level due to a trade-off with survival. We further show that while the manipulation experiments have been widely accepted to be informative, they are not in fact an effective test of whether within-species variation in clutch size is the result of a trade-off between reproduction and survival.

The comment that we are reporting the same finding as Santos & Nakagawa (2012) is a misrepresentation of both that study and our own. Santos & Nakagawa found an effect of parental effort on survival only in males who had their clutch size increased – but no effect for males who had their clutch size reduced and no survival effect on females for either increasing or reducing parental effort. However, we found an overall reduction in survival for birds who had brood sizes manipulated to be larger than their original brood (for both sexes and mixed sex studies combined). In our supplementary information, we demonstrate that the overall survival effect of a change in reproductive effort is close to zero for males, negative (though non-significant) for females and significantly negative for mixed sexes (which are not included in the Santos & Nakagawa study). Please also note that the Santos & Nakagawa study was conducted over 10 years ago. This means we added additional data (L364-365). Furthermore, meta-analyses are an evolving practice and we also corrected and improved on the overall analysis approach (e.g. L358-359 and L 393-397, and see detailed SI).

The paper does a very poor job of critically discussing whether we should take this at face value or whether instead there may be short-comings in the general experimental approach. A major reason why survival cost estimates are barely significantly different from zero may well be that parents do not fully adjust their parental effort to the manipulated brood size, either because of time/energy constraints, because it is too costly and therefore not optimal, or because parents do not register increased offspring needs. Whatever the reason, as a consequence, there is usually a strong effect of brood size manipulation on offspring growth and thereby presumably their fitness prospects. In the simulations (Fig.4), the consequences of the survival costs of reproduction for optimal clutch size were investigated without considering brood size manipulation effects on the offspring. Effects on offspring are briefly acknowledged in the discussion, but otherwise ignored. Assuming that the survival costs of reproduction are indeed difficult to discern because the offspring bear the brunt of the increase in brood size, a simulation that ignores the latter effect is unlikely to yield any insight in optimal clutch size. It is not clear therefore what we learn from these calculations.

The reviewer’s comment is somewhat of a paradox. We take the best studied example of the trade-off between reproductive effort and parental survival – a key theme in life history and the biology of ageing – and subject this to a meta-analysis. The reviewer suggests we should interpret our finding as if there must be something wrong with the method or studies we included, rather than considering that the original hypothesis could be false or inflated in importance. We do not consider questioning the premise of the data over questioning a favoured hypothesis to necessarily be the best scientific approach here. In many places in our manuscript, we question and address, at length, the underlying data and their interpretation (L116-117, L165-167, 202-204 and L277-282). Moreover, we make it clear that we focus on the trade-off between current reproductive effort and subsequent parental survival, while being aware that other trade-offs could counter-balance or explain our findings (discussed on L208-210 & L301-316). Note that it is also problematic, when you do not find the expected response, to search for an alternative that has not been measured. In the case here, of potential trade-offs, there are endless possibilities of where a trade-off might operate between traits. We purposefully focus on the one well-studied and most commonly invoked trade-off. We clearly acknowledge, though, that when all possible trade-offs are taken into account a trade-off on the fitness level can occur and cite two famous studies (Daan et al., 1990 and Verhulst & Tinbergen 1991) that have shown just that (L314-316).

So whilst we agree with the reviewer that the offspring may incur costs themselves, rather than costs being incurred by the parents, the aim of our study was to test for a general trend across species in the survival costs of reproductive effort. It is unrealistic to suggest that incorporating offspring growth into our simulations would add insight, as a change in offspring number rarely affects all offspring in the nest equally and there can even be quite stark differences; for example, this will be most evident in species that produce sacrificial offspring. This effect will be further confounded by catch-up growth, for example, and so it is likely that increased sibling competition from added chicks alters offspring growth trajectories, rather than absolute growth as the reviewer suggests. There are mixed results in the literature on the effect of altering clutch size on offspring survival, with an increased clutch size through manipulation often increasing the number of recruits from a nest.

What we do appreciate from the reviewer’s comment is that the interpretation of our findings is complex. Even though our in-text explanation includes the caveats the reviewer refers to, and are discussed at length, their inter-relationships are hard to appreciate from a text format. To improve this presentation and for ease of the reader, we have added a decision tree (Figure 5) which represents the logical flow from the hypothesis being tested through to what overall conclusion can be drawn from our results. We believe this clarifies what conclusions can be drawn from our results. We emphasise again that the theory that trade-offs between reproductive effort and parental survival being the major driver of variation in offspring production was not supported though is the one that practitioners in the field would be most likely to invoke, and our result is important for this reason.

There are other reasons why brood size manipulations may not reveal the costs of reproduction animals would incur when opting for a larger brood size than they produced spontaneously themselves. Firstly, the manipulations do not affect the effort incurred in laying eggs (which also biases your comparison with natural variation in clutch size). Secondly, the studies by Boonekamp et al on Jackdaws found that while there was no effect of brood size manipulation on parental survival after one year of manipulation, there was a strong effect when the same individuals were manipulated in the same direction in multiple years. This could be taken to mean that costs are not immediate but delayed, explaining why single year manipulations generally show little effect on survival. It would also mean that most estimates of the fitness costs of manipulated brood size are not fit for purpose, because typically restricted to survival over a single year.

First, our results did show a survival cost of reproduction for brood manipulations (L107-123, Figure 1, Table 1). Note, however, that much theory is built on the immediate costs of reproduction and, as such, these costs are likely overinterpreted, meaning that our overall interpretation still holds, i.e. “parental survival trade-off is not the major determinative trade-off in life history within-species” (Figure 5).

We agree with the reviewer that lifetime manipulations could be even more informative than single-year manipulations. Unfortunately, there are currently too few studies available to be able to draw generalisable conclusions across species for lifetime manipulations. This is, however, the reason we used lifetime change in clutch size in our fitness projections, which the reviewer seems to have missed – please see methods line 466-468, where we explicitly state that this is lifetime enlargement. Of course, such interpretations do not include an accumulation of costs that is greater than the annual cost, but currently there is no clear evidence that such an assumption is valid. Such a conclusion can also not be drawn from the study on jackdaws by Boonekamp et al (2014) as the treatments were life-long and, therefore, cannot separate annual from accrued (multiplicative) costs that are more than the sum of the annual costs incurred. Note that we have now included specific discussion of this study in response to the reviewer (L265-269).

Details of how the analyses were carried out were opaque in places, but as I understood the analysis of the brood size manipulation studies, manipulation was coded as a covariate, with negative values for brood size reductions and positive values for brood size enlargements (and then variably scaled or not to control brood or clutch size). This approach implicitly assumes that the trade-off between current brood size (manipulation) and parental survival is linear, which contrasts with the general expectation that this trade-off is not linear. This assumption reduces the value of the analysis, and contrasts with the approach of Santos & Nakagawa.

We thank the reviewer for highlighting a lack of clarity in places in our methods. We have added additional detail to the methodology section (see “Study sourcing & inclusion criteria” and “Extracting effect sizes”) in our revised manuscript. Note, that our data and code was not shared with the reviewers despite us supplying this upon submission and again during the review process, which would have explained a lot more of the detail required.

For clarity in our response, each effect size was extracted by performing a logistic regression with survival as a binary response variable and clutch size was the absolute value of offspring in the nest (i.e., for a bird that laid a clutch size of 5 but was manipulated to have -1 egg, we used a clutch size value of 4). The clutch size was also standardised and, separately, expressed as a proportion of the species’ mean.

We disagree that our approach reduces the value of our analysis. First, our approach allows a direct comparison between experimental and observational studies, which is the novelty of our study. Our approach does differ from Santos & Nakagawa but we disagree that it contrasts. Our approach allows us to take into consideration the severity of the change in clutch size, which Santos & Nakagawa do not. Therefore, we do not agree that our approach is worse at accounting for non-linearity of trade-offs than the approach used by Santos & Nakagawa. Arguably, the approach by Santos & Nakagawa is worse, as they dichotomise effort as increased or decreased, factorise their output and thereby inflate their number of outcomes, of which only 1 cell of 4 categories is significant (for males and females, increased and decreased brood size). The proof is in the pudding as well, as our results clearly demonstrate that the magnitude of the manipulation is a key factor driving the results, i.e. one offspring for a seabird is a larger proportion of care (and fitness) than one offspring for a passerine. Such insights were not achieved by Santos & Nakagawa’s method and, again, did not allow a direct quantitative comparison between quality (correlational) and experimental (brood size manipulation, i.e. “trade-off”) effects, which forms a central part of our argumentation (Figure 5). 

Our analysis, alongside a plethora of other ecological studies, does assume that the response to our predictor variable is linear. However, it is common knowledge that there are very few (if any) truly linear relationships. We use linear relationships because they serve a good approximation of the trend and provide a more rigorous test for an underlying relationship than would fitting nonlinear models. For many datasets the range of added chicks required to estimate a non-linear relationship was not available. The question also remains of what the shape of such a non-linear relationship should be and is hard to determine a priori. There is also a real risk when fitting non-linear terms that they are spurious and overinterpreted, as they often present a better fit (denoting one df is not sufficient especially when slopes vary). We have added this detail to our discussion.

The observational study selection is not complete and apparently no attempt was made to make it complete. This is a missed opportunity - it would be interesting to learn more about interspecific variation in the association between natural variation in clutch size and parental survival.

We clearly state in our manuscript that we deliberately tailored the selection of studies to match the manipulation studies (L367-369). We paired species extracted for observational studies with those extracted in experimental studies to facilitate a direct comparison between observational and experimental studies, and to ensure that the respective datasets were comparable. The reviewer’s focus in this review seems to be solely on the experimental dataset. This comment dismisses the equally important observational component of our analysis and thereby fails to acknowledge one of the key questions being addressed in this study. Note that in our revised version we have edited the phylogenetic tree to indicate for which species we have both types of information, which highlights our approach to selecting observational data (Figure 3).

Reviewer #2 (Public Review):

I have read with great interest the manuscript entitled "The optimal clutch size revisited: separating individual quality from the costs of reproduction" by LA Winder and colleagues. The paper consists in a meta-analysis comparing survival rates from studies providing clutch sizes of species that are unmanipulated and from studies where the clutch sizes are manipulated, in order to better understand the effects of differences in individual quality and of the costs of reproduction. I find the idea of the manuscript very interesting. However, I am not sure the methodology used allows to reach the conclusions provided by the authors (mainly that there is no cost of reproduction, and that the entire variation in clutch size among individuals of a population is driven by "individual quality").

We would like to highlight that we do not conclude that there is no cost of reproduction. Please see lines 336–339, where we state that our lack of evidence for trade-offs driving within-species variation in clutch size does not necessarily mean the costs of reproduction are non-existent. We conclude that individuals are constrained to their optima by the survival cost of reproduction. It is also an over-statement of our conclusion to say that we believe that variation in clutch size is only driven by quality. Our results show that unmanipulated birds that have larger clutch sizes also lived longer, and we suggest that this is evidence that some individuals are “better” than others, but we do not say, nor imply, that no other factors affect variation in clutch size. We have added Figure 5 to our manuscript to help the reader better understand what questions we can answer with our study and what conclusions we can draw from our results.

I write that I am not sure, because in its current form, the manuscript does not contain a single equation, making it impossible to assess. It would need at least a set of mathematical descriptions for the statistical analysis and for the mechanistic model that the authors infer from it.

We appreciate this comment, and have explained our methods in terms that are accessible to a wider audience. Note, however, that our meta-analysis is standard and based on logistic regression and standard meta-analytic practices. We have added the model formula to the model output tables.

For the simulation, we simply simulated the resulting effects. We of course supplied our code for this along with our manuscript (https://doi.org/10.5061/dryad.q83bk3jnk), though as we mentioned above, we believe this was not shared with the reviewers despite us making this available for the review process. We therefore understand why the reviewer feels the simulations were not explained thoroughly. We have revised our methods section and added details which we believe make our methodology more clear without needing to consult the supplemental material. However, we have also added the equations used in the process of calculating our simulated data to the Supplementary Information for readers who wish to have this information in equation form.

The texts mixes concepts of individual vs population statistics, of within individual vs among-individuals measures, of allocation trade-offs and fitness trade-offs, etc ....which means it would also require a glossary of the definitions the authors use for these various terms, in order to be evaluated.

We would like to thank the reviewer for highlighting this lack of clarity in our text. Throughout the manuscript we have refined our terminology and indicated where we are referring to the individual level or the population level. The inclusion of our new Figure 5 (decision tree) should also help in this context, as it is clear on which level we base our interpretation and conclusions on.

This problem is emphasised by the following sentence to be found in the discussion "The effect of birds having naturally larger clutches was significantly opposite to the result of increasing clutch size through brood manipulation". The "effect" is defined as the survival rate (see Fig 1). While it is relatively easy to intuitively understand what the "effect" is for the unmanipulated studies: the sensitivity of survival to clutch size at the population level, this should be mentioned and detailed in a formula. Moreover, the concept of effect size is not at all obvious for the manipulated ones (effect of the manipulation? or survival rate whatever the manipulation (then how could it measure a trade-off ?)? at the population level? at the individual level ?) despite a whole appendix dedicated to it. This absolutely needs to be described properly in the manuscript.

Thank you for identifying this sentence for which the writing was ambiguous, our apologies. We have now rewritten this and included additional explanation. L282-290: ‘The effect on parental annual survival of having naturally larger clutches was significantly opposite to the result of increasing clutch size through brood manipulation, and quantitatively similar. Parents with naturally larger clutches are thus expected to live longer and this counterbalances the “cost of reproduction” when their brood size is experimentally manipulated. It is, therefore, possible that quality effects mask trade-offs. Furthermore, it could be possible that individuals that lay larger clutches have smaller costs of reproduction, i.e. would respond less in terms of annual survival to a brood size manipulation, but with our current dataset we cannot address this hypothesis (Figure 5).’

We would also like to thank the reviewer for bringing to our attention the lack of clarity about the details of our methodology. We have added details to our methodology (see “Extracting effect sizes” section) to address this (see highlighted sections). For clarity, the effect size for both manipulated and unmanipulated nests was survival, given the brood size raised. We performed a logistic regression with survival as a binary response variable (i.e., number of individuals that survived and number of individuals that died after each breeding season), and clutch size was the absolute value of offspring in the nest (i.e., for a bird that laid a clutch size of 5 but was manipulated to have -1 egg, we used a clutch size value of 4). This allows for direct comparison of the effect size (survival given clutch size raised) between manipulated and unmanipulated birds.

Despite the lack of information about the underlying mechanistic model tested and the statistical model used, my impression is still that the interpretation in the introduction and discussion is not granted by the outputs of the figures and tables. Let's use a model similar to that of (van Noordwijk and de Jong, 1986): imagine that the mechanism at the population level is

a.c_(i,q)+b.s_(i,q)=E_q

Where c_(i,q) are s_(i,q) are respectively the clutch size for individual i which is of quality q, and E_q is the level of "energy" that an individual of quality q has available during the given time-step (and a and b are constants turning the clutch size and survival rate into energy cost of reproduction and energy cost of survival, and there are both quite "high" so that an extra egg (c_(i,q) is increased by 1) at the current time-step, decreases s_(i,q) markedly (E_q is independent of the number of eggs produced), that is, we have strong individual costs of reproduction). Imagine now that the variance of c_(i,q) (when the population is not manipulated) among individuals of the same quality group, is very small (and therefore the variance of s_(i,q) is very small also) and that the expectation of both are proportional to E_q. Then, in the unmanipulated population, the variance in clutch size is mainly due to the variance in quality. And therefore, the larger the clutch size c_(i,q) the higher E_q, and the higher the survival s_(i,q).

In the manipulated populations however, because of the large a and b, an artificial increase in clutch size, for a given E_q, will lead to a lower survival s_(i,q). And the "effect size" at the population level may vary according to a,b and the variances mentioned above. In other words, the costs of reproduction may be strong, but be hidden by the data, when there is variance in quality; however there are actually strong costs of reproduction (so strong actually that they are deterministic and that the probability to survive is a direct function of the number of eggs produced)

We would like to thank the reviewer for these comments. We have added detail to our methodology section so our models and rationale are more clear. Please note that our simulations only take the experimental effect of brood size on parental survival into account. Our model does not incorporate quality effects. The reviewer is right that the relationship between quality and the effects exposed by manipulating brood size can take many forms and this is a very interesting topic, but not one we aimed to tackle in our manuscript. In terms of quality we make two points: (1) overall quality effects connecting reproduction and parental survival are present, (2) these effects are opposite in direction to the effects when reproduction is manipulated and similar in magnitude. We do not go further than that in interpreting our results. The reviewer is correct, however, that we do suggest and repeat suggestions by others that quality can also mask the trade-off in some individuals or circumstances (L74-76, L95-98 & L286-289), but we do not quantify this, as it is dependent on the unknown relationship between quality and the response to the manipulation. A focussed set of experiments in that context would be interesting and there are some data that could get at this, i.e. the relationship between produced clutch size and the relative effect of the manipulation (now included L287-290). Such information is, however, not available for all studies and, although we explored the possibility of analysing this, currently this is not possible with adequate confidence and there is the possible complexity of non-linear effects. We have added this rationale in our revision (L259-265).

Moreover, it seems to me that the costs of reproduction are a concept closely related to generation time. Looking beyond the individual allocative (and other individual components of the trade-off) cost of reproduction and towards a populational negative relationship between survival and reproduction, we have to consider the intra-population slow fast continuum (some types of individuals survive more and reproduce less (are slower) than other (which are faster)). This continuum is associated with a metric: the generation time. Some individuals will produce more eggs and survive less in a given time-period because this time-period corresponds to a higher ratio of their generation time (Gaillard and Yoccoz, 2003; Gaillard et al., 2005). It seems therefore important to me, to control for generation time and in general to account for the time-step used for each population studied when analysing costs of reproduction. The data used in this manuscript is not just clutch size and survival rates, but clutch size per year (or another time step) and annual (or other) survival rates.

The reviewer is right that this is interesting. There is a longstanding unexplained difference in temperate (seasonal) and tropical reproductive strategies. Most of our data come from seasonal breeders, however. Although there is some variation in second brooding and such, these species mostly only produce one brood. We do agree that a wider consideration here is relevant, but we are not trying to explain all of life history in our paper. It is clearly the case that other factors will operate and the opportunity for trade-offs will vary among species according to their respective life histories. However, our study focuses on the two most fundamental components of fitness – longevity and reproduction – to test a major hypothesis in the field, and we uncover new relationships that contrast with previous influential studies and cast doubt on previous conclusions. We question the assumed trade-off between reproduction and annual survival. We show that quality is important and that the effect we find in experimental studies is so small that it can only explain between-species patterns but is unlikely to be the selective force that constrains reproduction within species. We do agree that there is a lot more work that can be done in this area. We hope we are contributing to the field, by questioning this central trade-off. We have incorporated some of the reviewers suggestions in the revision (L309-315). We have added Figure 5 to make clear where we are able to reach solid conclusions and the evidence on which these are based as clearly as possible in an easily accessible format.

Finally, it is important to relate any study of the costs of reproduction in a context of individual heterogeneity (in quality for instance), to the general problem of the detection of effects of individual differences on survival (see, e.g., Fay et al., 2021). Without an understanding of the very particular statistical behaviour of survival, associated to an event that by definition occurs only once per life history trajectory (by contrast to many other traits, even demographic, where the corresponding event (production of eggs for reproduction, for example) can be measured several times for a given individual during its life history trajectory).

Thank you for raising this point. The reviewer is right that heterogeneity can dampen or augment selection. Note that by estimating the effect of quality here we give an example of how heterogeneity can possibly do exactly this. We thank the reviewer for raising that we should possibly link this to wider effects of heterogeneity and we have added to our discussion of how our results play into the importance of accounting for among-individual heterogeneity (L252-256).

References:

Fay, R. et al. (2021) 'Quantifying fixed individual heterogeneity in demographic parameters: Performance of correlated random effects for Bernoulli variables', Methods in Ecology and Evolution, 2021(August), pp. 1-14. doi: 10.1111/2041-210x.13728.

Gaillard, J.-M. et al. (2005) 'Generation time: a reliable metric to measure life-history variation among mammalian populations.', The American naturalist, 166(1), pp. 119-123; discussion 124-128. doi: 10.1086/430330.

Gaillard, J.-M. and Yoccoz, N. G. (2003) 'Temporal Variation in Survival of Mammals: a Case of Environmental Canalization?', Ecology, 84(12), pp. 3294-3306. doi: 10.1890/02-0409.

van Noordwijk, A. J. and de Jong, G. (1986) 'Acquisition and Allocation of Resources: Their Influence on Variation in Life History Tactics', American Naturalist, p. 137. doi: 10.1086/284547.

Reviewer #3 (Public Review):

The authors present here a comparative meta-analysis analysis designed to detect evidence for a reproduction/ survival trade-off, central to expectations from life history theory. They present variation in clutch size within species as an observation in conflict with expectations of optimisation of clutch size and suggest that this may be accounted for from weak selection on clutch size. The results of their analyses support this explanation - they found little evidence of a reproduction - survival trade-off across birds. They extrapolated from this result to show in a mathematical model that the fitness consequences of enlarged clutch sizes would only be expected to have a significant effect on fitness in extreme cases, outside of normal species' clutch size ranges. Given the centrality of the reproduction-survival trade-off, the authors suggest that this result should encourage us to take a more cautious approach to applying concepts the trade-off in life history theory and optimisation in behavioural ecology more generally. While many of the findings are interesting, I don't think the argument for a major re-think of life history theory and the role of trade-offs in fitness maximisation is justified.

The interest of the paper, for me, comes from highlighting the complexities of the link between clutch size and fitness, and the challenges facing biologists who want to detect evidence for life history trade-offs. Their results highlight apparently contradictory results from observational and experimental studies on the reproduction-survival trade-off and show that species with smaller clutch sizes are under stronger selection to limit clutch size.

Unfortunately, the authors interpret the failure to detect a life history trade-off as evidence that there isn't one. The construction of a mathematical model based on this interpretation serves to give this possible conclusion perhaps more weight than is merited on the basis of the results, of this necessarily quite simple, meta-analysis. There are several potential complicating factors that could explain the lack of detection of a trade-off in these studies, which are mentioned and dismissed as unimportant (lines 248-250) without any helpful, rigorous discussion. I list below just a selection of complexities which perhaps deserve more careful consideration by the authors to help readers understand the implications of their results:

We would like to thank the reviewer for their thoughtful response and summary of the findings that we also agree are central to our study. The reviewer also highlights areas where our manuscript could benefit from a deeper consideration and we have added detail accordingly to our revised discussion.

We would like to highlight that we do not interpret the failure to detect a trade-off as evidence that there is not one. First, and importantly, we do find a trade-off but show this is only incurred when individuals produce a clutch beyond their optimal level. Second, we also state on lines 322-326 that the lack of evidence to support trade-offs being strong enough to drive variation in clutch size does not necessarily mean there are no costs of reproduction.

The statement that we have constructed a mathematical model based on the interpretation that we have not found a trade-off is, again, factually incorrect. We ran these simulations because the opposite is true – we did find a trade-off. There is a significant effect of clutch size when manipulated on annual parental survival. We benefit from our unique analysis allowing for a quantitative fitness estimate from the effect size on annual survival (as this is expressed on a per-egg basis). This allowed us to ask whether this quantitative effect size can alone explain why reproduction is constrained, and we evaluate this using simulations. From these simulations we find that this effect size is too small to explain the constraint, so something else must be going on, and we do spend a considerable amount of text discussing the possible explanations (L202-215). Note that the possibly most parsimonious conclusion here is that costs of reproduction are not there, or simply small, so we also give that explanation some thought (L221-224 and L315-331).

We are disappointed by the suggestion that we have dismissed complicating factors that could prevent detection of a trade-off, as this was not our intention. We were aiming to highlight that what we have demonstrated to be an apparent trade-off can be explained through other mechanisms, and that the trade-off between clutch size and survival is not as strong in driving within-species variation in clutch size as previously assumed. We have added further discussion to our revised manuscript to make this clear and give readers a better understanding of the complexity of factors associated with life-history theory, including the addition of a decision tree (Figure 5).

• Reproductive output is optimised for lifetime reproductive success and so the consequences of being pushed off the optimum for one breeding attempt are not necessarily detectable in survival but in future reproductive success (and, therefore, lifetime reproductive success).

We agree this is a valid point, which is mentioned in our manuscript in terms of alternative stages where the costs of reproduction might be manifested (L316-320). We would also like to highlight that , in our simulations, the change in clutch size (and subsequent survival cost) was assumed for the lifetime of the individual, for this very reason.

• The analyses include some species that hatch broods simultaneously and some that hatch sequentially (although this information is not explicitly provided (see below)). This is potentially relevant because species which have been favoured by selection to set up a size asymmetry among their broods often don't even try to raise their whole broods but only feed the biggest chicks until they are sated; any added chicks face a high probability of starvation. The first point this observation raises is that the expectation of more chicks= more cost, doesn't hold for all species. The second more general point is that the very existence of the sequential hatching strategy to produce size asymmetry in a brood is very difficult to explain if you reject the notion of a trade-off.

We agree with the reviewer that the costs of reproduction can be absorbed by the offspring themselves, and may not be equal across offspring (we also highlight this at L317-318 in the manuscript). However, we disagree that for some species the addition of more chicks does not equate to an increase in cost, though we do accept this might be less for some species. This is, however, difficult to incorporate into a sensible model as the impacts will vary among species and some species do also exhibit catch-up growth. So, without a priori knowledge on this, we kept our model simple to test whether the effect on parental survival (often assumed to be a strong cost) can explain the constraint on reproductive effort, and we conclude that it does not.

We would also like to make clear that we are not rejecting the notion of a trade-off. Our study shows evidence that a trade-off between survival and reproductive effort probably does not drive within-species variation in clutch size. We do explicitly say this throughout our manuscript, and also provide suggestions of other areas where a trade-off may exist (L317-320). The point of our study is not whether trade-offs exist or not, it is whether there is a generalisable across-species trend for a trade-off between reproductive effort and survival – the most fundamental trade-off in our field but for which there is a lack of conclusive evidence within species. We believe the addition of Figure 5 to our reviewed manuscript also makes this more evident.

• For your standard, pair-breeding passerine, there is an expectation that costs of raising chicks will increase linearly with clutch size. Each chick requires X feeding visits to reach the required fledge weight. But this is not the case for species which lay precocious chicks which are relatively independent and able to feed themselves straight after hatching - so again the relationship of care and survival is unlikely to be detectable by looking at the effect of clutch size but again, it doesn't mean there isn't a trade-off between breeding and survival.

Precocial birds still provide a level of parental care, such as protection from predators. Though we agree that the level of parental care in provisioning food (and in some cases in all parental care given) is lower in precocial than altricial birds, this would only make our reported effect size for manipulated birds to be an underestimate. Again, we would like to draw the reviewer’s attention to the fact we did detect a trade-off in manipulated birds and we do not suggest that trade-offs do not exist. The argument the reviewer suggests here does not hold for unmanipulated birds, as we found that birds that naturally lay larger clutch sizes have higher survival.

• The costs of raising a brood to adulthood for your standard pair-breeding passerine is bound to be extreme, simply by dint of the energy expenditure required. In fact, it was shown that the basal metabolic rate of breeding passerines was at the very edge of what is physiologically possible, the human equivalent being cycling the Tour de France (Nagy et al. 1990). If birds are at the very edge of what is physiologically possible, is it likely that clutch size is under weak selection?

If birds are at the very edge of what is physiologically possible, then indeed it would necessarily follow that if they increase the resource allocated in one area then expenditure in another area must be reduced. In many studies, however, the overall brood mass is increased when chicks are added and cared for in an experimental setting, suggesting that birds are not operating at their limit all the time. Our simulations show that if individuals increase their clutch size, the survival cost of reproduction counterbalances the fitness gained by increasing clutch size and so there is no overall fitness gain to producing more offspring. Therefore, selection on clutch size is constrained to the within-species level. We do not say in our manuscript that clutch size is under weak selection – we only ask why variation in clutch size is maintained if selection always favours high-producing birds.

• Variation in clutch size is presented by the authors as inconsistent with the assumption that birds are under selection to lay the Lack clutch. Of course, this is absurd and makes me think that I have misunderstood the authors' intended point here. At any rate, the paper would benefit from more clarity about how variable clutch size has to be before it becomes a problem for optimality in the authors' view (lines 84-85; line 246). See Perrins (1965) for an exquisite example of how beautifully great tits optimise clutch size on average, despite laying between 5-12 eggs.

We thank the reviewer for highlighting that our manuscript may be misleading in places, however, we are unsure which part of our conclusions the author is referring to here. The question we pose is “Why don’t all birds produce a clutch size at the population optimum?”, and is central to the decades-long field of life-history theory. Why is variation maintained? As the reviewer outlines, there is extensive variability, with some birds laying half of what other birds lay.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

(1) Title: while the costs of reproduction are possibly important in shaping optimal clutch size, it is not clear what you can about it given that you do not consider clutch / brood size effects on fitness prospects of the offspring.

We have expanded on our discussion of how some costs may be absorbed by the offspring themselves. However, a change in offspring number rarely affects all offspring in the nest equally and there can even be quite stark differences; for example this will be most evident in species that produce sacrificial offspring. This effect will be further confounded by catch-up growth. There are mixed results in the literature on the effect of altering clutch size on offspring survival, with an increased clutch size through manipulation often increasing the number of recruits from a nest. We have focussed on the relationship between reproductive effort and survival because it is given the most weight in the field in terms of driving intra-specific variation in clutch size. We have altered our title to show we focus on the survival costs specifically: “The optimal clutch size revisited: separating individual quality from the parental survival costs of reproduction”.

(2) L.11-12: I agree that this is true for birds, but this is phrased more generally here. Are you sure that that is justified?

The trade-off between survival and reproductive effort has largely been tested experimentally through brood manipulations in birds as this provides a good system in which to test the costs and benefits of increasing parental effort. The work in this area has provided theory beyond just passerine birds, which are the most commonly manipulated group, to across-taxa theories. We are unaware of any study/studies that provide evidence that the reproduction/survival trade-off is generalisable across multiple species in any taxa. As such, we do believe this sentence is justified. An example is the lack of a consistent negative genetic correlation in populations of fruitflies, for example, that has also been hailed as a lack-of-cost paradigm. Furthermore, some mutants that live longer do so without a cost on reproduction.

(3) L.13-14: Not sure what you mean with this sentence - too much info lacking.

We have added some detail to this sentence.

(4) L.14: it is slightly awkward to say 'parental investment and survival' because it is the survival effect that is usually referred to as the 'investment'. Perhaps what you want to say is 'parental effort and survival'?

We have replaced “parental investment” with “reproductive effort”

(5) L.15: you can omit 'caused'. Compared to control treatment or to reduced broods? Why not mention effects or lack thereof of brood reduction? And it would be good to also mention here whether effects were similar in the sexes.

Please see our methodology where we state that we use clutch size as a continuous variable (we do not compare to control or reduced but include the absolute value of offspring in a logistic regression). The effects of a brood reduction are drawn from the same regression and so are opposite. Though we appreciate the detail here is lacking to fully comprehend our study, we would like to highlight this is the abstract and details are provided in the main text.

(6) L. 15: I am not sure why you write 'however', as the finding that experimental and natural variation have opposite effects is in complete agreement with what is generally reported in the literature and will therefore surprise no one that is aware of the literature.

We use “however” to highlight the change in direction of the effect size from the results in the previous sentence. We also believe that ours ise the first study that provides a quantitative estimate of this effect and that previous work is largely theoretical. The reviewer states that this is what is generally reported but it is not reported in all cases, as some relationships between reproductive effort and survival are negative (for the quality measurement, in correlational space, see Figure 1).

(7) L.16: saying 'opposite to the effect of phenotypic quality' seems difficult to justify, as clutch size cannot be equated with phenotypic quality. Perhaps simply say 'natural variation in clutch size'? If that is what you are referring to.

Please note we are referring to effect sizes here –- that is, the survival effect of a change in clutch size. By phenotypic quality we are referring to the fact that we find higher parental survival when natural clutch sizes are higher. It is not the case that we refer to quality only as having a higher clutch size. This is explicitly stated in the sentence you refer to. We have changed “effect” to “effect size” to highlight this further.

(8) L.18: why do you refer to 'parental care' here? Brood size is not equivalent to parental care.

Brood size manipulations are used to manipulate parental care. The effect on parental survival is expected to be incurred because of the increase in parental care. We have changed “parental care” to “reproductive effort” to reduce the number of terms we use in our manuscript.

(9) L.18-19: suggest to tone down this claim, as this is no more than a meta-analytic confirmation of a view that is (in my view) generally accepted in the field. That does not mean it is not useful, just that it does not constitute any new insight.

We are unaware of any other study which provides generalisable across-species evidence for opposite effects of quality and costs of reproduction. The work in this area is also largely theoretical and is yet to be supported experimemtally, especially in a quantitative fashion. It is surprising to us that the reviewer considers there to be general acceptance in a field, rather than being influenced by rigorous testing of hypotheses, made possible by meta-analysis, the current gold standard in our field.

(10) L.21: what does 'parental effort' mean here? You seem to use brood size, parental care, parental effort, and parental investment interchangeably but these are different concepts. Daan et al (1990, Behaviour), which you already cite, provide a useful graph separating these concepts. Please adjust this throughout the manuscript, i.e. replace 'reproductive effort' with wording that reflect the actual variable you use.

We have not used the phrase “parental effort” in this sentence. We agree these are different concepts but in this context are intertwined. For example, brood size is used to manipulate parental care as a result of increased parental effort. We do agree the manuscript would benefit from keeping terminology consistent throughout the manuscript and have adjusted this throughout.

(11) L.23: perhaps add 'in birds' somewhere in this sentence? Some reference to the assumptions underlying this inference would also be useful. Two major assumptions being that birds adjusted their effort to the manipulation as they would have done had they opted for a larger brood size themselves, and that the costs of laying and incubating extra eggs can be ignored. And then there is the effect that laying extra eggs will usually delay the hatch date, which in many species reduces reproductive success.

Though our study does exclusively use birds, birds have been used to test the survival/reproduction trade-off because they present a convenient system in which to experimentally test this. The conclusions from these studies have a broader application than in birds alone. We believe that although these details are important, they are not appropriate in the abstract of our paper.

(12) L.26: how is this an explanation? It just repeats the finding.

We intend to refer to all interpretations from all results presented in our manuscript. We have made this more clear by adjusting our writing.

(13) L.27: I do not see this point. And 'reproductive output' is yet another concept, that can be linked to the other concepts in the abstract in different ways, making it rather opaque.

We have changed “reproductive output” to “reproductive effort”.

(14) L.33: here you are jumping from 'resources' to 'energetically' - it is not clear that energy is the only or main limiting resource, so why narrow this down to energy?

We do not say energy is the only or main limiting resource. We simply highlight that reproduction is energetically demanding and so, intuitively, a trade-off with a highly energetically demanding process would be the focal place to observe a trade off. We have, though, replaced “energetically” with “resource”.

(15) L.35-36: this is new to me - I am not aware of any such claims, and effects on the residual reproductive value could also arise through effects on future reproduction. The authors you cite did not work on birds, or (in their own study systems) presented results that as far as I remember warrant such a general statement.

The trade-off between reproduction and survival is seminal to the disposable soma theory, proposed by Kirkwood. Though Kirkwood’s work was largely not focussed on birds, it had fundamental implications for the field of evolutionary ecology because of the generalisable nature of his proposed framework. In particular, it has had wide-reaching influence on how the biology of aging is interpreted. The readership of the journal here is broad, and our results have implications for that field too. The work of Kirkwood (many of the papers on this topic have over 2000 citations each) has been perhaps overly influential in many areas, so a link to how that work should be interpreted is highly relevant. If the reviewer is interested in this topic the following papers by one of the co-authors and others could be of interest, some of which we could not cite in the main manuscript due to space considerations:

https://www.science.org/doi/pdf/10.1126/sciadv.aay3047

https://agingcelljournal.org/Archive/Volume3/stochasticity_explains_non_genetic_inheritance_of_lifespan/

https://pubmed.ncbi.nlm.nih.gov/21558242/

https://besjournals.onlinelibrary.wiley.com/doi/full/10.1111/1365-2435.13444

https://www.nature.com/articles/362305a0

https://www.cell.com/trends/ecology-evolution/fulltext/S0169-5347(12)00147-4

https://www.cell.com/cell/pdf/S0092-8674(15)01488-9.pdf

https://bmcbiol.biomedcentral.com/articles/10.1186/s12915-018-0562-z

(16) L.42: this could be preceded with mentioning the limitations of observational data.

We have added detail as to why brood manipulations are a good test for trade-offs and so this is now inherently implied.

(17) L.42-43: why?

We have added detail to this sentence.

(18) L.45: do any of the references cited here really support this statement? I am certain that several do not - in these this statement is an assumption rather than something that is demonstrated. It may be useful to look at Kate Lessell's review on this that appeared in Etologia, I think in the 1990's. Mind however that 'reproductive effort' is operationally poorly defined for reproducing birds - provisioning rate is not necessarily a good measure of effort in so far as there are fitness costs.

We have updated the references to support the sentence.

(19) L.47: Given that you make this statement with respect to brood size manipulations in birds, it seems to me that the paper by Santos & Nakagawa is the only paper you should cite here. Given that you go on to analyze the same data it deserves to be discussed in more detail, for example to clarify what you aim to add to their analysis. What warrants repeating their analysis?

Please first note that our dataset includes Santos & Nakagawa and additional studies, so it is not accurate to say we analyse the same data. Furthermore, we believe our study has implications beyond birds alone and so believe it is appropriate to cite the papers that do support our statement. We have added details to the methods to explicitly state what data is gathered from Santos & Nakagawa (it is only used to find the appropriate literature and data was re-extracted and re-analysed in a more appropriate way) and, separately, how we gathered the observational studies (see L352-381).

(20) L.48: There are more possible explanations to this, which deserve to be discussed. For example, brood size manipulations may not have been that effective in manipulating reproductive effort - for example, effects on energy expenditure tend to be not terribly convincing. Secondly, the manipulations do not affect the effort incurred in laying eggs (which also biases your comparison with natural variation in clutch size). Thirdly, the studies by Boonekamp et al on Jackdaws found that while there was no effect of brood size manipulation on parental survival after one year of manipulation, there was a strong effect when the same individuals were manipulated in the same direction in multiple years. This could be taken to mean that costs are not immediate but delayed, explaining why single year manipulations generally show little effect on survival. It would also mean that most estimates of the fitness costs of manipulated brood size are not fit for purpose, because typically restricted to survival over a single year.

Please see our response to this comment in the public reviews.

Out of interest and because the reviewer mentioned “energy expenditure” specifically: There are studies that show convincing effects of brood size manipulation on parental energy expenditure. We do agree that there are also studies that show ceilings in expenditure. We therefore disagree that they “tend to be not terribly convincing”. Just a few examples:

https://academic.oup.com/beheco/article/10/5/598/222025 (Figure 2)

https://besjournals.onlinelibrary.wiley.com/doi/full/10.1111/1365-2435.12321 (Figure 1)

https://besjournals.onlinelibrary.wiley.com/doi/full/10.1046/j.1365-2656.2000.00395.x (but ceiling at enlarged brood).

(21) L.48, "or, alternatively, that individuals may differ in quality": how do you see that happening when brood size is manipulated, and hence 'quality' of different experimental categories can be assumed to be approximately equal? This point does apply to observational studies, so I assume that that is what you had in mind, but that distinction should be clear (also on line 54).

We have made it more clear that we determine if there are quality effects separate to the costs of reproduction found using brood manipulation studies.

(22) L.50: Drent & Daan, in their seminal paper on "The prudent parent" (1980, Ardea) were among the earliest to make this point and deserve to be cited here.

We have added this citation

(23) L.51, "relative importance": relative to what? Please be more specific.

We have adjusted this sentence.

(24) L.54: Vedder & Bouwhuis (2018, Oikos) go some way towards this point and should be explicitly mentioned with reference to the role of 'quality' effects on the association between reproductive output and survival.

We have added this reference.

(25) L.55: can you be more specific on what you want to do exactly? What you write here could be interpreted differently.

We have added an explicit aim after this sentence to be more clear.

(26) L.57: Here also a more specific wording would be useful. What does it mean exactly when you say you will distinguish between 'quality' and 'costs'?

We have added detail to this sentence.

(27) L.62: it should be clearer from the introduction that this is already well known, which will indirectly emphasize what you are adding to what we know already.

We would argue this is not well known and has only been theorised but not shown empirically, as we do here.

(28) L.62: you equate clutch size with 'quality' here - that needs to be spelled out.

We refer to quality as the positive effect size of survival for a given clutch size, not clutch size alone. We appreciate this is not clear in this sentence and have reworded.

(29) L.64: this looks like a serious misunderstanding to me, but in any case, these inferences should perhaps be left to the discussion (this also applies to later parts of this paragraph), when you have hopefully convinced readers of the claims you make on lines 62-63.

We are unsure of what the reviewer is referring to as a misunderstanding. We have chosen this format for the introduction to highlight our results. If this is a problem for the editors we will change as required.

(30) L.66: quantitative comparison of what?

Comparison of species. We have changed the wording of this sentence

(31) L.67-69: this should be in the methods.

We have used a modern format which highlights our result. We are happy to change the format should the editors wish us to.

(32) L.74-88: suggest to (re)move this entire paragraph, presenting inferences in such an uncritical manner before presenting the evidence is inappropriate in my view. I have therefore refrained from commenting on this paragraph.

We have chosen a modern format which highlights our result. We are happy to change the format should the editors wish us to.

(33) L.271, "must detail variation in the number of raised young": it is not sufficiently clear what this means - what does 'detail' mean in this context? And what does 'number of raised young' mean? The number hatched or raised to fledging?

We have now made this clear.

(34) L271, "must detail variation in the number of raised young": looking at table S4, it seems that on the basis of this criterion also brood size manipulation studies where details on the number of young manipulated were missing are excluded. I see little justification for this - surely these manipulations can for example be coded as for example having the average manipulation size in the meta-analysis data set, thereby contributing to tests of manipulation effects, but not to variation within the manipulation groups?

We have done in part what the reviewer describes. We are specifically interested in the manipulation size, so we required this to compare effect sizes across species and categories, a key advance of our study and outlined in many places in our manuscript. Note, however, that we only need comparative differences, and have used clutch size metrics more generally to obtain a mean clutch size for a species, as well as SD where required. Please also note that our supplement details exactly why studies were excluded from our analysis, as is the preferred practice in a meta-analysis.

(35) L.271, "referred to as clutch size": the point of this simplification is not clear to me why it is clearly confusing - why not refer to 'brood size' instead?

Brood size and clutch size can be used interchangeably here because, in the observational studies, the individuals vary in the number of eggs produced, whereas for brood manipulations this obviously happens after hatching and brood is perhaps a more appropriate term, but we wanted to simplify the terminology used. However, we use clutch size throughout as the aim of our study is to determine why individuals differ in the number of offspring they produce, and so clutch size is the most appropriate term for that.

(36) L.280: according to the specified inclusion criteria (lines 271/272) these studies should already be in the data set, so what does this mean exactly?

Selection criteria refers to whether a given study should be kept for analysis or not. It does not refer to how studies were found. Please see lines 361-378 for details on how we found studies (additional details are also in the Supplementary Methods).

(37) L.281: the use of 'quality' here is misleading - natural variation in clutch or brood size will have multiple causes, variation in phenotypic quality of the individuals and their environment (territories) is only one of the causes. Why not simply refer to what you are actually investigating: natural and experimental variation in brood size.

We disagree, our study aims to separate quality effects from the costs of reproduction and we use observational studies to test for quality differences, though we make no inference about the mechanisms. We do not imply that the environment causes differences in quality, but that to directly compare observation and experimental groups, they should contain similar species. So, to be clear again, quality refers to the positive covariation of clutch size with survival. We feel that we explain this clearly in our study’s rationale and have also improved our writing in several sections on this to avoid any confusion (see responses to earlier comments by the three reviewers).

(38) L.283, "in most cases": please be exact and say in xx out xx cases.

We have added the number of studies for each category here.

(39) L.283-285: presumably readers can see this directly in a table with the extracted data?

Our data and code can be accessed with the following link: https://doi.org/10.5061/dryad.q83bk3jnk. We believe the data are too large to include as a table in the main text and are not essential in understanding the paper. Though we do believe all readers should have access to this information if they wish and so is publicly available.

(40) L.293: there does not seem to be a table that lists the included studies and effect sizes. It is not uncommon to find major errors in such tables when one is familiar with the literature, and absence of this information impedes a complete assessment of the manuscript.

We supplied a link to our full dataset and the code we used in Dryad with our submitted manuscript. We were also asked to supply our data during the review process and we again supplied a link to our dataset and code, along with a folder containing the data and code itself. We received confirmation that the reviewers had been given our data and code. We support open science and it was our intention that our dataset should be fully available to reviewers and readers. We believe the data are too large to include as a table in the main text and are not essential in understanding the paper. Our data and code are at https://doi.org/10.5061/dryad.q83bk3jnk.

(41) L.293: from how many species?

We have added this detail.

(42) L.296, "longevity": this is a tricky concept, not usually reported in the studies you used, so please describe in detail what data you used.

We have removed longevity as we did not use this data in our current version of the manuscript.

(43) L. 298: again: where can I see this information?

Our data and code can be accessed with the following link: https://doi.org/10.5061/dryad.q83bk3jnk. We did supply this information when we submitted our manuscript and again during the review process but we believe this was not passed onto the reviewers.

(44) L. 304, "we used raw data": I assume that for the majority of papers the raw data were not available, so please explain how you dealt with this. Or perhaps this applies to a selection of the studies only? Perhaps the experimental studies?

By raw data, we mean the absolute value of offspring in the nest. We have changed the wording of this sentence and added detail about whether the absolute value of offspring was not present for brood manipulation studies (L393-397).

(45) L.304: When I remember correctly, Santos and Nakagawa examined effects of reducing and enlarging brood size separately, which is of importance because trade-off curves are unlikely to be linear and whether they are or not has major effects on the optimization process. But perhaps you tackled this in another way? I will read on.....

You are correct that Santos & Nakagawa compared brood increases and reductions to control separately. Note that this only partially accounts non-linearity and it does not take into account the severity of the change in brood size. By using a logistic regression of absolute clutch size, as we have done, we are able to directly compare brood manipulations with experimental studies. Please see Supplementary Methods lines 11-12, where we have added additional detail as to why our approach is beneficial in this analysis.

(46) L.319: what are you referring to exactly with "for each clutch size transformation"?

We refer to the raw, standardised and proportional clutch size transformations. We have added detail here to be more clear.

(47) L.319: is there a cost of survival? Perhaps you mean 'survival cost'? This would be appropriate for the experimental data, but not for the observational data, where the survival variation may be causally unrelated to the brood size variation, even if there is a correlation.

We have changed “cost of survival” to “effect of parental survival”. We only intend to imply causality for the experimental studies. For observational studies we do not suggest that increasing clutch size is causal for increasing survival, only correlative (and hence we use the phrase “quality”).

(48) L.320: please replace "parental effort" with something like 'experimental change in brood size'.

We have changed “parental effort” to “reproductive effort”

(49) L.321: due to failure of one or more eggs to hatch, and mortality very early in life, before brood sizes are manipulated, it is not likely that say an enlargement of brood size by 1 chick can be equated to the mean clutch size +1 egg / check. For example, in the Wytham great tit study, as re-analysed by Richard Pettifor, a 'brood size manipulation' of unmanipulated birds is approximately -1, being the number of eggs / chicks lost between laying and the time of brood size manipulation. Would this affect your comparisons?

Though we agree these are important factors in determining what a clutch/brood size actually is for a given individual/pair, as this can vary from egg laying to fledging. We do not believe that accounting for this (if it was possible to do so) would significantly affect our conclusions, as observational studies are comparable in the fact that these birds would also likely see early life mortality of their offspring. It is also possibly the case that parents already factor in this loss, and so a brood manipulation still changes the parental care effort an individual has to incur.

(50) L.332: instead of "adjusted" perhaps say 'mean centred'?

We have implemented this suggestion.

(51) L.345: this statement surprised me, but is difficult to verify because I could not locate a list of the included studies. However, to my best knowledge, most studies reporting brood size manipulation effects on parental survival had this as their main focus, in contrast to your statement.

Our data and code can be accessed with the following link: https://doi.org/10.5061/dryad.q83bk3jnk. We did supply this information when we submitted our manuscript and again during the review process but we believe this was not passed onto the reviewers by the journal, although supplied by us on several occasions. We regret that the reviewer was impeded by this unfortunate communication failure, but we did our best to make the data available to the reviewers during the initial review process.

(52) L.361-362: this seems a realistic approach from an evolutionary perspective, but we know from the jackdaw study by Boonekamp that the survival effect of brood size manipulation in a single year is very different from the survival effect of manipulating as in your model, i.e. every year of an individual's life the same manipulation. For very short-lived species this possibly does not make much difference, but for somewhat longer-lived species this could perhaps strongly affect your results. This should be discussed, and perhaps also explored in your simulations?

Note that the Boonekamp study does not separate whether the survival effects are additive or

multiplicative. As such, we do not know whether the survival effects for a single year manipulation are just small and hard to detect, or whether the survival effects are multiplicative. Our simulations assumed that the brood enlargement occurred every year throughout their lives. We have added some text to the discussion on the point you raise.

(53) L.360: what is "lifetime reproductive fitness"? Is this different from just "fitness"?

We have changed “lifetime reproductive fitness” to “lifetime reproductive output”.

(54) L.363: when you are interested in optimal clutch size, why not also explore effects of reducing clutch size?

As we find that a reduction in clutch size leads to a reduction in survival (for experimental studies), we already know that these individuals would have a reduced fitness return compared to reproducing at their normal level, and so we would not learn anything from adding this into our simulations. The interest in using clutch size enlargements is to find out why an individual does not produce more offspring than it does, and the answer is that it would not have a fitness benefit (unless its clutch size and survival rate combination is out of the bounds of that observable in the wild).

(55) Fig.1 - using 'parental effort' in the y-axis label is misleading, suggest to replace with e.g. "clutch or brood size". Using "clutch size" in the title is another issue, as the experimental studies typically changed the number of young rather than the number of eggs.

We have updated the figure axes to say “clutch size” rather than “parental effort”. Please see response to comment 35 where we explain our use of the term “clutch size” throughout this manuscript.

(56) L.93 - 108: I appreciate the analysis in Table 1, in particular the fact that you present different ways of expressing the manipulation. However, in addition, I would like to see the results of an analysis treating the manipulations as factor, i.e. without considering the scale of the manipulation. This serves two purposes. Firstly, I believe it is in the interest of the field that you include a detailed comparison with the results of Santos & Nakagawa's analysis of what I expect to be largely the same data (manipulation studies only - for this purpose I would also like to see a comparison of effect size between the sexes). Secondly, there are (at least) two levels of meta-analysis, namely quantifying an overall effect size, and testing variables that potentially explain variation in effect size. You are here sort of combining the two levels of analysis, but including the first level also would give much more insight in the data set.

Our main intention here was to improve on how the same hypothesis was approached by Santos & Nakagawa. We did this by improving our analysis (on a by “egg” basis) and by adding additional studies (i.e. more data). In this process mistakes are corrected (as we re-extracted all data, and did not copy anything across from their dataset – which was used simply to ensure we found the same papers); more recent data were also added, including studies missed by Santos & Nakagawa. This means that the comparison with Santos & Nakagawa becomes somewhat irrelevant, apart from maybe technical reasons, i.e. pointing out mistakes or limitations in certain approaches. We would not be able to pinpoint these problems clearly without considering the whole dataset, yet Santos & Nakagawa only had a small subset of the data that were available to us. In short, meta-analysis is an iterative process and similar questions are inevitably analysed multiple times and updated. This follows basic meta-analytic concepts and Cochrane principles. Except where there is a huge flaw in a prior dataset or approach (like we sometimes found and highlighted in our own work, e.g. Simons, Koch, Verhulst 2013, Aging Cell), in itself a comparison of the kind the reviewer suggests distracts from the biology. With the dataset being made available others can make these comparisons, if required. On the sex difference, we provide a comparison of effect sizes separated between both sexes and mixed sex in Table S2 and Figure S1.

(57) L.93 - 108: a thing that does not become clear from this section is whether experimentally reducing brood size affects parental survival similarly (in absolute terms) as enlarging brood size. Whether these effects are symmetric is biologically important, for example because of its effect on clutch size optimization. In the text you are specific about the effects of increasing brood size, but the effect you find could in theory be due entirely to brood size reduction.

We have added detail to make it clear that a brood reduction is simply the opposite trend. We use linear relationships because they serve a good approximation of the trend and provide a more rigorous test for an underlying relationship than would fitting nonlinear models. For many datasets there is not a range of chicks added for which a non-linear relationship could be estimated. The question also remains of what the shape of this non-linear relationship should be and is hard to determine a priori.

We have added some discussion on this to our manuscript (L278-282), in response to an earlier comment.

(58) L.103-107: this is perhaps better deferred to the discussion, because other potential explanations should also be considered. For example, there have been studies suggesting that small birds were provisioning their brood full time already, and hence had no scope to increase provisioning effort when brood size was experimentally increased.

We agree this is a discussion point but we believe it also provides an important context for why we ran our simulations, and so we believe this is best kept brief but in place. We agree the example you give is relevant but believe this argument is already contained in this section. See line 121-123 “...suggesting that costs to survival were only observed when a species was pushed beyond its natural limits”.

(59) L.103-107: this discussion sort of assumes that the results in Table 1 differ between the different ways that the clutch/brood size variation is expressed. Is there any statistical support for this assumption?

We are unsure of what the reviewer means here exactly. Note that in each of the clutch size transformations, experimental and observational effect sizes are significantly opposite. For the proportional clutch size transformation, experimental and observation studies are both separately significantly different from 0.

(60) L.104: at this point, I would like to have better insight into the data set. Specifically, a scatter plot showing the manipulation magnitude (raw) plotted against control brood size would be useful.

Our data and code can be accessed with the following link: https://doi.org/10.5061/dryad.q83bk3jnk. We did supply this information when we submitted our manuscript and again during the review process but we believe this was not passed onto the reviewers by the journal.

Thank you for this suggestion: this is a useful suggestion also to illustrate how manipulations are relatively stronger for species with smaller clutches, in line with our interpretation of the result presented in Figure 2. We have added Figure S1 which shows the strength of manipulation compared to the species average.

(61) L. 107: this seems a bold statement - surely you can test directly whether effect size becomes disproportionally stronger when manipulations are outside the natural range, for example by including this characterization as a factor in the models in Table 1.

It is hard to define exactly what the natural range is here, so it is not easy to factorise objectively, which is why we chose not to do this. However, it is clear that for species with small clutches the manipulation itself is often outside the natural range. Thank you for your suggestion to include a figure for this as it is clear manipulations are stronger in species with smaller clutches. We attribute this to species being forced outside their natural range. We consider our wording makes it clear that this is our interpretation of our findings and we therefore do not think this is a bold statement, especially as it fits with how we interpret our later simulations.

(62) Fig.3, legend: the term 'node support' does not mean much to me, please explain.

Node support is a value given in phylogenetic trees to dictate the confidence of a branch. In this case, values are given as a percentage and so can translate to how many times out of 100 the estimate of the phylogeny gives the same branching. Our values are low, as we have relatively few species in our meta-analysis.

(63) Fig.3: it would be informative when you indicate in this figure whether the species contributed to the experimental or the observational data set or both.

We have added into Fig 3 whether the species was observational, experimental or both.

(64) L.139: the p-value refers to the interaction between species clutch size and treatment (observational vs. experimental), but it appears that no evidence is presented for the correlation being significant in either observational or experimental studies.

We agree that our reporting of the effect size could be misinterpreted and have added detail here. The statistic provided describes the slopes are significantly different between observational and experimental, implying there are differences between the slopes of small and large clutch-laying species.

(65) L.140: I am wondering to what extent these correlations, which are potentially interesting, are driven by the fact that species average clutch size was also used when expressing the manipulation effect. In other words, to what extent is the estimate on the Y-axis independent from the clutch size on the X-axis? Showing that the result is the same when using survival effect sizes per manipulation category would considerably improve confidence in this finding.

We are unsure what the reviewer means by “per manipulation category”. Please also note that we have used a logistic regression to calculate our effect sizes of survival, given a unit increase in reproductive effort. So, for example, if a population contained birds that lay 2,3 or 4 eggs, provided that the number of birds which survived and died in each category did not change, if we changed the number of eggs raised to 10,11 or 12, respectively, then our effect size would be the same. In this way, our effect sizes are independent of the species’ average clutch size.

(66) L.145: when I remember correctly, Santos & Nakagawa considered brood size reduction and enlargement separately. Can this explain the contrasting result? Please discuss.

You are correct, in that Santos & Nakagawa compared reductions and enlargements to controls separately. However, we found some mistakes in the data extracted by Santos & Nakagawa that we believe explain the differences in our results for sex-specific effect sizes. We do not feel that highlighting these mistakes in the main text is fair, useful or scientifically relevant, as our approach is to improve the test of the hypothesis.

(67) L.158-159: looking at table S2 it seems to me you have a whole range of estimates. In any case, there is something to be said for taking the estimates for females because it is my impression (and experience) that clutch size variation in most species is a sex-linked trait, in that clutch size tends to be repeatable among females but not among males.

We agree that, in many cases, the female is the one that ultimately decides on the number of chicks produced. We did also consider using female effect sizes only, however, we decided against this for the following reasons: (1) many of the species used in our meta-analysis exhibit biparental care, as is the case for many seabirds, and so using females only would bias our results towards species with lower male investment; in our case this would bias the results towards passerine species. (2) it has also been shown that, as females in some species are operating at their maximum of parental care investment, it is the males who are able to adjust their workload to care for extra offspring. (3) we are ultimately looking at how many offspring the breeding adults should produce, given the effort it costs to raise them, and so even if the female chooses a clutch size completely independently of the male, it is still the effort of both parents combined that determines whether the parents gain an overall fitness benefit from laying extra eggs. (4) some studies did not clearly specify male or female parental survival and we would not want to reduce our dataset further.

(68) L.158-168: please explain how you incorporated brood size effects on the fitness prospects of offspring, given that it is a very robust finding of brood size manipulation studies that this affects offspring growth and survival.

We would argue this is near-on impossible to incorporate into our simulations. It is unrealistic to suggest that incorporating offspring growth into our simulations would add insight, as a change in offspring number rarely affects all offspring in the nest equally and there can even be quite stark differences; for example, this will be most evident in species that produce sacrificial offspring. This effect will be further confounded by catch-up growth, for example, and so it is likely that increased sibling competition from added chicks alters offspring growth trajectories, rather than absolute growth as the reviewer suggests. There are mixed results in the literature on the effect of altering clutch size on offspring survival, with an increased clutch size through manipulation often increasing the number of recruits from a nest. It would be interesting, however, to explore this further using estimates from the literature, but this is beyond our current scope, and would in our initial intuition not be very accurate. It would be interesting to explore how big the effect on offspring should be to constrain effect size strongly. Such work would be more theoretical. The point of our simple fitness projections here is to aid interpretation of the quantitative effect size we estimated.

(69) L.163: while I can understand that you select the estimate of -0.05 for computational reasons, it has enormous confidence intervals that also include zero. This seems problematic to me. However, in the simulations, you also examined the results of selecting -0.15, which is close to the lower end of the 95% C.I., which seems worth mentioning here already.

Thank you for this suggestion. Yes, indeed, our range was chosen based on the CI, and we have now made this explicit in the manuscript.

(70) L.210: defined in this way, in my world this is not what is generally taken to be a selection differential. Is what you show not simply scaled lifetime reproductive success?

As far as we are aware, a selection differential is the relative change between a given group and the population mean, which is what we have done here. We appreciate this is a slightly unusual context in which to place this, but it is more logical to consider the individuals who produce more offspring as carrying a potential mutation for higher productivity. However, we believe that “selection differential” is the best terminology for the statistic we present. We also detail in our methodology how we calculate this. We have adjusted this sentence to be more explicit about what we mean by selection differential.

(71) L.177-180: is this not so because these parameter values are closest to the data you based your estimates on, which yielded a low estimate and hence you see that here also?

We are unsure of what exactly the reviewer means here. The effect sizes for our exemplar species were predicted from each combination of clutch size and survival rate. Note that we used a range of effect sizes, higher than that estimated in our meta-analysis, to explore a large parameter space and that these same conclusions still hold.

(72) L.191-194: these statements are problematic, because based on the assumption that an increase in brood size does not impact the fitness prospects of the offspring, and we know this assumption to be false.

Though we appreciate that some cost is often absorbed by the offspring themselves, we are unaware of any evidence that these costs are substantial and large enough to drive within-species variation in reproductive effort, though for some specific species this may be the case. However, in terms of explaining a generalisable, across-species trend, the fitness costs incurred by a reduction in offspring quality are unlikely to be significantly larger than the survival costs to reproduce. We also find it highly unlikely the cost to fitness incurred by a reduction in offspring quality is large enough to counter-balance the effect of parental quality that we find in our observational studies. We do also discuss other costs in our discussion.

(73) L.205: here and in other places it would be useful to be more explicit on whether in your discussion you are referring to observational or experimental variation.

We have added this detail to our manuscript. Do note that many of our conclusions are drawn by the combination of results of experimental and observational studies. We believe the addition of Figure 5 makes this more clear to the reader.

(74) L.225: this may be true (at least, when we overlook the misuse of the word 'quality' here), but I would expect some nuance here to reflect that there is no surprise at all in this result as this pattern is generally recognized in the literature and has been the (empirical) basis for the often-repeated explanation of why experiments are required to demonstrate trade-offs. On a more quantitative level, it is worth mentioning the paper of Vedder & Bouwhuis (2017, Oikos) that essentially shows the same thing, i.e. a positive association between reproductive output and parental survival.

We have added some discussion on this point, including adding the citation mentioned. However, we would like to highlight that our results demonstrate that brood manipulations are not necessarily a good test of trade-offs, as they fail to recognise that individuals differ in their underlying quality. Though we agree that this result should not necessarily be a surprising one, we have also not found it to be the case that differences in individual quality are accepted as the reason that intra-specific clutch size is maintained – in fact, we find that it is most commonly argued that when costs of reproduction are not identifiedit is concluded that the costs must be elsewhere – yet we cannot find conclusive evidence that the costs of reproduction (wherever they lie) are driving intra-specific variation in reproductive effort. Furthermore, some studies in our dataset have reported negative correlations between reproductive effort and survival (see observational studies, Figure 1).

(75) L.225-226: perhaps present this definition when you first use the term.

We have added more detail to where we first use and define this term to improve clarity (L57-58).

(76) L.227-228, "currently unknown": this statement surprised me, given that there is a plethora of studies showing within-population variation in clutch size to depend on environmental conditions, in particular the rate at which food can be gathered.

We mean to question that if an individual is “high quality”, why is it not selected for? We have rephrased, to improve clarity.

(77) L.231: this seems no more than a special case of the environmental effect you mention above.

We think this is a relevant special case, as it constitutes within-individual variation in reproduction that is mistaken for between-individual variation. This is a common problem in our field, that we feel needs adressing. We only have between-individual variation here in our study on quality, and by highlighting this we show that there might not be any variation between individuals, but this could come about fully (doubtful) or partly (perhaps likely) due to terminal effects.

(78) L235-236: but apparently depending on how experimental and natural variation was expressed? Please specify here.

We are not sure what results the reviewer is referring to here, as we found the same effect (smaller clutch laying species are more severely affected by a change in clutch size) for both clutch size expressed as raw clutch size and standardised clutch size.

(79) L.237: the concept of 'limits' is not very productive here, and it conflicts with the optimality approach you apply elsewhere. What you are saying here can also be interpreted as there being a non-linear relationship between brood size manipulation and parental survival, but you do not actually test for that. A way to do this would be to treat brood size reduction and enlargement separately. Trade-off curves are not generally expected to be linear, so this would also make more sense biologically than your current approach.

We have replaced “limits” with “optima”. We believe our current approach of treating clutch size as a continuous variable, regardless of manipulation direction, is the best approach, as it allows us to directly compare with observational studies and between species that use different manipulations (now nicely illustrated by the reviewer’s suggested Figure S1). Also note that transforming clutch size to a proportion of the mean allows us to account for the severity in change in clutch size. We also do not believe that treating reductions and enlargements separately accounts for non-linearity, as either we are separating this into two linear relationships (one for enlargements and one for reductions) or we compare all enlargements/reductions to the control, as in Santos & Nakagawa 2012, which does not take into account the severity of the increase, which we would argue is worse for accounting for non-linearity. Furthermore, in the cases where the manipulation involved one offspring only, we also cannot account for non-linearity.

(80) L.239: assuming birds are on average able to optimize their clutch size, one could argue that any manipulation, large or small, on average forces birds to raise a number of offspring that deviates from their natural optimum. At this point, it would be interesting to discuss in some detail studies with manipulation designs that included different levels of brood size reduction/enlargement.

We agree with the reviewer that any manipulation is changing an individual’sclutch size away from its own individual optima, which we have argued also means brood manipulations are not necessarily a good test of whether a trade-off occurs in the wild (naturally), as there could be interactions with quality – we have now edited to explicitly state this (L299-300).

(81) L.242-244: when you choose to maintain this statement, please add something along the lines of "assuming there is no trade-off between number and quality of offspring".

As explained above, though we agree that the offspring may incur some of the cost themselves, we are not aware of any evidence suggesting this trade-off is also large enough to drive intra-specific variation in clutch size across species. Furthermore, in the context here, the trade-off between number and quality of offspring would not change our conclusion – that the fitness benefit of raising more offspring is offset by the cost on survival. We have added detail on the costs incurred by offspring earlier in our discussion (L309-315). The addition of Figure 5 should help interpret these data.

(82) L.253: instead of reference 30 the paper by Tinbergen et al in Behaviour (1990) seems more appropriate.

We believe our current citation is relevant here but we have also added the Tinbergen et al (1990) citation.

(83) L.253-254: such trade-offs may perfectly explain variation in reproductive effort within species if we were able to estimate cost-benefit relations for individuals. In fact, reference 29 goes some way to achieve this, by explaining seasonal variation in reproductive effort.

We are unaware of any quantitative evidence that any combination of trade-offs explains intra-specific variation in reproductive effort, especially as a general across-species trend.

(84) L.255: how does one demonstrate "between species life-history trade-offs"? The 'trade-off' between reproductive rate and survival we observe between species is not necessarily causal, and hence may not really be a trade-off but due to other factors - demonstrating causality requires some form of experimental manipulation.

Between-species trade-offs are well established in the field, stemming from GC Williams’ seminal paper in 1966, and for example in r/K selection theory. It is possible to move from these correlations to testing for causation, and this is happening currently by introducing transgenes (genes from other species) that promote longevity into shorter-lived species (e.g., naked-mole rat genes into mice). As yet it is unclear what the effects on reproduction are.

(85) L.256: it is quite a big claim that this is a novel suggestion. In fact, it is a general finding in evolutionary theory that fitness landscapes tend to be rather flat at equilibrium.

It is important to note here that we simulate the effect size found, and hence this is the novel suggestion, that because the resulting fitness landscape is relatively flat there is no directional selection observed. We did not intend to suggest our interpretation of flat fitness landscapes is novel. We have changed the phrasing of this sentence to avoid misinterpretation.

(86) L.259: why bring up physiological 'costs' here, given that you focus on fitness costs? Do you perhaps mean fitness costs instead of physiological costs? Furthermore, here and in the remainder of this paragraph it would be useful to be more specific on whether you are considering natural or experimental variation.

The cost of survival is a physiological cost incurred by the reduction of self-maintenance as a result of lower resource allocation. This is one arm of fitness; we feel it would be confusing here to talk about costs to fitness, as we do not assess costs to future reproduction (which formed the large part of the critique offered by the reviewer). We would like to highlight that the aim of this manuscript was to separate costs of reproduction from the effects of quality, and this is why we have observational and experimental studies in one analysis, rather than separately. Our conclusion that we have found no evidence that the survival cost to reproduce drives within-species variation in clutch size comes both from the positive correlation found in the observational studies and our negligible fitness return estimates in our simulations. We therefore, do not believe it is helpful to separate observational and experimental conclusions throughout our manuscript, as the point is that they are inherently linked. We hope that with the addition of Figure 5 that this is more clear.

(87) L.262: The finding that naturally more productive individuals tend to also survive better one could say is by definition explained by variation in 'quality', how else would you define quality?

We agree, and hence we believe quality is a good term to describe individuals who perform highly in two different traits. Note that we also say the lack of evidence that trade-offs drive intra-specific variation in clutch size also potentially suggests an alternative theory, including intra-specific variation driven by differences in individual quality.

Supplementary information

(88) Table S1: please provide details on how the treatment was coded - this information is needed to derive the estimates of the clutch size effect for the treatments separately.

We have added this detail.

(89) Table S2: please report the number of effect sizes included in each of these models.

We have added this detail.

(90) Table S4: references are not given. Mentioning species here would be useful. For example, Ashcroft (1979) studied puffins, which lay a single egg, making me wonder what is meant when mentioning "No clutch or brood size given" as the reason for exclusion. A few more words to explain why specific studies were excluded would be useful. For example, what does "Clutch size groups too large" mean? It surprises me that studies are excluded because "No standard deviation reported for survival" - as the exact distribution is known when sample size and proportion of survivors is known.

We have updated this table for more clarity.

(91) Fig.S1: please plot different panels with the same scale (separately for observational and experimental studies). You could add the individual data points to these plots - or at least indicate the sample size for the different categories (female, male, mixed).

We have scaled all panels to have the same y axis and added sample sizes to the figure legend.

(92) Fig.S3: please provide separate plots for experimental and observational studies, as it seems entirely plausible that the risk of publication bias is larger for observational studies - in particular those that did not also include a brood size manipulation. At the same time, one can wonder what a potential publication bias among observational studies would represent, given that apparently you did not attempt to collect all studies that reported the relevant information.

We have coloured the points for experimental and observational studies. Note that a study is an independent effect size and, therefore, does not indicate whether multiple data (i.e., both experimental and observational studies) came from the same paper. As we detail in the paper and above in our reviewer responses, we searched for observational studies from species used in the experimental studies to allow direct comparison between observational and experimental datasets.

Reviewer #2 (Recommendations For The Authors):

I strongly recommend improving the theoretical component of the analysis by providing a solid theoretical framework before, from it, drawing conclusions.

This, at a minimum, requires a statistical model and most importantly a mechanistic model describing the assumed relationships.

We thank the reviewer for highlighting that our aims and methodology are unclear in places. We have added detail to our model and simulation descriptions and have improved the description of our rationale. We also feel the failure of the journal to provide code and data to the reviewers has not helped their appreciation of our methodology and use of data.

Because the field uses the same wording for different concepts and different wording for the same concept, a glossary is also necessary.

We thank the reviewer for raising this issue. During the revision of this manuscript, we have simplified our terminology or given a definition, and we believe this is sufficient for readers to understand our terminology.

Reviewer #3 (Recommendations For The Authors):

• The files containing information of data extracted from each study were not available so it has not been possible to check how any of the points raised above apply to the species included in the study. The ms should include this file on the Supp. Info as is standard good practice for a comparative analysis.

We supplied a link to our full dataset and the code we used in Dryad with our submitted manuscript. We were also asked to supply our data during the review process and we again supplied a link to our dataset and code, along with a folder containing the data and code itself. We received confirmation that the reviewers had been given our data and code. We support open science and it was our intention that our dataset should be fully available to reviewers and readers. We believe the data is too large to include as a table in the main text and is not essential in understanding the paper. Our data and code are at https://doi.org/10.5061/dryad.q83bk3jnk.

• For clarity, refer to 'the effect size of clutch size on survival" rather than simply "effect size". Figures 1 and 2 require cross-referencing with the main text to understand the y-axis.

We have added detail to the figure legend to increase the interpretability of the figures.

• Silhouettes in Figure 3 (or photos) would help readers without ornithological expertise to understand the taxonomic range of the species included in the analyses.

We have added silhouettes into Figure 3.

• Throughout the discussion: superscripts shouldn't be treated as words in a sentence so please add authors' names where appropriate.

We have added author names and dates where required.

https://web.archive.org/web/20240528070547/https://shkspr.mobi/blog/2023/05/the-limits-of-general-purpose-computation/

Terence Eden (posted #2023/05/28 ) on the question if an app provider does have a say on being willing to run their code on your device, in contrast me being in control of a device and determining which code to run there or not. In this case a bank that would disallow their app on a rooted phone, because of risk profiles attached to that. Interesting tension: my risk assessment, control over general computation devices versus a service provider for which their software is a conduit and their risk assessments. I suspect the issue underneath this is such tensions need to be a conversation or negotiation to resolve, but in practice it's a dictate by one party based on a power differential (the bank controls your money, so they can set demands for your device, because you will need to keep access to your account.)

tính năng người dùng hỗ trợ tương tác, hiển thị và các thứ

Summary of "Revised Report on the Propagator Model" by Alexey Radul and Gerald Jay Sussman

Introduction

• Main Problem: Traditional programming models hinder extending existing programs for new situations due to rigid commitments in the code.
• Quote: "The most important problem facing a programmer is the revision of an existing program to extend it for some new situation."
• Solution: The Propagator Programming Model supports multiple viewpoints and integration of redundant solutions to aid program extensibility.
• Quote: "The Propagator Programming Model is an attempt to mitigate this problem."

Propagator Programming Model

• Core Concept: Autonomous machines (propagators) communicate via shared cells, continuously adding information based on computations.
• Quote: "The basic computational elements are autonomous machines interconnected by shared cells through which they communicate."
• Additivity: New contributions are seamlessly integrated by adding new propagators without disrupting existing computations.
• Quote: "New ways to make contributions can be added just by adding new propagators."

Propagator System

• Language Independence: The model can be implemented in any programming language as long as a communication protocol is maintained.
• Quote: "You should be able to write propagators in any language you choose."
• Cell Operations: Cells support adding content, collecting content, and registering propagators for notifications on content changes.
• Quote: "Cells must support three operations: add some content, collect the content currently accumulated, register a propagator to be notified when the accumulated content changes."

Implementing Propagator Networks

• Creating Cells and Propagators: Cells store data, while propagators compute based on cell data. Propagators are attached using d@ (diagram style) or e@ (expression style) for simpler cases.
• Quote: "The cells' job is to remember things; the propagators' job is to compute."
• Example: Adding two and three using propagators.
• Quote: "(define-cell a) (define-cell b) (add-content a 3) (add-content b 2) (define-cell answer (e:+ a b)) (run) (content answer) ==> 5"

Advanced Features

• Conditional Network Construction: Delayed construction using conditional propagators like p:when and p:if to control network growth.
• Quote: "The switch propagator does conditional propagation -- it only forwards its input to its output if its control is 'true'."
• Partial Information: Cells accumulate partial information, which can be incrementally refined.
• Quote: "Each 'memory location' of Scheme-Propagators, that is each cell, maintains not 'a value', but 'all the information it has about a value'."

Built-in Partial Information Structures

• Types: Nothing, Just a Value, Numerical Intervals, Propagator Cells, Compound Data, Closures, Truth Maintenance Systems, Contradiction.
• Quote: "The following partial information structures are provided with Scheme-Propagators: nothing, just a value, intervals, propagator cells, compound data, closures, supported values, truth maintenance systems, contradiction."

Debugging and Metadata

• Debugging: Scheme's built-in debugger aids in troubleshooting propagator networks. Metadata tracking for cells and propagators enhances debugging.
• Quote: "The underlying Scheme debugger is your friend."
• Metadata: Tracking names and connections of cells and propagators helps navigate and debug networks.
• Quote: "Inspection procedures using the metadata are provided: name, cell?, content, propagator?, propagator-inputs, propagator-outputs, neighbors, cell-non-readers, cell-connections."

Benefits of the Propagator Model

• Additivity and Redundancy: Supports incremental additions and multiple redundant computations, enhancing flexibility and resilience.
• Quote: "It is easy to add new propagators that implement additional ways to compute any part of the information about a value in a cell."
• Intrinsic Parallelism: Each component operates independently, making the model naturally parallel and race condition-resistant.
• Quote: "The paradigm of monotonically accumulating information makes [race conditions] irrelevant to the final results of a computation."
• Dependency Tracking: Facilitates easier integration and conflict resolution via premises and truth maintenance.
• Quote: "If the addition turns out to conflict with what was already there, it (or the offending old thing) can be ignored, locally and dynamically, by retracting a premise."

Conclusion

• Goal Achievement: The Propagator Model approaches goals of extensibility and additivity by allowing flexible integration and redundancy in computations.
• Quote: "Systems built on the Propagator Model of computation can approach some of these goals."

• The speaker initially describes the excitement and complexity of rendering a simple red triangle in Clojure using a Java library.

  • "I found a Java library that gave bindings I started playing around with it and after quite a bit of struggle I was able to get a red triangle to show up on the screen."

• The creation of more complex shapes like the Sierpinski pyramid, which involves recursive geometric transformations, serves as an example to explore different programming abstractions.

  • "It's actually fairly straightforward and I'll switch to two dimensions for your convenience, you start with a triangle and you shrink it down to half its size and then you copy it twice."

• The speaker introduces macros as a way to handle repetitive code by creating a reusable "Sierpinski macro" that can be nested to achieve different levels of detail.

  • "We can write ourselves a Sierpinski macro which takes a body which is really just anything and first we wrap it in a function and then we create a scoped transform which shrinks everything that we draw by half."

• Despite their usefulness, macros have limitations in terms of composition and downstream flexibility, prompting the exploration of functions as a better abstraction.

  • "Macros are not necessarily our most composable sort of abstraction and this has two issues... there is no potential for downstream composition."

• Functions, though still limited, allow for more composable and testable abstractions by introducing indirection and treating rendering operations as data.

  • "We take our draw triangle function and we call it now it's a renderer and now we have a render function which simply invokes it."

• The speaker demonstrates how higher-order functions and mapping over data can create more flexible and testable code, moving from functions to data-centric approaches.

  • "We defined three of these that will offset and scale appropriately and now we Define a Sierpinski method which takes a list of shapes and returns a list of shapes which is three times larger with all of them sort of offset and scaled appropriately."

• The comparison between data, functions, and macros emphasizes the generality and composability of data-centric approaches, albeit with the necessity of grounding them in executable code.

  • "Data doesn't do anything by itself we have to sort of eventually ground out in code that does something we have to wrap our data in functions and execute our functions somewhere within our code."

• The speaker critiques taxonomies while acknowledging their utility in providing a framework for discussion and suggesting approaches.

  • "Taxonomies are not a way to perfectly model the world... but they give us both a vocabulary to talk about it and they give us sort of a predictiveness."

• Applying these abstractions to more practical examples, like sequence transformations and transducers, illustrates the balance between abstraction and practical utility.

  • "We can use the double threaded arrow to structure it so that the flow of data is left to right rather than inside out."

• The exploration of automaton theory and finite state machines (like Automat) showcases the power of data-driven approaches in providing flexibility and compositional capabilities beyond traditional regular expressions.

  • "Automaton Theory... there's a much richer set of tools there than I'd originally realized and I tried to encompass this in a library called Automat."

• The discussion on backpressure and causality in asynchronous programming highlights the importance of managing side effects and execution order in concurrent systems.

  • "Backpressure here is this emergent property because we have this structural relationship between this it's just that one happens before the other and that one can cause the other not to happen."

• The introduction of streams and deferreds in the Manifold library exemplifies a less opinionated approach to handling eventual values and asynchronous computation, allowing for greater flexibility in execution models.

  • "A stream is lossy right you take a message it's gone a deferred represents a single unrealized value and you can sort of consume it as many times as you like."

• The concept of "let-flow" in Manifold, which optimizes concurrency by analyzing data dependencies, demonstrates advanced techniques for achieving optimal parallel execution.

  • "Let-flow will basically walk the entire let binding figure out what the data dependencies are and execute them in the correct order."

• The speaker concludes by emphasizing the importance of understanding the different forces at play in software composition and encourages ongoing discussion to improve the ecosystem.

  • "This is what causes our ecosystem to flourish or dwindle right the degree to which all the disparate pieces can work together."

• In the Q&A, the speaker briefly touches on the position of monads in the spectrum and compares Automat to other finite state machine libraries like Regal.

  • "Where do you put monads in your spectrum... somewhere between functions and data right."
  • "Automat... is meant to be sort of a combinator version of Regal effectively."

• Computational Challenges:
• We lack effective computational methods: "i think we actually have the foggiest idea how to compute very well."

• Importance of fast, efficient processes: "it took only 100 milliseconds... we don't understand how to do."

• Genomic Complexity:

• Human genome's complexity and flexibility: "with a small change to it you make a cow instead of a person."

• High-level language for biological processes is unknown: "what I'm interested in is the high-level language that's necessary to do things like that."

• Programming Evolution:

• Legacy of programming assumptions based on scarcity: "all of our sort of intuitions from being programmers have come from a time of assuming a kind of scarcity."

• Current abundance of resources shifts the focus: "memory is free, computing is free."

• Security and Correctness:

• Traditional concerns of correctness and security are secondary: "people worry about correctness... is it the real problem? maybe... most things don't have to work."

• Evolution and adaptability of code are crucial: "we spend all our time modifying existing code."

• Programming Constraints:

• Early decisions in programming constrain future changes: "we make decisions early in some process that spread all over our system."

• Need for flexibility in modifying systems: "organize systems so that the consequences of decisions we make are not expensive to change."

• Generic Operators and Extensions:

• Dynamically extensible operations: "dynamically extend things while my program is running."

• Symbolic algebra as an extension of arithmetic: "expand this arithmetic on functions... it's a classical thing people can do in algebra."

• Propagators and Parallelism:

• Concept of propagators for parallel computation: "propagators are independent little stateful machines."

• Parallelism and monotonic information merging: "we don't actually put values in these cells we put information about a value in a cell."

• Truth Maintenance Systems (TMS):

• Maintaining and improving data consistency: "truth maintenance systems... maintain the best estimates of what's going on."

• Dependency-directed backtracking for efficient problem-solving: "automatically find for me the consistent sub consistent sub the sub world views that are consistent."

• Historical and Educational Insights:

• Historical evolution of computation: "when I started computing in 1961... the total amount of memory is probably about 10 kilobytes."

• Educational gaps between theory and practical engineering: "what we taught the students wasn't at all what the students actually were expected to learn."

• Vision for the Future:

• Future computing systems must be inherently parallel, redundant, and flexible: "future... computers are so cheap and so easy to make... they can talk to each other and do useful things."

• Importance of evolving current computational thinking: "we have to throw away our current ways of thinking if we ever expect to solve these problems."

• Summary and Call to Action:

• Main challenge is evolvability, not correctness: "problem facing us as computer engineers is not correctness it's evolvability."
• Proposals include extensible operations and new architectural paradigms: "extensible generic operations... a more radical proposal is maybe there are freedoms that we can unlock by throwing away our idea of architecture."

This outline captures the essential points and arguments presented, while providing specific quotes for reference.

• Introduction

  • Jerry Sussman discusses the importance of flexible programming systems.
  • "I want to show how to the ways of making systems that have the property that you can you write this big pile of code and you know you, you get all of a sudden it's gee I have a different problem I have to solve why can't I use the same piece of code."

• Personal Background

  • Sussman's extensive experience as a programmer since the 1960s.
  • "I'm the oldest guy here probably and way back when I first started programming computers that's what they looked like."

• Goals for Robust Systems

  • Desires systems that are generalizable, evolvable, and tough.
  • "I want is robust systems that have the following property that they're generalizable in the sense that... they're evolvable in the sense that they can be adapted to new jobs without modification."

• Critique of Programming 'Religions'

  • Emphasizes the need for diverse tools and approaches in programming.
  • "We have a lot of people who have religions about how to program... Each of which is good for some particular problems but not good for a lot of problems."

• Body Plans in Engineering and Programming

  • Discusses the concept of body plans from biology and its application in engineering.
  • "Superrod radio receiver... a body plan... that separates band selectivity from inter-channel selectivity."

• Multiple Approaches in Problem Solving

  • Highlights the value of having multiple methods to solve the same problem, inspired by biology.
  • "There are two ways to make a frog... why don't we do that in programming?"

• Biological Inspiration in Programming

  • Advocates learning from nature's solutions, such as the flexible human genome.
  • "One of the things nature does is it's very expensive... generates and tests... we don't do that very much in programming because it's expensive."

• Generating and Testing in Programming

  • Discusses McCarthy's amb operator for non-deterministic search.
  • "McCarthy's amb operator... is a modeling non-deterministic autometer."

• Generic Operations and Extensibility

  • Explains the power of generic operations and their application in programming.
  • "Most people think generic operations... in fact, automatic differentiation is just a generic extension of arithmetic."

• Risks and Benefits of Generic Extensions

  • Acknowledges the dangers of generic programming while emphasizing its power.
  • "Generic arithmetic... very dangerous... the only thing that scares me in programming is floating point."

• Teaching and Practical Applications

  • Emphasizes the importance of teaching robust, flexible programming techniques.
  • "I've only given you three of them... I have hundreds of them that I just understand how to avoid programming yourself into a corner."

• Conclusion

  • Discusses his books and teaching philosophy, integrating traditional and programming languages for clarity.
  • "I've written several books about this... using programming as the way of expressing the ideas besides the traditional mathematics in addition to you make it unambiguous CL clear and therefore easy to read."

Résumé de la vidéo [00:00:00][^1^][1] - [00:29:11][^2^][2]:

Cette vidéo présente une discussion sur le harcèlement et la violence à l'école, animée par Myriam Ilouz et Catherine Perelmutter. Elle aborde les impacts psychologiques du harcèlement, son évolution à travers le temps, et les défis de l'identification des harceleurs dans un contexte scolaire.

Points forts: + [00:00:00][^3^][3] Introduction et contexte * Présentation de Myriam Ilouz, psychologue clinicienne * Importance du sujet du harcèlement à l'école + [00:01:00][^4^][4] Le harcèlement à l'école * Impact du harcèlement sur l'introduction de l'enfant au social * La souffrance des victimes et des harceleurs + [00:03:02][^5^][5] Changement dans la nature du harcèlement * Augmentation de l'intensité et de la violence du harcèlement * Utilisation des médias modernes pour harceler + [00:10:02][^6^][6] Caractéristiques des harceleurs * Agressivité, nuisance intentionnelle et répétée * Instauration d'une relation de disymétrie sociale + [00:20:01][^7^][7] La perversion et le harcèlement * Le harcèlement comme manifestation de la perversion narcissique * Difficulté à démasquer les harceleurs et à protéger les victimes + [00:27:02][^8^][8] Conséquences sociétales du harcèlement * Impact sur la confiance en l'école et la société * Nécessité d'une éducation solide pour prévenir la perversion Résumé de la vidéo [00:29:13][^1^][1] - [00:56:27][^2^][2]:

La vidéo aborde le problème du harcèlement et de la violence à l'école, en se concentrant sur les changements dans l'éducation des enfants, l'impact de la société moderne sur le comportement des élèves, et les défis rencontrés par les enseignants et les parents. Elle souligne l'importance de comprendre la loi, la frustration et la castration symbolique dans l'éducation pour prévenir le harcèlement.

Points forts: + [00:29:13][^3^][3] L'évolution de l'éducation des enfants * La psychanalyse française et son impact * La création d'enfants rois et le manque de règles claires * L'importance de la loi et de la frustration dans l'éducation + [00:32:35][^4^][4] Le rôle des parents et des enseignants * La disparition de l'autorité et de la hiérarchie * La nécessité d'une alliance éducative entre l'école et la famille * L'importance du respect de l'autorité des enseignants + [00:39:01][^5^][5] Le harcèlement scolaire et la justice * Définition légale et formes de harcèlement * L'impact des réseaux sociaux sur le harcèlement * La vulnérabilité des victimes et l'importance de la prévention + [00:47:02][^6^][6] Les mesures et les lois contre le harcèlement * Statistiques et plans gouvernementaux * Le droit à l'éducation et la protection contre la violence * Les initiatives pour améliorer le climat scolaire et prévenir le harcèlement Résumé de la vidéo [00:56:29][^1^][1] - [01:14:14][^2^][2]:

Cette vidéo aborde le harcèlement et la violence à l'école, en se concentrant sur les aspects juridiques du harcèlement en France, notamment les changements apportés par la loi du 2 mars 2022. Elle explique les nouvelles dispositions du Code pénal français concernant le harcèlement scolaire, les peines encourues et les mesures à prendre pour prouver le harcèlement et obtenir justice.

Points forts: + [00:56:29][^3^][3] Cadre juridique du harcèlement * Discussion sur le Code pénal français et la loi du 2 mars 2022 * Explication des articles relatifs au harcèlement * Importance de la preuve et des démarches légales + [01:01:14][^4^][4] Cas judiciaire spécifique * Examen d'un jugement du tribunal pour enfants d'Épinal * Analyse de la causalité entre le harcèlement et le suicide * Mention d'un appel possible devant la cour d'appel + [01:07:58][^5^][5] Témoignage d'une mère * Récit d'une mère sur le harcèlement subi par sa fille * Difficultés rencontrées dans la prise en charge et la justice * Appel à des actions concrètes pour soutenir les victimes

Résumé de la vidéo [00:00:00][^1^][1] - [00:26:57][^2^][2]:

Cette vidéo présente le Conseil Économique, Social et Environnemental (CESE) en France, ses missions, sa composition et son impact sur la société. Le CESE est décrit comme un pont entre les citoyens et les pouvoirs publics, offrant une plateforme pour la démocratie participative et l'élaboration de politiques publiques.

Points forts: + [00:00:00][^3^][3] Rôle et missions du CESE * Conseille le gouvernement et le Parlement * Favorise la démocratie participative * Évalue l'efficacité des politiques publiques + [00:06:29][^4^][4] Composition du CESE * 175 conseillers issus de divers secteurs * Représentation de la société civile organisée * Groupes d'intérêt et affinités variés + [00:14:15][^5^][5] Débats et propositions * Discussions sur des sujets d'actualité et de société * Interventions des membres sur des thématiques variées * Propositions pour améliorer la vie quotidienne + [00:21:05][^6^][6] Inégalités de genre, crise climatique et transition écologique * Analyse de l'impact du genre sur les questions écologiques * Vulnérabilité des femmes face aux crises * Rôle des femmes dans la promotion de la durabilité Résumé de la vidéo [00:26:59][^1^][1] - [00:53:06][^2^][2]:

La vidéo présente une discussion sur les solutions pour construire une société durable et respectueuse de l'égalité de genre. Elle aborde l'écoféminisme, la mixité des métiers, et l'impact du changement climatique sur les femmes.

Points forts: + [00:27:02][^3^][3] L'écoféminisme * Parallèle entre la domination de la nature et celle des femmes * Vision d'une société sans patriarcat ni domination * Importance de renouer avec le vivant + [00:29:17][^4^][4] Les stéréotypes de genre * Impact des stéréotypes dès l'enfance * Influence sur la vie et le rapport à la nature * Nécessité de promouvoir la mixité des métiers + [00:31:18][^5^][5] L'égalité de genre dans les politiques publiques * Lien entre égalité de genre et action pour le vivant * Intégration des réalités de genre dans les solutions climatiques * Importance de la diplomatie féministe et du financement des associations féministes + [00:38:04][^6^][6] La participation des femmes à la lutte environnementale * Femmes comme actrices majeures de la lutte pour l'environnement * Changement de paradigme pour valoriser leurs compétences * Connexion entre les questions sociales et environnementales Résumé de la vidéo [00:53:08][^1^][1] - [01:17:09][^2^][2]:

La vidéo présente les solutions pour construire une société durable et respectueuse de l'égalité de genre, en se concentrant sur les impacts différenciés du changement climatique sur les femmes et les hommes. Elle souligne l'importance de l'intégration de l'égalité de genre dans les politiques environnementales et la nécessité d'une action concrète pour protéger les droits des femmes.

Points forts: + [00:53:08][^3^][3] Introduction et quiz * Présentation des recommandations principales * Quiz interactif pour évaluer les connaissances sur l'égalité de genre * Importance de l'égalité de genre dans la gestion des catastrophes + [01:00:04][^4^][4] Impact différencié du changement climatique * Les femmes sont affectées de manière disproportionnée par les catastrophes climatiques * Les crises climatiques augmentent les violences envers les femmes * Nécessité de soutenir les projets portés par les femmes + [01:05:03][^5^][5] Intégration de l'égalité de genre dans les politiques * La diplomatie féministe de la France et ses implications * L'importance de l'évaluation des engagements internationaux * La sécurité des femmes déplacées par les changements climatiques + [01:14:00][^6^][6] Conséquences des activités industrialisées * Les pays riches sont responsables des crises climatiques * Les pays en développement sont les plus touchés * Appel à la protection juridique des migrants environnementaux Résumé de la vidéo [01:17:11][^1^][1] - [01:39:37][^2^][2] :

Cette partie de la vidéo aborde les solutions pour construire une société durable et respectueuse de l'égalité de genre. Elle met en lumière l'intégration des questions de genre dans les politiques environnementales, l'importance de l'investissement public dans la transition écologique, et le rôle des collectivités territoriales et des entreprises dans la promotion de l'égalité de genre.

Points forts : + [01:17:11][^3^][3] Intégration du genre dans la fiscalité environnementale * Éviter de renforcer les inégalités existantes * Corriger les inégalités à travers les investissements publics * Stratégie française pour l'énergie et le climat + [01:18:00][^4^][4] Objectifs transversaux d'écologie et d'égalité * Intégrer les objectifs d'écologie et de réduction des inégalités * Documenter avec des données spécifiques au genre * Chaque euro dépensé doit également bénéficier à l'égalité de genre + [01:20:04][^5^][5] Politique de mobilité et impact sur les femmes * Exemple de la promotion du vélo et ses conséquences sur l'espace public * Nécessité pour les collectivités de croiser les thématiques d'environnement et de genre * Politiques inclusives comme celles de la Ville de Genève + [01:24:04][^6^][6] Inégalités professionnelles dans les métiers verdissants * Sous-représentation des femmes dans les secteurs émetteurs de gaz à effet de serre * Importance de l'inclusion des femmes dans la transition écologique * Lever les obstacles à la participation des femmes dans ces métiers Résumé de la vidéo [01:39:39][^1^][1] - [02:03:26][^2^][2] : La vidéo aborde les solutions pour construire une société durable et respectueuse de l'égalité de genre. Elle met en lumière les défis et les préconisations du Conseil Économique, Social et Environnemental (CESE) en France, notamment en matière d'accueil des réfugiés, de politiques publiques, de biodiversité, de pollution et de participation démocratique.

Points forts : + [01:40:00][^3^][3] Défis et réactions face à l'égalité de genre * Discussion sur les réactions négatives aux travaux sur le genre * Confusion entre genre masculin et masculinité * Importance de prévenir les réactions négatives + [01:41:06][^4^][4] Intégration des questions de genre dans les politiques environnementales * Lien entre biodiversité, pollution et inégalités de genre * Nécessité d'une approche intégrée et détaillée * Choix difficiles dans les axes de préconisation + [01:45:52][^5^][5] Accueil des réfugiés et prise en charge spécifique des femmes et des filles * Préconisation d'intégrer une jurisprudence dans le Code de l'entrée et du séjour des étrangers * Besoins spécifiques des femmes et des filles réfugiées * Importance de projets spécifiques et de soutien financier + [01:57:43][^6^][6] Importance des données ventilées par sexe pour les politiques publiques * Collecte de données pour mieux connaître et agir * Évaluation continue des outils existants * Nécessité d'améliorer l'index d'égalité professionnelle Résumé de la vidéo [02:03:29][^1^][1] - [02:29:31][^2^][2]:

La vidéo aborde les solutions pour construire une société durable respectant l'égalité des genres. Elle souligne l'importance de l'intégration des femmes dans les métiers verts, la nécessité d'une diplomatie féministe, et l'impact du changement climatique sur les femmes. Elle appelle à une meilleure représentation des femmes dans les décisions politiques et environnementales, et à l'adoption de politiques publiques sensibles au genre.

Points forts: + [02:03:29][^3^][3] Impact du changement climatique sur les femmes * Importance de la recherche sur les différences d'impact entre les sexes * Nécessité d'une meilleure représentation des femmes dans les métiers verts * Appel à une diplomatie féministe et à des politiques publiques adaptées + [02:06:00][^4^][4] Justice de genre et justice climatique * Lien entre la préservation de la planète et l'évolution de la société * La justice de genre comme élément central de la justice climatique * Les politiques publiques doivent intégrer l'égalité des sexes + [02:10:21][^5^][5] Rôle des femmes dans la lutte contre la crise climatique * Les femmes sont plus vulnérables et exposées aux catastrophes naturelles * Nécessité de reconnaître et promouvoir les innovations des femmes * Importance de l'égalité des sexes pour évoluer les politiques publiques + [02:15:16][^6^][6] Intégration du genre dans la transition écologique * Les inégalités de genre exacerbent l'impact de la crise climatique * Propositions pour intégrer le genre dans les stratégies d'adaptation climatique * Valorisation de l'action des femmes et leur intégration dans la prise de décision + [02:22:14][^7^][7] Engagement des femmes dans la transition écologique * Les femmes doivent être des actrices majeures dans la lutte contre le changement climatique * Nécessité d'une approche transversale des politiques climatiques et d'égalité * Importance de la collecte de données sexo-spécifiques pour informer les politiques + [02:27:00][^8^][8] Rôle des femmes dans l'agriculture et la production bio * Évolution du secteur agricole avec une augmentation des femmes chefs d'exploitation * Défis rencontrés par les femmes dans l'adaptation au changement climatique * L'émancipation économique des femmes comme objectif pour la justice sociale et climatique Résumé de la vidéo [02:29:33][^1^][1] - [02:42:34][^2^][2]:

Cette partie de la vidéo aborde les solutions pour construire une société durable et respectueuse de l'égalité de genre. Elle souligne l'importance d'intégrer les spécificités de genre dans les politiques nationales et internationales, en particulier en ce qui concerne les conséquences du dérèglement climatique sur les femmes. La vidéo met en avant la nécessité de sensibiliser et d'accompagner les acteurs économiques sur ces enjeux, ainsi que de lutter contre les stéréotypes de genre dans les métiers verts.

Points forts: + [02:29:33][^3^][3] Intégration des spécificités de genre * Importance dans les politiques face au climat * Impact disproportionné sur les femmes * Solutions portées par les femmes + [02:31:38][^4^][4] Sensibilisation et éducation * Importance de la sensibilisation dès l'école * Lutte contre les stéréotypes de genre * Mixité des métiers verts + [02:34:15][^5^][5] Données genrées et politiques publiques * Nécessité de données pour réduire les inégalités * Engagement dans de nouvelles politiques * Participation des femmes aux décisions + [02:36:28][^6^][6] Diplomatie féministe et développement durable * Spécificité des revendications des femmes * Importance de l'éducation et de la formation * Accès des femmes à tous les métiers

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Reply to the reviewers

Manuscript number: RC-2024-02393

Corresponding author(s): Katja Petzold

1. General Statements [optional]

We thank the reviewers for recognising the impact of our manuscript. The reviewers noted the novelty of the miRNA bulge structure, the importance of the three observed binding modes and their potential for use in future structure-based drug design, and the possible importance of the duplex release phenomenon. We are also thankful for the relevant and constructive feedback provided.

Our responses to the comments are written point by point in blue, and any changes in the manuscript are shown in red.

2. Description of the planned revisions

In response to Reviewer 1 - major comment 2

Some of the data is over-interpreted. For example, in Figure 3A, it is concluded that supplementary regions are more important for weaker seeds. Only two 8-mer seeds are present among the twelve target sites and thus it might be difficult to generalize.

We found the relationship between seed type and the effect of supplementary pairing in our data intriguing. To further investigate this effect, we tested whether it exists in published microarray data from HCT116 cells transfected with six different miRNAs (Linsley et al., 2007; Argawal et al., 2015). Here we found that the for the two miRNAs (miR-103 and miR-106b) where we see an impact of supplementary pairing, the difference is primarily driven by 7mer-m8 seeds.

Since the effect appears to be specific to the miRNA, we would like to test whether it can be observed for miR-34a in a larger dataset. Therefore, we plan to transfect HEK293T cells with miR-34a and analyse the mRNA response via RNAseq. We will repeat the analysis shown above, using the predicted number of supplementary pairs to categorise the dataset into groups with or without the effect of supplementary pairing. We will then compare the three seed types within these groups.

In response to Reviewer 2 - minor comment 1, "why was the 34-nt 3'Cy3-labeled miR34a complementary probe shifted up in the presence of AGO?".

We plan to investigate the upper band, which we hypothesise is a result of duplex release, using EMSA to ascertain whether the band height agrees with the size of the duplex.

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

Reviewer #1

Evidence, reproducibility and clarity

Sweetapple et al. Biophysics of microRNA-34a targeting and its influence on down-regulation

In this study, the authors have investigated binding of miR-34a to a panel of natural target sequences using EMSA, luciferase reporter systems and structural probing. The authors compared binding within a binary and a ternary complex that included Ago2 and find that Ago2 affects affinity and strengthens weak binders and weakens strong binders. The affinity is, however, generally determined by binary RNA-RNA interactions also in the ternary complex. Luciferase reporter assays containing 12 different target sites that belong to one of three seed-match types were tested. Generally, affinity is a strong contributor to repression efficiency. Duplex release, a phenomenon observed for specific miRNA-target complementarities, seems to be more pronounced when high affinity within the binary complex is observed. Furthermore, the authors use RABS for structural probing either in a construct in CIS or binding by the individual miRNA in TRANS or in a complex with Ago2. They find pronounced asymmetric target binding and Ago2 does not generally change the binding pattern. The authors observe one specific structural group that was unexpected, which was mRNA binding with bulged miRNAs, which was expected sterically problematic based on the known structures. MD simulations, however, revealed that such structures could indeed form.

This is an interesting manuscript that contributes to our mechanistic understanding of the miRNA-target pairing rules. The combination of affinity measurements, structural probing and luciferase reporters allow for a broad correlation of target binding and repression strength, which is a well-thought and highly conclusive approach. However, there are a number of shortcomings that are summarized below.

The manuscript is not easy to read and to follow for several reasons. First, many of the sub-Figures are not referenced in the text of the results section (1C, 1D, 2C, 4D), which is somewhat annoying. Figure 4A seems to be mis-labeled. Second, a lot of data is presented in suppl. Figures. It should be considered to move more data into the main text in order to make it easier for readers to evaluate and follow.

Thank you for bringing this to our attention. We have now revised the figure references accordingly.

We have relocated gel images of BCL2, WNT1, MTA2 and the control samples from Figure S3 and S4 to the main results (Figure 2A-B) to improve readability and provide controls and details that aid in clear understanding. Additionally, we have relocated panel C from Figure S6 to Figure 2C to enhance the clarity of our rationale for using polyuridine (pU) in our AGO2 binding assays.

The updated figure is shown below, with changes to the legend marked in red.

Figure 2. Binary and ternary____ complex binding affinities measured by EMSA. (A) Binary (mRNA:miR-34a) binding assays showing examples of BCL2, WNT1 and MTA2. (B) Ternary (mRNA:miR-34a-AGO2) binding assays showing examples of BCL2, WNT1, MTA2, and the three control targets PERFECT, SCRseed, and SCRall. The Cy5 labelled species is indicated with asterisk (*). F indicates the free labelled species (miR34a or mRNA), B indicates binary complex, and T indicates ternary complex. Adjacent titrations points differ two-fold in concentration, with maximum concentrations stated at the top right. Adjacent titration points for MTA2 differed three-fold to assess a wider concentration range. In theternary assay, miRNA duplex release from AGO2 was observed for amongst others BCL2, WNT1, PERFECT, and SCRseed (band indicated with B), while it was not observed for SCRall and MTA2. See Figures S3 and S4 for representative gel images for all targets. See Supplementary files 2 and 3 for all images and replicates. (C) Titrations with increasing miR-34a-AGO2 concentration against Cy5-labelled SCRall (left) or PNUTS (right) comparing the absence and presence of 20 μM polyuridine (pU) during equilibration. pU acted as a blocking agent, reducing nonspecific binding, as seen by the different KD,app values for SCRall and PNUTS after addition of 20 μM pU. Therefore, all final mRNA:miR-34a-AGO2 EMSAs were carried out in the presence of 20 μM pU. Labels are as stated above. (D) Individual binding profiles for each of the 12 mRNA targets assessed by electrophoretic mobility assay (EMSA). Each datapoint represents an individual experiment (n=3). Blue represents results for the binary complex, and green represents results for the ternary complex. Dotted horizontal lines represent the KD,app values, which are also stated in blue and green with standard deviations (units = nM). Note that the x-axis spans from 0.1 to 100,000 in CCND1, MTA2 and NOTCH2, whereas the remaining targets span 0.1 to 10,000.

Some of the data is over-interpreted. For example, in Figure 3A, it is concluded that supplementary regions are more important for weaker seeds. Only two 8-mer seeds are present among the twelve target sites and thus it might be difficult to generalize.

We have revised our wording to recognise that more 8-mer sites would be required to draw a stronger conclusion based on this hypothesis. This hypothesis would be interesting to confirm in a larger dataset but is unfortunately outside of the scope of this paper.

Our hypothesis also aligns with recent data from Kosek et al. (NAR 2023; Figure 2D) where SIRT1 with an 8mer and 7mer-A1 seed was compared. Only the 7mer-A1 was sensitive to mutations in the central region or switching all mismatched to WC pairs.

Page 21 now states:

"This result indicates that the impact of supplementary binding may be greater for targets with weaker seeds, as has been observed earlier in a mutation study of miR-34a binding to SIRT1 (Kosek et al., 2023), although a larger sample size would be needed to confirm this observation."

Furthermore, we found the relationship between seed type and the effect of supplementary pairing in our data intriguing. To further investigate this effect, we tested whether it exists in published microarray data from HCT116 cells transfected with six different miRNAs (Linsley et al., 2007; Argawal et al., 2015). Here we found that the for the two miRNAs (miR-103 and miR-106b) where we see an impact of supplementary pairing, the difference is primarily driven by 7mer-m8 seeds. We therefore plan to test whether the effect can be observed for miR-34a in a larger dataset. We have outlined our preliminary data and planned experiments in Section 2 - description of the planned revisions.

I did not understand why the CIS system shown in 4A is a good test case for miR-34a-target binding. It appears very unnatural and artificial. This needs to be rationalized better. Otherwise it remains questionable, whether these data are meaningful at all.

Thank you for pointing out the need for clearer rationalisation.

The TRANS construct, where the scaffold carries the mRNA targeting sequence, provides reactivity information for the mRNA side only, while the microRNA is bound within RISC, with the backbone protected by AGO2. Therefore, to gain information on the miR-34a side of each complex we used the CIS construct, which provides reactivity information from both the miRNA and mRNA. We used the miRNA and mRNA reactivities to calculate all possible secondary structures for the binary complex, and then compared these structures to the mRNA reactivity in TRANS to find which structure fitted the reactivity patterns observed in the ternary complex.

We have included an additional statement in the manuscript to clarify this point on pages 12-13:

"Two RNA scaffolds were used for each mRNA target; i) a CIS-scaffold: RNA scaffold containing both mRNA target and miRNA sequence separated by a 10 nucleotide non-interacting closing loop, and ii) a TRANS-scaffold: RNA scaffold containing only the mRNA target sequence, to which free miR-34a or the miR-34a-AGO2 complex was bound (Figure 4A). The CIS constructs therefore provided reactivity information on the miRNA side, which is lacking in the TRANS construct, and was used to complement the TRANS data."

It may be worthwhile noting that a non-interacting 10 nucleotide loop was inserted between then miRNA and mRNA of the CIS constructs, allowing the miRNA and mRNA strands to bind and release freely. The reactivity patterns of each mRNA:miRNA duplex were compared between CIS and TRANS, and showed similar base pairing (Figure 4D). Furthermore, we have previously compared the two scaffolds in our RABS methodology paper (Banijamali et al. 2022), where no differences were observed besides reduced end fraying in the CIS construct.

For the TRANS experiments, only one specific scaffold structure is used. This structure might impact binding as well and thus at least one additional and independent scaffold should be selected for a generalized statement.

For each construct, the potential of interaction with the scaffold was tested using the RNAstructure (Reuter & Mathews, 2010)package. Based on the results of this assessment, two different scaffolds were used for our TRANS experiments. The testing and use of scaffolds has now been clarified further on page 13:

"The overall conformation of each scaffold with the inserted RNA was assessed using the RNAstructure (Reuter & Mathews, 2010) package to ensure that the sequence of interest did not interact with the scaffold. If any interaction was observed between the RNA of interest and the scaffold, then the scaffold was modified until no predicted interaction occurred. The different scaffolds and their sequence details are shown in supplementary information (Table S1)."

We have previously examined the scaffold's effect on binding and structure during the development of the RABS method. We tested the same mRNA (SIRT1) in separate, independent scaffolds to verify the consistency of the results. An example of this can be found in the supplementary information (Figure S1a) of Banijamali et al. (2022).

Generally, it would be nice to have some more information about the experiments also in the result section. Recombinant Ago2 is expressed in insect cells and re-loaded with miR-34a, luciferase reporters are transfected into tissue culture cells, I guess.

We have now stated the cell types used for AGO2 expression and luciferase reporter assays in the results.

On page 17 we have included:

"Samples of each of the 12 mRNA targets, as well as miR-34a and AGO2, were synthesised in-house for biophysical and biological characterisation. Target mRNA constructs were produced via solid-phase synthesis while miR-34a was transcribed in vitro and cleaved from a tandem transcript (Feyrer et al., 2020), ensuring a 5' monophosphate group. AGO2 was produced in Sf9 insect cells."

"To measure the affinity of each mRNA target binding to miR-34a, both within the binary complex (mRNA:miR-34a) and theternary complex (mRNA:miR-34a-AGO2), we optimised an RNA:RNA binding EMSA protocol to suit small RNA interactions. The protocol is loosely based on Bak et al. (2014)36, with major differences being use of a sodium phosphate buffering system so as not to disturb weaker interactions (James et al., 1996; Stellwagen et al., 2000), supplemented with Mg2+ as a counterion to reduce electrostatic repulsion between the two negatively charged RNAs (Misra & Draper, 1998), and fluorescently labelled probes."

Page 19:

" We successfully tested various RNA backgrounds, including polyuridine (pU) and total RNA extract (Figure S6B) to block any unspecific binding. Ultimately, we supplemented our binding buffer with pU at a fixed concentration of 20 µM for the ternary assays to achieve the greatest consistency."

Page 20:

"Repression efficacy for the 12 mRNA targets by miR-34a was assessed through a dual luciferase reporter assay6. Target mRNAs were cloned into reporter constructs and transfected into HEK293T cells."

Page 22:

"To infer base pairing patterns and secondary structure for each of the 12 mRNA:miR-34a pairs, we used the RABS technique (Banijamali et al., 2023) with 1M7 as a chemical probe. All individual reactivity traces are shown in Figure S9. Reactivity of each of the 22 miR-34a nucleotides was assessed upon binding to each of the 12 mRNA targets within a CIS construct, containing both miR-34a and the mRNA target site separated by a non-interacting 10-nucleotide loop. The two RNAs can therefore bind and release freely within the CIS construct and reactivity information is collected from both RNA strands."

In the first sentence of the abstract, Argonaute 2 should be replaced by Argonaute only since other members bind to miRNAs as well.

Thank you for recognising this. It has now been corrected.

Significance

This is an interesting manuscript that contributes to our mechanistic understanding of the miRNA-target pairing rules. The combination of affinity measurements, structural probing and luciferase reporters allow for a broad correlation of target binding and repression strength, which is a well-thought and highly conclusive approach. However, there are a number of shortcomings.

We thank the reviewer for recognising the approach and impact of our work. In addition we thank the reviewer for identifying the need for further data to support our conclusions from the luciferase assays, which is something that we plan to address, as described in section 2.

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Reviewer #2

Evidence, reproducibility and clarity

Summary: Sweetapple et al. took the approaches of EMSA, SHAPE, and MD simulations to investigate target recognition by miR-34a in the presence and absence of AGO2. Surprisingly, their EMSA showed that guide unloading occurred even with seed-unpaired targets. Although previous studies reported guide unloading, they used perfectly complementary guide and target sets. The authors of this study concluded that the base-pairing pattern of miR-34a with target RNAs, even without AGO2, can be applicable to understanding target recognition by miR-34a-bound AGO2.

Major comments:

(Page 11 and Figure S4) The authors pre-loaded miR-34a into AGO2 and subsequently equilibrated the RISC with a 5' modified Cy5 target mRNA. Since properly loaded miR-34a is never released from AGO2, it is impossible for the miR-34a loaded into AGO2 to form the binary complex (mRNA:miR-34a) in the EMSA (guide unloading has been a long-standing controversy). However, they observed bands of the binary complex in Figure S4. The authors did not use ion-exchange chromatography. AGOs are known to bind RNAs nonspecifically on their positively charged surface. Is it possible that most miR-34a was actually bound to the surface of AGO2 instead of being loaded into the central cleft? This could explain why they observed the bands of the binary complex in EMSA.

Thank you for mentioning this crucial point which has been a focus of our controls. We have addressed this point in four ways:

Salt wash during reverse IMAC purification. Separation of unbound RNA and proteins via SEC. Blocking non-specific interactions using polyuridine. Observing both the presence and absence of duplex release among different targets using the same AGO2 preparation and conditions.

Firstly, although we did not use a specific ion exchange column for purification, we believe the ionic strength used in our IMAC wash step was sufficient to remove non-specific interactions. We used A linear gradient with using buffer A (50 mM Tris-HCl, 300 mM NaCl, 10 mM Imidazole, 1 mM TCEP, 5% glycerol v/v) and buffer B (50 mM Tris-HCl, 500 mM NaCl, 300 mM Imidazole, 1 mM TCEP, 5% glycerol) at pH 8. The protocol followed recommendation by BioRad for their Profinity IMAC resins where it is stated that 300 mM NaCl should be included in buffers to deter nonspecific protein binding due to ionic interactions. The protein itself has a higher affinity for the resin than nucleic acids.

A commonly used protocol for RISC purification follows the method by Flores-Jasso et al. (RNA 2013). Here, the authors use ion exchange chromatography to remove competitor oligonucleotides. After loading, they washed the column with lysis buffer (30 mM HEPES-KOH at pH 7.4, 100 mM potassium acetate, 2 mM magnesium acetate and 2 mM DTT). AGO was eluted with lysis buffer containing 500 mM potassium acetate. Competing oligonucleotides were eluted in the wash.

As ionic strength is independent of ion identity or chemical nature of the ion involved (Jerermy M. Berg, John L. Tymoczko, Gregory J. Garret Jr., Biochemistry 2015), we reasoned that our Tris-HCl/NaCl/ imidazole buffer wash should have at comparable ionic strength to the Flores-Jasso protocol.

Our total ionic contributions were: 500 mM Na+, 550 mM Cl-, 50 mM Tris and 300 mM imidazole. We recognise that Tris and imidazole are both partially ionized according the pH of the buffer (pH 8) and their respective pKa values, but even if only considering the sodium and chloride it should be comparable to the Flores-Jasso protocol.

We have restated the buffer compositions below written the methods section more explicitly to describe this:

"Following dialysis, any precipitate was removed by centrifugation, and the resulting supernatant was loaded onto a IMAC buffer A-equilibrated HisTrap-Ni2+ column to remove TEV protease, other proteins, and non-specifically bound RNA. A linear gradient was employed using IMAC buffers A and B."

Secondly, after reverse HisTrap purification, AGO2 was run through size exclusion chromatography to remove any remaining impurities (shown Figure S2B).

Thirdly, knowing that AGO2 has many positively charged surface patches and can bind nucleic acid nonspecifically (Nakanishi, 2022; O'Geen et al., 2018), we tested various blocking backgrounds to eliminate nonspecific binding effects in our EMSA ternary binding assays. We were able to address this issue by adding either non-homogenous RNA extract or homogenous polyuridine (pU) in our EMSA buffer during equilibration background experiments. This allowed us to eliminate non-specific binding of our target mRNAs, as shown previously in Supplementary Figure S6. We appreciate that the reviewer finds this technical detail important and have moved the panel C of figure S6 into the main results in Figure 2C, to highlight the novel conditions used and important controls needed to be performed. If miR-34a were non-specifically bound to the surface of AGO2 after washing, this blocking step would render any impact of surface-bound miR-34a negligible due to the excess of competing polyuridine (pU).

Our EMSA results show that, using polyU, we can reduce non-specific interaction between AGO2 and RNAs that are present. And still, duplex release occurs despite the blocking step. It is therefore less likely that duplex release is caused by surface-bound miR-34a.

Finally, the observation of distinct duplex release for certain targets, but not for others (e.g. MTA2, which bound tightly to miR-34a-AGO2 but did not exhibit duplex release; see Figure 2), argues against the possibility that the phenomenon was solely due to non-specifically bound RNA releasing from AGO2.

In response to the reviewers statement "Since properly loaded miR-34a is never released from AGO2, it is impossible for the miR-34a loaded into AGO2 to form the binary complex (mRNA:miR-34a)" we would like to refer to the three papers, De et al. (2013) Jo MH et al. (2015), and Park JH et al. (2017), which have previously reported duplex release and collectively provide considerable evidence that miRNA can be unloaded from AGO in order to promote turnover and recycling of AGO. It is known that AGO recycling must occur, therefore there must be some mechanisms to enable release of miRNA from AGO2 to enable this. It is possible that AGO recycling proceeds via miRNA degradation (TDMD) in the cell, but in the absence of enzymes responsible for oligouridylation and degradation, the miRNA duplex may be released. As TDMD-competent mRNA targets have been observed to release the miRNA 3' tail from AGO2 (Sheu-Gruttadauria et al., 2019; Willkomm et al., 2022), there is a possible mechanistic similarity between the two processes, however, we do not have sufficient data to make any statement on this.

(Page 18 and Figure S5) Previous studies (De et al., Jo MH et al., Park JH et al.) reported guide unloading when they incubated a RISC with a fully complementary target. However, neither MTA2, CCND1, CD44, nor NOTCH2 can be perfectly paired with miR-34a (Figure 1A). Therefore, the unloading reported in this study is quite different from the previously reported works and thus cannot be explained by the previously reported logic. The authors need to explain the guide unloading mechanism that they observed. Otherwise, they might misinterpret the results of their EMSA and RABS of the ternary complex.

The three aforementioned studies have reported unloading/duplex release. However, they did not only report fully complementary targets in this process.

De et al. (2013) reported that "highly complementary target RNAs promote release of guide RNAs from human Argonaute2".

Subsequently, Park et al. (2017) reported: "Strikingly, we showed that miRNA destabilization is dramatically enhanced by an interaction with seedless, non-canonical targets."

A figure extracted from Figure 5 of Park et al. is shown below illustrating the occurrence of unloading in the presence of seed mismatches in positions 2 and 3 (mm 2-3). Jo et al. (2015) also reported that binding lifetime was not affected by the number of base pairs in the RNA duplex.

In addition to these three reports, a methodology paper focusing on miRNA duplex release was published recently titled "Detection of MicroRNAs Released from Argonautes" (Min et al., 2020).

Therefore, we do believe that the previously observed microRNA release is similar to our observation. Here we also correlate it to structure and stability of the complex.

(Page 20) The authors reported, "it is notable that the seed region binding does not appear to be necessary for duplex release." The crystal structures of AGO2 visualize that the seed of the guide RNA is recognized, whereas the rest is not, except for the 3' end captured by the PAZ domain. How do the authors explain the discrepancy?

In this manuscript, we intend to present our observations of duplex release. There are many potential relationships between duplex release and AGO2 activity, which we do not have data to speculate upon. Previous studies, such as Park et al. (2017) have also observed non-canonical and seedless targets leading to duplex release, supporting our findings. Additionally, other publications including McGearly et al. (2019) report 3'-only miRNA targets, Lal et al. (2009) have documented seedless binding by miRNA and their downstream biological effects, and Duan et al. (2022) show that a large number of let-7a targets are regulated through 3′ non-seed pairing.

It is also possible that duplex release is not coupled to classical repression outcomes, and does not need to proceed by the seed, but instead regulates AGO2 recycling before AGO2 enters the quality control mode of recognising the formed seed.

(Pages 22) The authors mentioned, "It follows that the structure imparted via direct RNA:RNA interaction remains intact within AGO2, highlighting the role of RNA as the structural determinant." A free guide and a target can start their annealing from any nucleotide position. In contrast, a guide loaded into AGO needs to start annealing with targets through the seed region. Additionally, the Zamore group reported that the loaded guide RNA behaves quite differently from its free state (Wee et al., Cell 2012). How do the authors explain the discrepancy?

The key point we would like to emphasise is that AGO does not seem to alter the underlying RNA:RNA interactions. The bound state in the ternary complex reflects the structure established in the binary complex. We do not aim to claim a specific sequence of events, as this interpretation is not possible from our equilibrium data. Our data indicates that the protein is flexible enough to accommodate the RNA structure that is favoured in the binary complex. This hypothesis is further supported by our MD simulation, which demonstrates the accommodation of a miRNA-bulge structure within AGO2.

Targets lacking seeds have been identified previously (McGeary et al. 2019, Park et al. 2017, Lal et al. 2009) and can bind to miRNA within AGO. Therefore, there must be a mechanism by which these targets can anneal within AGO, such as via sequence-independent interactions (as discussed in question 3).

With respect to Wee et al., (2012), which studied fly and mouse AGO2 and found considerable differences between the thermodynamic and kinetic properties of the two AGO2 species. Furthermore, they found different average affinities between the two species, with the fly AGO binding tighter the mouse. Following this logic, it is not unexpected that human AGO2 would have unique properties compared to those of fly and mouse.

Below is an extract from Wee et al., (2012):

"Our KM data and published Argonaute structures (Wang et al., 2009) suggest that 16-17 base pairs form between the guide and the target RNAs, yet the binding affinity of fly Ago2-RISC (KD = 3.7 {plus minus} 0.9 pM, mean {plus minus} S.D.) and mouse AGO2-RISC (KD = 20 {plus minus} 10 pM, mean {plus minus} S.D.) for a fully complementary target was comparable to that of a 10 bp RNA:RNA helix. Thus, Argonaute functions to weaken the binding of the 21 nt siRNA to its fully complementary target: without the protein, the siRNA, base paired from positions g2 to g17, is predicted to have a KD ∼3.0 × 10−11 pM (ΔG25{degree sign}C = −30.7 kcal mol−1). Argonaute raises the KD of the 16 bp RNA:RNA hybrid by a factor of > 1011."

In the Wee et al. (2012) paper, affinity data on mouse and fly AGO2 was collected via filter binding assays, using a phosphorothioate linkage flanked by 2′-O-methyl ribose at positions 10 and 11 of the target to prevent cleavage. They then compared the experimentally determined mean KD and ΔG values for each species to predicted values of an RNA:RNA helix of 16-17 base-pairs. No comparison was made between individual targets, and no experimental data was collected for the RNA:RNA binding. The calculated energy values were made based on a simple helix without taking into account any possible secondary structure features. Considering the different AGO species, alternative experimental setup, modified nucleotides in the tested RNA, and the computationally predicted RNA values compared to the averaged experimental values, we believe there is considerable reason to observe differences compared to our findings.

We have expanded our discussion on page 27 to the following:

"An earlier examination of mRNA:miRNA binding thermodynamics by Wee and colleagues (2012) found that mouse and fly AGO2 reduce the affinity of a guide RNA for its target61. Our data indicate that the range of miR-34a binary complex affinities is instead constricted by human AGO2 in the ternary complex - strengthening weak binders while weakening strong binders. The 2012 study reported different average affinities between the two AGO2 species, with the fly protein binding tighter the mouse. Following this logic, it is not unexpected that human AGO2 would have unique properties compared to those of fly and mouse."

The authors concluded that the range of binary complex affinities is constricted by human AGO2 in the ternary complex - strengthening weak binders while weakening strong binders. This may hold true for miR-34a, but it cannot be generalized. Other miRNAs need to be tested.

That is true, we have now adjusted the wording to encompass this more clearly, shown below. Testing of further miRNAs is the likely content of future work from us and others.

"Our data indicate that the range of miR-34a binary complex affinities is instead constricted by human AGO2 in the ternary complex - strengthening weak binders while weakening strong binders."

Minor comments:

(Figure S2) Why was the 34-nt 3'Cy3-labeled miR34a complementary probe shifted up in the presence of AGO?

We believe this observation is also indicative of duplex release. At the time that these activity assays were collected, we were not as aware of the presence of duplex release so did not test it further, assuming it may be due to transient interactions. We plan to investigate this via EMSA and have included this in the planned revisions (section 2).

2.(Page 17) Does the Cy3 affect the interaction of the 3' end of miR-34 with AGO2?

miR-34a-3'Cy5 was used for binary experiments only and the reverse experiment was conducted as a control (where Cy5 was located on the mRNA) (Figure S3b), showing no change in affinity/interaction when the probe was switched to the target. For ternary experiments the mRNA target was labelled on the 5' terminus, to make sure there was no interference with loading miR-34a into AGO2.

A Cy3 labelled RNA probe (fully complementary to miR-34a) was used to detect miR-34a in northern blots, but AGO2 interaction is not relevant here under denaturing conditions.

Otherwise, the 34-nt slicing probe had Cy3 on the 5 nt 3' overhang and should therefore not interact with AGO.

1. Several groups reported that overproduced AGOs loaded endogenous small RNAs. The authors should mention that their purified AGO2 was not as pure as a RISC with miR-34a. Otherwise, readers might think that the authors used a specific RISC.

We have now improved our explanation of the loading efficiency to make it more clear to the reader that our AGO2 sample was not fully bound by miR-34a, and that all concentrations refer to the miR-34a-loaded portion of AGO2. The following text can be found in the results on page 18:

"The mRNA:miR-34a-AGO2 assay had a limited titration range, reaching a maximum miR-34a-AGO2 concentration of 268 nM due to a 5% loading efficiency (see Figure S2D for loading efficiency quantification). The total AGO2 concentration was thus 20-fold higher than the miR-34a-loaded portion. Further increase in protein concentration was prevented by precipitation. Weaker mRNA targets (CD44, CCND1, and NOTCH2) did not reach a saturated binding plateau within this range, leading to larger errors in their estimated KD,app values. However, reasonable estimation of the KD,app was possible by monitoring the disappearance of the free mRNA probe. Note that we refer to the miR-34a-loaded portion of AGO2 when discussing concentration values for all titration ranges. To ensure AGO2 binding specificity despite low loading efficiency, a scrambled control was used (SCRall; lacking stable base pairing with miR-34a or other human miRNAs according to the miRBase database57). SCRall showed no interaction with miR-34a-AGO2 (Figure 2B)."

(Figure legend of Figure S5) Binding was assessed "by."

Thank you for pointing this out, it is now fixed.

(Page 17) It would be great if the authors could even briefly describe the mechanism by which the sodium phosphate buffer with magnesium does not disturb weaker interactions by citing reference papers.

We have now added a supplementary methods section to our manuscript and included the description below on page 10:

"We found that a more traditional Tris-borate-EDTA (TBE) buffer disrupted weaker RNA:RNA binding interactions (Supplementary Methods Figure M1). Borate anions form stable adducts with carbohydrate hydroxyl groups (James et al., 1996) and can form complexes with nucleic acids, likely through amino groups in nucleic bases or oxygen in phosphate groups (Stellwagen et al., 2000). This makes TBE unsuitable for assessment of RNA binding, particularly involving small RNA molecules, which typically have weaker affinities. We therefore adapted our buffer system to a sodium phosphate buffer supplemented with magnesium. Magnesium acts as a counterion to reduce electrostatic repulsion between the two negatively charged backbones by neutralisation (Misra et al., 1998)."

We have also clarified the buffer adaptions in our results section on page 17:

The protocol is loosely based on Bak et al. (2014)36, with major differences being use of a sodium phosphate buffering system so as not to disturb weaker interactions(James et al., 1996; Stellwagen et al., 2000), supplemented with Mg2+ as a counterion to reduce electrostatic repulsion between the two negatively charged RNAs(Misra & Draper, 1998), and fluorescently labelled probes. Original gel images and quantification are shown in supplementary Figures S3 and S4. All KD,app values are shown in Supplementary Table 1, and represent the mean of three independent replicates.

Figure M1. Comparison of Tris-borate EDTA (TBE) and sodium phosphate with magnesium (NaP-Mg2+) buffer systems for EMSA. Cy5-labelled miR-34a and unlabelled CD44 were equilibrated in the two different buffer systems, using the same titration range. No mobility shifts were observed in the TBE system, while clear binding shifts were observed in the NaP-Mg2+ system.

6.(Page 22) The authors cited Figure 4C in the sentence, "Comparison between CIS and TRANS ..." Is this supposed to be Figure 4D?

The reviewer was correct in their assumption, and this has now been corrected.

7.(Figure 6) Readers would appreciate it if the guide and target were colored in red and blue. The color codes have been used in most papers reporting AGO structures. The current color codes are opposite.

We have now adjusted the colour schemes throughout the manuscript, and Figure 6 has been modified to the following:

__"Figure 6. The miRNA-bulge structure is readily accommodated by AGO2 as shown by molecular dynamics simulation. __Panel (A) displays a snapshot of the all-atom MD simulation of miR-34a (red) and NOTCH1 (blue) in AGO2. The NOTCH1:miR-34a duplex is shown with AGO2 removed for clarity and is rotated 90{degree sign} to show the miRNA bulge and bend in the duplex. This NOTCH1:miR-34a-AGO2 structure is compared with (B), which shows the crystal structure of miR-122 (orange) paired with its target (purple) via the seed and four nucleotides in the supplementary region (PDB-ID 6N4O17), and (C), which shows the crystal structure of miR-122 (orange) and its target (green) with extended 3' pairing, necessary for the TDMD-competent state (PDB-ID 6NIT19). AGO2 is depicted in grey, with the PAZ domain in green, and the N-terminal domain marked with N. The miRNA duplexes in (B) and (C) feature symmetrical 4-nucleotide internal loops, whereas the NOTCH1 structure in (A) has an asymmetrical miRNA bulge with five unpaired nucleotides on the miRNA side and a 3-nucleotide asymmetry."

Significance

This paper will have a significant impact on the field if seed-unpaired targets can indeed unload guide RNAs. The authors may want to validate their results very carefully.

We thank the reviewer for recognising the significance of duplex release (or guide unloading) from AGO2. We agree that the observations should be tested rigorously and have outlined the actions we took to ensure validity in our AGO2 preparation.

__Reviewer #3 __

Evidence, reproducibility and clarity (Required):

In this manuscript, the authors use a combination of biochemical, biophysical, and computational approaches to investigate the structure-function relationship of miRNA binding sites. Interestingly, they find that AGO2 weakens tight RNA:RNA binding interactions, and strengthens weaker interactions.

Given this antagonistic role, I wonder: shouldn't there be an 'average' final binding affinity? Furthermore, if I understand correctly, not many trends were observed to correlate binding affinity with repression, etc.

Overall, there was no 'average' final binding affinity observed, as the binary assays had a much higher maximum (NOTCH2binary affinity was within the micromolar range) skewing the mean average of the binary affinities to 657 nM, versus 111 nM for the ternary affinities. We also compare the variances of the binary and ternary affinity datasets using the F-test and found that F > F(critical one tail) and thus the variation of the two populations is unequal (binary variation is significantly larger than ternary).

F-Test Two-Sample for Variances

• *

binary affinity

ternary affinity

Mean

657.3

110.971667

Variance

2971596.1

24406.4012

Observations

12

12

df

11

11

F

121.754784

P(F

7.559E-10

F(critical one-tail)

2.81793047

We agree that the overall correlation between affinity and repression was not strong, although we found a stronger correlation within the miRNA-bulge group (Figure 5C and S7C). A larger sample size of miRNA bulge-forming duplexes would be needed to test the generalizability of this observation.

Given the context of the study - whereby structure is being investigated as a contributing factor to the interaction between the miRNA and mRNA, I find it interesting that the authors chose to use MC-fold to predict the structures of the mRNA, rather than using an experimental approach to assess / validate the structures. Thirty-seven RNAs were assessed; I think even for a subset (the 12 that were focused on in the study), the secondary structure should be validated experimentally (e.g., by chemical probing experiments, which the research group has demonstrated expertise in over the last several years). The validation should follow the in silico folding approach used to narrow down the region of interest. It is necessary to know whether an energy barrier (associated with the mRNA unfolding) has to occur prior to miRNA binding; this could help explain some of the unexplained results in the study. Indeed, the authors mention that there are many variables that influence miRNA regulation.

Indeed, experimentally validated structures offer valuable insights that cannot be obtained solely through sequence-based predictions. This is why we opted to employ our RABS method to experimentally evaluate the binary and ternary complex binding of our 12 selected targets (as depicted in Figures 4 and S9 and discussed in the text on pages 23-24). While we (in silico) assessed all 37 RNA targets that were experimentally confirmed at the time, selecting 12 to represent both biological and predicted structural diversity, it would have been impractical to experimentally pre-assess all the targets not included in the final selection. Our in-silico assessment was designed to narrow down the regions of interest and evaluate predicted secondary structures present. The pipeline is shown in Figure 1. Details of the code used in the in-silico analysis are provided in Supplementary File 1.

Regarding the energy of unfolding of mRNA, our constructs considered the isolated binding sites thus the effects of surrounding mRNA interactions were removed. We compared our affinities to dG as well as MFE and have now included this analysis in Figure S8A. Additionally, we have included the text on page 27-28 of the discussion:

"Gibbs free energy (G), which is often included in targeting prediction models as a measure of stability of the miRNA:mRNA pair12,62, correlated with the log of our binary KD,app values, using ΔG values predicted by RNAcofold (R2 = 0.61). There was a weaker correlation with the free energy values derived from the minimum free energy (MFE) structures predicted by RNAcofold (R2 = 0.41) (Figure S8A). This result highlights the contribution of unfolding (in ΔG) as being an important in predicting KD. The differences between ΔG and KD,app are likely primarily due to inaccurately predicted structures used for energy calculations."

Additionally, we assessed the free form of all mRNA targets via RABS (Figure S9) and observed that the seed of each free mRNA was available for miRNA binding (seeds of the free mRNA were not stably bound).

Finally, when designing our luciferase plasmids we used RNAstructure (Reuter & Mathews, 2010) to check for self-folding effects which could interfere with target site binding and ensured that all plasmids were void of such effects.

In the methods, T7 is italicized by accident in the T7 in vitro transcription section. Bacmid is sometimes written with a capital B and other times with a lower-cased b. The authors should be consistent. The concentration of TEV protease that was added (as opposed to the volume) should be described for reproducibility.

Thank you for pointing out these overlooked points. They have now been corrected.

In figure S2D, what is the second species in the gel on the right-hand side of the gel in the miR-34a:AGO lanes? The authors should mention this.

We believe that the faint upper band corresponds to other longer RNA species loaded into AGO2. As AGO2 is loaded with a diversity of RNA species, it is likely that some of them may have a weak affinity for the miR-34a-complementary probe, and therefore show up on the northern blot.

Figure S3B and S3A are referenced out of order in the text. In regard to S3A, what are the anticipated or hypothesized alternative conformations for NOTCH1, DLL1, and MTA2? There are really interesting things going on in the gels, also for HNF4a and NOTCH2. Can the authors offer some explanation for why the free RNA bands don't seem to disappear, but rather migrate slowly? Is this a new species?

The order of the figure references have now been updated, thank you for alerting us to this.

Figure S3A: For MTA2, the two alternative conformations are shown in Figure S9 and S10 (and shown below here, miR-34aseed marked in pink). It appears that a single conformation is favoured at high concentration (> 1 µM) while the two conformations are present at {less than or equal to} 1 µM. The RABS data for MTA2 also indicated multiple binding conformations, as the reactivity traces were inconsistent. We expect that the conformation shown on the left was most dominant within AGO2, based on the reactivity of the TRANS + AGO assays. However, we cannot exclude a possible G-quadruplex formation due to the high G content of MTA2 (shown below right).

Regarding NOTCH1 and DLL1, a faint fluorescent shadow was observed beneath the miR-34a bound band. The RABS reactivity traces indicated a single dominant conformation for these targets, so it is possible that the lower shadow observed was due to more subtle differences in conformation, such as the opening/closing of one or a few base pairs at the terminus or bulge, (i.e. end fraying). HNF4α and NOTCH2 appear to never fully saturate the miR-34a, so a small un-bound population remains visible on the gel. For NOTCH2 this free miR-34a band appears to migrate upwards, possibly due to overloading the gel lane with excess NOTCH2 (which are not observed in the Cy5 fluorescence image).

In the EMSA for Perfect, why does the band intensity for the bound complex increase then decrease? How many replicates were run for this? This needs to be reconciled.

As for all EMSAs, three replicates were carried out for each mRNA target and all gels are shown in Supplementary Files 2 and 3, for the binary and ternary assays respectively.

Uneven heat distribution across the gel can lead to bleaching of the Cy5 fluorophore. To address this, we we used a circulating cooler in our electrophoresis tank, as outlined in our methods (page 10). However, the aforementioned gel for one of thePERFECT sample replicates appears to have been evenly cooled. As the binding ratio (rather than total band volume) was used for quantification, the binding curve was unaffected, and this did not influence KD,app.

We have now replaced the exemplary gel for PERFECT in Figure S3 with a more representative and evenly labelled gel from our replicates (Cy5 fluorescence image shown below). The binding curve for PERFECT is also shown here:

The authors list that the RNA concentration was held constant at 10 nM; in EMSAs, the RNA concentration should be less than the binding affinity; what is the lowest concentration of protein used in the assays shown in S3A? Is this a serial dilution? It seems to me like the binding assays for MTA2, Perfect, and SRCseed might have too high of an RNA concentration. (Actually, now I see in the supplement the concentrations of proteins, and the RNA concentration is too high). Also, why is the intensity of bands for bound complex for SRCseed more intense than the free RNA?

Why are the binding affinity error bars so large (e.g., for NOTCH2 with mir-34a) - 6 uM +/- 3 uM?

No protein was used in the binary assays shown in Figure S3A. For the ternary assays in Figure S4, the maximum concentration of miR-34a-loaded AGO2 (miR-34a-AGO2) was 268 nM, with a serial dilution down to a minimum of 0.06 nM.

Optimal EMSA conditions require a constant RNA concentration that is lower than the binding affinity to accurately estimate high-affinity interactions.

For our tightest binders, such as SIRT1, we can confidently state that the KD,app is less than 10 nM, estimated at 0.4 {plus minus} 1.1 nM. Therefore, the accuracy of this estimation is reduced, and the standard deviation is larger than the estimated KD,app. As NOTCH2 bound miR-34a very weakly and did not reach a fully bound plateau, the resulting high error was expected. Consequently, we do not have the same level of certainty for extremely tight or weak binders. In this study, the relative affinities were of primary importance.

We have included on page 18:

As the Cy5-miR-34a concentration was fixed to 10 nM to give sufficient signal during detection, KD,app values below 10 nM have a lower confidence.

Regarding the control samples PERFECT and SCRseed, our focus was not on determining the exact KD,app of these artificial constructs. Instead, we were primarily interested in whether they exhibited binding and under which conditions. For SCRseed, we neither adjusted the titration range nor calculated KD,app. For PERFECT, the concentration was adjusted to a lower range of 30 nM - 0.001 nM to give a relative comparison with the other tight binder SIRT1. However, further reduction in RNA concentration was not pursued, as it already fell well below the 10 nM sensitivity threshold.

Regarding the intensity of the bound SCRseed band, we observed that the bound fluorophore often resulted in stronger intensity than for the free probe. This was observed for a number of the samples (PERFECT, BLC2, SCRseed). A previous publication reported that Cy5 is sequence dependent in DNA, that the effect is more sensitive to double-stranded DNA, and that the fluorophore is sensitive to the surrounding 5 base pairs (Kretschy, Sack and Somoza, 2016). It is likely that the same phenonenon exists in RNA.

For MTA2, the two alternative conformations (shown in Figure S9 and S10) make assessment of KD,app more difficult. As the higher affinity conformation did not reach a fully-bound plateau before the weaker affinity conformation appeared, the binding curve plateau (where all miR-34a was bound) reflected the weaker conformation KD,app. We increased the range of titration tested by using a three-fold serial dilution, but further reduction in RNA concentration would not have been fruitful as it already dropped below well below the 10 nM sensitivity range. Therefore the MTA2 binary complex had a higher error at (944 {plus minus} 274 nM) and lower confidence.

We then decided to run a competition assay to detect the weaker KD,app of MTA2. The assay was set up using the known binding affinity of CD44, which was labelled with Cy5 to track the reaction. MTA2 was titrated against a constant concentration of Cy5-CD44:miR-34a, and disruption of the CD44 and miR-34a binding was monitored. We fitted the data to a quadratic for competitive binding (Cheng and Prusoff., 1973) to calculate the KD,app for competitive binding, or KC,app.

We validated our competition assay by comparing it with our direct binding assays, specifically assessing CD44 in a self-competition assay. The CD44 KC,app (168 {plus minus} 24 nM; mean and SD of three replicates) was found to be consistent with the KD,app obtained from the direct assay (165 {plus minus} 21 nM).

As we wanted all affinity data to be directly comparable (using the same methodology), we compared the KD,app values obtained via direct assay in the manuscript. It appears that the competitive EMSA assay for MTA2 reflects the weaker affinity conformation observed in the direct assay.

It would be very helpful if the authors wrote in the Kds in Figure 2A in green and blue (in the extra space in the plots). This would help the reader to better understand what's going on, and for me, as a reviewer, to better consider the analysis/conclusions presented by the authors.

KD,app values are written in in green and blue in what is now Figure 2D (originally Figure 2A).

The authors state on page 18 that 'Interestingly, however, we did not observe a correlation between binary or ternary complex affinity and seed type.' They should elaborate on why this is interesting.

The prevailing view is that the miRNA seed type significantly influences affinity within AGO2. The largest biochemical studies of miRNA-target interactions to date, conducted by McGeary et al. (2019, 2022), used AGO-RBNS (RNA Bind-n-Seq) to reveal relative binding affinities. These studies demonstrated strong correlations between the canonical seed types and binding affinity. Therefore, we find it interesting that no such correlation was observed in our dataset (despite its small size).

We have now added to the manuscript (page 20):

"The largest biochemical studies of miRNA-target interactions to date (McGeary et al., 2019, 2022) used AGO-RBNS (RNA Bind-n-Seq) to extract relative binding affinities, demonstrating strong correlations between the canonical seed types and binding affinity. Therefore, it is intriguing that our dataset, despite its small size, showed no such correlation."

Figure 2C is not referenced in the text (the authors should go back through the text to make sure everything is referenced and in order). The Kds should be listed alongside the gels in Figure 2C.

Figure 2 has now been rearranged and updated, with KD,app values listed in what is now Figure 2D.

Figure 3B is rather confusing to understand.

We have now adapted Figure 3 to simplify readability. Panel B has now been moved to C, and we have introduced panel A (moved from Figure 2B). In Figure 3C (originally 3B) we have added arrows to indicate the direction of affinity change from binary to ternary complex, and moved the duplex release information to panel A. We thank the reviewer and think that the data is now much clearer.

Figure 3. AGO2 moderates affinity by strengthening weak binders and weakening strong binders. (A) Correlation of relative mRNA:miR-34a with mRNA:miR-34aAGO2 binding affinities. No seed type correlation is observed, seeds coloured, where 8mer is pink, 7mer-m8 is turquoise, and 7-mer-A1 is mauve. The slope of the linear fit is 0.48, and intercept on the (log y)-axis is 7.11. The occurrence of miRNA duplex release from AGO2 is marked with diamonds. (B) miR-34a-mediated repression of dual luciferase reporters fused to the 12 mRNA targeting sites. Luciferase activity from HEK293T cells co-transfected with each reporter construct, miR-34a was measured 24 hours following transfection and normalised to the miR-34a-negative transfection control. Each datapoint represents the R/F ratio for an independent experiment (n=3) with standard deviations indicated. SCRseed is a scrambled seed control, SCRall is a fully scrambled control, and PERFECT is the perfect complement of miR-34a. Dotted horizontal lines represent the repression values for the 22-nucleotide seed-only controls6 for the respective seed types, in the absence of any other WC base pairing. (C) Comparison of relative target repression with relative affinity assessed by EMSA. Blue represents mRNA:miR-34a affinity (binary complex), while green represents mRNA:miR-34a-AGO2 affinity (ternary complex). Arrows indicate the direction of change in affinity upon binding within AGO2 compared to the binary complex. It is seen that AGO2 moderates affinity bi-directionally by strengthening weak binders and weakening strong binders.

Page 20: Perfect should be italicized.

Thank you for bringing this to our attention, this how now been adjusted.

Have the authors considered using NMR to assess the base pair pattern formed between the miRNA:mRNA complexes (with / without AGO)? As a validation for results obtained by RABS? This could be helpful for the Asymmetric target binding section, the Ago increases flexibility section, and the three distinct structural groups section in the results. It is widely accepted that while chemical probing is insightful, results should be validated using alternative approaches. Distinguishing structural changes and protected reactivity in the presence of protein is challenging.

NMR provides high-resolution information on RNA base-pairing patterns, allowing us to compare our RABS results for SIRT1with those obtained via NMR (Banijamali et al., 2022) for the binary complex. For SIRT1, the RNA:RNA structures identified were consistent between both methods. However, using NMR to measure RNA:RNA binding within AGO2 is challenging due to the protein's large size. Currently, there are no published complete NMR structures of RNA within AGO2. The largest solution-state NMR structures published that include AGO consist solely of the PAZ domain. Our group has been working on method development using DNP-enhanced solid-state NMR to obtain structural information within the complete AGO2 protein, but the current resolution does not allow us to fully reconstruct a complete NMR structure. We hope that in the coming years, this will be a method to evaluate RNA within AGO. This limitation highlights the advantage of RABS in providing RNA base-pairing information within the ternary complex in solution.

Reviewer #3 (Significance (Required)):

The work is helpful for understanding how microRNAs recognize and bind their mRNA targets, and the impact Ago has on this interaction. I think for therapeutic studies, this will be helpful for structure-based design. Especially given the three types of structures identified to be a part of the interaction.

We thank the reviewer for their detailed remarks, especially concerning the importance of technical details the binding assays. We further thank the reviewer for recognising the potential impact of our work for rational design.

4. Description of analyses that authors prefer not to carry out

• *

In response to Reviewer 2 - major comment 1, we prefer to not run an additional ion exchange purification on the AGO2 protein due to the reasoning discussed above, which is repeated here:

We have addressed this point in three ways:

Thank you for mentioning this crucial point which has been a focus of our controls. We have addressed this point in four ways:

Salt wash during reverse IMAC purification. Separation of unbound RNA and proteins via SEC. Blocking non-specific interactions using polyuridine. Observing both the presence and absence of duplex release among different targets using the same AGO2 preparation and conditions.

Firstly, although we did not use a specific ion exchange column for purification, we believe the ionic strength used in our IMAC wash step was sufficient to remove non-specific interactions. We used A linear gradient with using buffer A (50 mM Tris-HCl, 300 mM NaCl, 10 mM Imidazole, 1 mM TCEP, 5% glycerol v/v) and buffer B (50 mM Tris-HCl, 500 mM NaCl, 300 mM Imidazole, 1 mM TCEP, 5% glycerol) at pH 8. The protocol followed recommendation by BioRad for their Profinity IMAC resins where it is stated that 300 mM NaCl should be included in buffers to deter nonspecific protein binding due to ionic interactions. The protein itself has a higher affinity for the resin than nucleic acids.

A commonly used protocol for RISC purification follows the method by Flores-Jasso et al. (RNA 2013). Here, the authors use ion exchange chromatography to remove competitor oligonucleotides. After loading, they washed the column with lysis buffer (30 mM HEPES-KOH at pH 7.4, 100 mM potassium acetate, 2 mM magnesium acetate and 2 mM DTT). AGO was eluted with lysis buffer containing 500 mM potassium acetate. Competing oligonucleotides were eluted in the wash.

As ionic strength is independent of ion identity or chemical nature of the ion involved (Jerermy M. Berg, John L. Tymoczko, Gregory J. Garret Jr., Biochemistry 2015), we reasoned that our Tris-HCl/NaCl/ imidazole buffer wash should have at comparable ionic strength to the Flores-Jasso protocol.

Our total ionic contributions were: 500 mM Na+, 550 mM Cl-, 50 mM Tris and 300 mM imidazole. We recognise that Tris and imidazole are both partially ionized according the pH of the buffer (pH 8) and their respective pKa values, but even if only considering the sodium and chloride it should be comparable to the Flores-Jasso protocol.

Secondly, after reverse HisTrap purification, AGO2 was run through size exclusion chromatography to remove any remaining impurities (shown Figure S2B).

Thirdly, knowing that AGO2 has many positively charged surface patches and can bind nucleic acid nonspecifically (Nakanishi, 2022; O'Geen et al., 2018), we tested various blocking backgrounds to eliminate nonspecific binding effects in our EMSA ternary binding assays. We were able to address this issue by adding either non-homogenous RNA extract or homogenous polyuridine (pU) in our EMSA buffer during equilibration background experiments. This allowed us to eliminate non-specific binding of our target mRNAs, as shown previously in Supplementary Figure S6. We appreciate that the reviewer finds this technical detail important and have moved the panel C of figure S6 into the main results in Figure 2C, to highlight the novel conditions used and important controls needed to be performed. If miR-34a were non-specifically bound to the surface of AGO2 after washing, this blocking step would render any impact of surface-bound miR-34a negligible due to the excess of competing polyuridine (pU).

Our EMSA results show that, using polyU, we can reduce non-specific interaction between AGO2 and RNAs that are present. And still, duplex release occurs despite the blocking step. It is therefore less likely that duplex release is caused by surface-bound miR-34a.

Finally, the observation of distinct duplex release for certain targets, but not for others (e.g. MTA2, which bound tightly to miR-34a-AGO2 but did not exhibit duplex release; see Figure 2), argues against the possibility that the phenomenon was solely due to non-specifically bound RNA releasing from AGO2.

In response to the reviewers statement "Since properly loaded miR-34a is never released from AGO2, it is impossible for the miR-34a loaded into AGO2 to form the binary complex (mRNA:miR-34a)" we would like to refer to the three papers, De et al. (2013) Jo MH et al. (2015), and Park JH et al. (2017), which have previously reported duplex release and collectively provide considerable evidence that miRNA can be unloaded from AGO in order to promote turnover and recycling of AGO. It is known that AGO recycling must occur, therefore there must be some mechanisms to enable release of miRNA from AGO2 to enable this. It is possible that AGO recycling proceeds via miRNA degradation (TDMD) in the cell, but in the absence of enzymes responsible for oligouridylation and degradation, the miRNA duplex may be released. As TDMD-competent mRNA targets have been observed to release the miRNA 3' tail from AGO2 (Sheu-Gruttadauria et al., 2019; Willkomm et al., 2022), there is a possible mechanistic similarity between the two processes, however, we do not have sufficient data to make any statement on this.

J'ai tout bien fais, mais dans le corrigé, la balise orpheline pour la langue est juste apres Doctype. Je l'ai mise dans les balises de paires head. Est- ce que ca pose un probleme? Et est-ce que j'aurais mal pris mes notes du cours ?

Author response:

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

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

(1) Lines 40-42: The sentence "The coupling of structural connectome (SC) and functional connectome (FC) varies greatly across different cortical regions reflecting anatomical and functional hierarchies as well as individual differences in cognitive function, and is regulated by genes" is a misstatement. Regional variations of structure-function coupling do not really reflect differences in cognitive function among individuals, but inter-subject variations do.

Thank you for your comment. We have made revisions to the sentence to correct its misstatement. Please see lines 40-43: “The coupling of structural connectome (SC) and functional connectome (FC) varies greatly across different cortical regions reflecting anatomical and functional hierarchies[1, 6-9] and is regulated by genes[6, 8], as well as its individual differences relates to cognitive function[8, 9].”

(2) In Figure 1, the graph showing the relation between intensity and cortical depth needs explanation.

Thank you for your comment. We have added necessary explanation, please see lines 133-134: “The MPC was used to map similarity networks of intracortical microstructure (voxel intensity sampled in different cortical depth) for each cortical node.”

(3) Line 167: Change "increased" to "increase".

We have corrected it, please see lines 173-174: “…networks significantly increased with age and exhibited greater increase.”

(4) Line 195: Remove "were".

We have corrected it, please see line 204: “…default mode networks significantly contributed to the prediction…”

(5) Lines 233-240, Reproducibility analyses: Comparisons of parcellation templates were not made with respect to gene weights. Is there any particular reason?

Thank you for your comment. We have quantified the gene weights based on HCPMMP using the same procedures. We identified a correlation (r \= 0.25, p<0.001) between the gene weights in HCPMMP and BNA. Given that this is a relatively weak correlation, we need to clarify the following points.

Based on HCPMMP, we produced an averaged gene expression profile for 10,027 genes covering 176 left cortical regions[1]. The excluding 4 cortical regions that had an insufficient number of assigned samples may lead to different templates having a relatively weak correlation of gene associations. Moreover, the effect of different template resolutions on the results of human connectome-transcriptome association is still unclear.

In brain connectome analysis, the choice of parcellation templates can indeed influence the subsequent findings to some extent. A methodological study[2] provided referenced correlations about 0.4~0.6 for white matter connectivity and 0.2~0.4 for white matter nodal property between two templates (refer to Figure 4 and 5 in [2]). Therefore, the age-related coupling changes as a downstream analysis was calculated using multimodal connectome and correlated with gene expression profiles, which may be influenced by the choice of templates. 

We have further supplemented gene weights results obtained from HCPMMP to explicitly clarify the dependency of parcellation templates.

Please see lines 251-252: “The gene weights of HCPMMP was consistent with that of BNA (r = 0.25, p < 0.001).”

Author response image 1.

The consistency of gene weights between HCPMMP and BNA.

Please see lines 601-604: “Finally, we produced an averaged gene expression profile for 10,027 genes covering 176 left cortical regions based on HCPMMP and obtained the gene weights by PLS analysis. We performed Pearson's correlation analyses to assess the consistency of gene weights between HCPMMP and BNA.”

Reviewer #2 (Recommendations For The Authors):

Your paper is interesting to read and I found your efforts to evaluate the robustness of the results of different parcellation strategies and tractography methods very valuable. The work is globally easy to navigate and well written with informative good-quality figures, although I think some additional clarifications will be useful to improve readability. My suggestions and questions are detailed below (I aimed to group them by topic which did not always succeed so apologies if the comments are difficult to navigate, but I hope they will be useful for reflection and to incorporate in your work).

* L34: 'developmental disorder'

** As far as I understand, the subjects in HCP-D are mostly healthy (L87). Thus, while your study provides interesting insights into typical brain development, I wonder if references to 'disorder' might be premature. In the future, it would be interesting to extend your approach to the atypical populations. In any case, it would be extremely helpful and appreciated if you included a figure visualising the distribution of behavioural scores within your population and in relationship to age at scan for your subjects (and to include a more detailed description of the assessment in the methods section) given that large part of your paper focuses on their prediction using coupling inputs (especially given a large drop of predictive performance after age correction). Such figures would allow the reader to better understand the cognitive variability within your data, but also potential age relationships, and generally give a better overview of your cohort.

We agree with your comment that references to 'disorder' is premature. We have made revisions in abstract and conclusion. 

Please see lines 33-34: “This study offers insight into the maturational principles of SC-FC coupling in typical development.”

Please see lines 395-396: “Further investigations are needed to fully explore the clinical implications of SC-FC coupling for a range of developmental disorders.”

In addition, we have included a more detailed description of the cognitive scores in the methods section and provided a figure to visualize the distributions of cognitive scores and in relationship to age for subjects. Please see lines 407-413: “Cognitive scores. We included 11 cognitive scores which were assessed with the National Institutes of Health (NIH) Toolbox Cognition Battery (https://www.healthmeasures.net/exploremeasurement-systems/nih-toolbox), including episodic memory, executive function/cognitive flexibility, executive function/inhibition, language/reading decoding, processing speed, language/vocabulary comprehension, working memory, fluid intelligence composite score, crystal intelligence composite score, early child intelligence composite score and total intelligence composite score. Distributions of these cognitive scores and their relationship with age are illustrated in Figure S12.”

Author response image 2.

Cognitive scores and age distributions of scans.

* SC-FC coupling

** L162: 'Regarding functional subnetworks, SC-FC coupling increased disproportionately with age (Figure 3C)'.

*** As far as I understand, in Figure 3C, the points are the correlation with age for a given ROI within the subnetwork. Is this correct? If yes, I am not sure how this shows a disproportionate increase in coupling. It seems that there is great variability of SC-FC correlation with age across regions within subnetworks, more so than the differences between networks. This would suggest that the coupling with age is regionally dependent rather than network-dependent? Maybe you could clarify?

The points are the correlation with age for a given ROI within the subnetwork in Figure 3C. We have revised the description, please see lines 168-174: “Age correlation coefficients distributed within functional subnetworks were shown in Figure 3C. Regarding mean SC-FC coupling within functional subnetworks, the somatomotor (𝛽𝑎𝑔𝑒\=2.39E-03, F=4.73, p\=3.10E-06, r\=0.25, p\=1.67E07, Figure 3E), dorsal attention (𝛽𝑎𝑔𝑒\=1.40E-03, F=4.63, p\=4.86E-06, r\=0.24, p\=2.91E-07, Figure 3F), frontoparietal (𝛽𝑎𝑔𝑒 =2.11E-03, F=6.46, p\=2.80E-10, r\=0.33, p\=1.64E-12, Figure 3I) and default mode (𝛽𝑎𝑔𝑒 =9.71E-04, F=2.90, p\=3.94E-03, r\=0.15, p\=1.19E-03, Figure 3J) networks significantly increased with age and exhibited greater increase.” In addition, we agree with your comment that the coupling with age is more likely region-dependent than network-dependent. We have added the description, please see lines 329-332: “We also found the SC-FC coupling with age across regions within subnetworks has more variability than the differences between networks, suggesting that the coupling with age is more likely region-dependent than network-dependent.” This is why our subsequent analysis focused on regional coupling.  

*** Additionally, we see from Figure 3C that regions within networks have very different changes with age. Given this variability (especially in the subnetworks where you show both positive and negative correlations with age for specific ROIs (i.e. all of them)), does it make sense then to show mean coupling over regions within the subnetworks which erases the differences in coupling with age relationships across regions (Figures 3D-J)?

Considering the interest and interpretation for SC-FC coupling, showing the mean coupling at subnetwork scales with age correlation is needed, although this eliminates variability at regional scale. These results at different scales confirmed that coupling changes with age at this age group are mainly increased.

*** Also, I think it would be interesting to show correlation coefficients across all regions, not only the significant ones (3B). Is there a spatially related tendency of increases/decreases (rather than a 'network' relationship)? Would it be interesting to show a similar figure to Figure S7 instead of only the significant regions?

As your comment, we have supplemented the graph which shows correlation coefficients across all regions into Figure 3B. Similarly, we supplemented to the other figures (Figure S3-S6).

Author response image 3.

Aged-related changes in SC-FC coupling. (A) Increases in whole-brain coupling with age. (B) Correlation of age with SC-FC coupling across all regions and significant regions (p<0.05, FDR corrected). (C) Comparisons of age-related changes in SC-FC coupling among functional networks. The boxes show the median and interquartile range (IQR; 25–75%), and the whiskers depict 1.5× IQR from the first or third quartile. (D-J) Correlation of age with SC-FC coupling across the VIS, SM, DA, VA, LIM, FP and DM. VIS, visual network; SM, somatomotor network; DA, dorsal attention network; VA, ventral attention network; LIM, limbic network; FP, frontoparietal network; DM, default mode network.

*** For the quantification of MPC.

**** L421: you reconstructed 14 cortical surfaces from the wm to pial surface. If we take the max thickness of the cortex to be 4.5mm (Fischl & Dale, 2000), the sampling is above the resolution of your anatomical images (0.8mm). Could you expand on what the interest is in sampling such a higher number of surfaces given that the resolution is not enough to provide additional information?

The surface reconstruction was based on state-of-the-art equivolumetric surface construction techniques[3] which provides a simplified recapitulation of cellular changes across the putative laminar structure of the cortex. By referencing a 100-μm resolution Merkerstained 3D histological reconstruction of an entire post mortem human brain (BigBrain: https://bigbrain.loris.ca/main.php), a methodological study[4] systematically evaluated MPC stability with four to 30 intracortical surfaces when the resolution of anatomical image was 0.7 mm, and selected 14 surfaces as the most stable solution. Importantly, it has been proved the in vivo approach can serve as a lower resolution yet biologically meaningful extension of the histological work[4]. 

**** L424: did you aggregate intensities over regions using mean/median or other statistics?

It might be useful to specify.

Thank you for your careful comment. We have revised the description in lines 446-447: “We averaged the intensity profiles of vertices over 210 cortical regions according to the BNA”.

**** L426: personal curiosity, why did you decide to remove the negative correlation of the intensity profiles from the MPC? Although this is a common practice in functional analyses (where the interpretation of negatives is debated), within the context of cortical correlations, the negative values might be interesting and informative on the level of microstructural relationships across regions (if you want to remove negative signs it might be worth taking their absolute values instead).

We agree with your comment that the interpretation of negative correlation is debated in MPC. Considering that MPC is a nascent approach to network modeling, we adopted a more conservative strategy that removing negative correlation by referring to the study [4] that proposed the approach. As your comment, the negative correlation might be informative. We will also continue to explore the intrinsic information on the negative correlation reflecting microstructural relationships.

**** L465: could you please expand on the notion of self-connections, it is not completely evident what this refers to.

We have revised the description in lines 493-494: “𝑁𝑐 is the number of connection (𝑁𝑐 = 245 for BNA)”.

**** Paragraph starting on L467: did you evaluate the multicollinearities between communication models? It is possibly rather high (especially for the same models with similar parameters (listed on L440-444)). Such dependence between variables might affect the estimates of feature importance (given the predictive models only care to minimize error, highly correlated features can be selected as a strong predictor while the impact of other features with similarly strong relationships with the target is minimized thus impacting the identification of reliable 'predictors').

We agree with your comment. The covariance structure (multicollinearities) among the communication models have a high probability to lead to unreliable predictor weights. In our study, we applied Haufe's inversion transform[5] which resolves this issue by computing the covariance between the predicted FC and each communication models in the training set. More details for Haufe's inversion transform please see [5]. We further clarified in the manuscript, please see in lines 497-499: “And covariance structure among the predictors may lead to unreliable predictor weights. Thus, we applied Haufe's inversion transform[38] to address these issues and identify reliable communication mechanisms.”

**** L474: I am not completely familiar with spin tests but to my understanding, this is a spatial permutation test. I am not sure how this applies to the evaluation of the robustness of feature weight estimates per region (if this was performed per region), it would be useful to provide a bit more detail to make it clearer.

As your comment, we have supplemented the detail, please see lines 503-507: “Next, we generated 1,000 FC permutations through a spin test[86] for each nodal prediction in each subject and obtained random distributions of model weights. These weights were averaged over the group and were investigated the enrichment of the highest weights per region to assess whether the number of highest weights across communication models was significantly larger than that in a random discovery.”

**** L477: 'significant communication models were used to represent WMC...', but in L103 you mention you select 3 models: communicability, mean first passage, and flow graphs. Do you want to say that only 3 models were 'significant' and these were exactly the same across all regions (and data splits/ parcellation strategies/ tractography methods)? In the methods, you describe a lot of analysis and testing but it is not completely clear how you come to the selection of the final 3, it would be beneficial to clarify. Also, the final 3 were selected on the whole dataset first and then the pipeline of SC-FC coupling/age assessment/behaviour predictions was run for every (WD, S1, S2) for both parcellations schemes and tractography methods or did you end up with different sets each time? It would be good to make the pipeline and design choices, including the validation bit clearer (a figure detailing all the steps which extend Figure 1 would be very useful to understand the design/choices and how they relate to different runs of the validation).

Thank you for your comment. In all reproducibility analyses, we used the same 3 models which was selected on the main pipeline (probabilistic tractography and BNA parcellation). According to your comment, we produced a figure that included the pipeline of model selection as the extend of Figure 1. And the description please see lines 106-108: “We used these three models to represent the extracortical connectivity properties in subsequent discovery and reproducibility analyses (Figure S1).” 

Author response image 4.

Pipeline of model selection and reproducibility analyses.

**** Might the imbalance of features between structural connectivity and MPC affect the revealed SC-FC relationships (3 vs 1)? Why did you decide on this ratio rather than for example best WM structural descriptor + MPC?

We understand your concern. The WMC communication models represent diverse geometric, topological, or dynamic factors. In order to describe the properties of WMC as best as possible, we selected three communication models after controlling covariance structure that can significantly predict FC from the 27 models. Compared to MPC, this does present a potential feature imbalance problem. However, this still supports the conclusion that coupling models that incorporate microarchitectural properties yield more accurate predictions of FC from SC[6, 7]. The relevant experiments are shown in Figure S2 below. If only the best WM structural descriptor is used, this may lose some communication properties of WMC.

**** L515: were intracranial volume and in-scanner head motion related to behavioural measures? These variables likely impact the inputs, do you expect them to influence the outcome assessments? Or is there a mistake on L518 and you actually corrected the input features rather than the behaviour measures?

The in-scanner head motion and intracranial volume are related to some age-adjusted behavioural measures, as shown in the following table. The process of regression of covariates from cognitive measures was based on these two cognitive prediction studies [8, 9]. Please see lines 549-554: “Prior to applying the nested fivefold cross-validation framework to each behaviour measure, we regressed out covariates including sex, intracranial volume, and in-scanner head motion from the behaviour measure[59, 69]. Specifically, we estimated the regression coefficients of the covariates using the training set and applied them to the testing set. This regression procedure was repeated for each fold.”

Author response table 1.

** Additionally, in the paper, you propose that the incorporation of cortical microstructural (myelin-related) descriptors with white-matter connectivity to explain FC provides for 'a more comprehensive perspective for characterizing the development of SC-FC coupling' (L60). This combination of cortical and white-matter structure is indeed interesting, however the benefits of incorporating different descriptors could be studied further. For example, comparing results of using only the white matter connectivity (assessed through selected communication models) ~ FC vs (white matter + MPC) ~ FC vs MPC ~ FC. Which descriptors better explain FC? Are the 'coupling trends' similar (or the same)? If yes, what is the additional benefit of using the more complex combination? This would also add strength to your statement at L317: 'These discrepancies likely arise from differences in coupling methods, highlighting the complementarity of our methods with existing findings'. Yes, discrepancies might be explained by the use of different SC inputs. However, it is difficult to see how discrepancies highlight complementarity - does MCP (and combination with wm) provide additional information to using wm structural alone?~

According to your comment, we have added the analyses based on different models using only the myelin-related predictor or WM connectivity to predict FC, and further compared the results among different models. please see lines 519-521: “In addition, we have constructed the models using only MPC or SCs to predict FC, respectively. Spearman’s correlation was used to assess the consistency between spatial patterns based on different models.” 

Please see lines 128-130: “In addition, the coupling pattern based on other models (using only MPC or only SCs to predict FC) and the comparison between the models were shown in Figure S2A-C.” Please see lines 178-179: “The age-related patterns of SC-FC coupling based other coupling models were shown in Figure S2D-F.”

Although we found that there were spatial consistencies in the coupling patterns between different models, the incorporation of MPC with SC connectivity can improve the prediction of FC than the models based on only MPC or SC. For age-related changes in coupling, the differences between the models was further amplified. We agree with you that the complementarity cannot be explicitly quantified and we have revised the description, please see line 329: “These discrepancies likely arise from differences in coupling methods.”

Author response image 5.

Comparison results between different models. Spatial pattern of mean SC-FC coupling based on MPC ~ FC (A), SCs ~ FC (B), and MPC + SCs ~ FC (C). Correlation of age with SC-FC coupling across cortex based on MPC ~ FC (D), SCs ~ FC (E), and MPC + SCs ~ FC (F).

** For the interpretation of results: L31 'SC-FC coupling is positively associated with genes in oligodendrocyte-related pathways and negatively associated with astrocyte-related gene'; L124: positive myelin content with SC-FC coupling...and similarly on L81, L219, L299, L342, and L490:

***You use a T1/T2 ratio which is (in large part) a measure of myelin to estimate the coupling between SC and FC. Evaluation with SC-FC coupling with myeline described in Figure 2E is possibly biased by the choice of this feature. Similarly, it is possible that reported positive associations with oligodendrocyte-related pathways and SC-FC coupling in your work could in part result from a bias introduced by the 'myelin descriptor' (conversely, picking up the oligodendrocyte-related genes is a nice corroboration for the T1/T2 ration being a myelin descriptor, so that's nice). However, it is possible that if you used a different descriptor of the cortical microstructure, you might find different expression patterns associated with the SCFC coupling (for example using neurite density index might pick up neuronal-related genes?). As mentioned in my previous suggestions, I think it would be of interest to first use only the white matter structural connectivity feature to assess coupling to FC and assess the gene expression in the cortical regions to see if the same genes are related, and subsequently incorporate MPC to dissociate potential bias of using a myelin measure from genetic findings.

Thank you for your insightful comments. In this paper, however, the core method of measuring coupling is to predict functional connections using multimodal structural connections, which may yield more information than a single modal. We agree with your comment that separating SCs and MPC to look at the genes involved in both separately could lead to interesting discoveries. We will continue to explore this in the future.

** Generally, I find it difficult to understand the interpretation of SC-FC coupling measures and would be interested to hear your thinking about this. As you mention on L290-294, how well SC predicts FC depends on which input features are used for the coupling assessment (more complex communication models, incorporating additional microstructural information etc 'yield more accurate predictions of FC' L291) - thus, calculated coupling can be interpreted as a measure of how well a particular set of input features explain FC (different sets will explain FC more or less well) ~ coupling is related to a measure of 'missing' information on the SC-FC relationship which is not contained within the particular set of structural descriptors - with this approach, the goal might be to determine the set that best, i.e. completely, explains FC to understand the link between structure and function. When you use the coupling measures for comparisons with age, cognition prediction etc, the 'status' of the SC-FC changes, it is no longer the amount of FC explained by the given SC descriptor set, but it's considered a descriptor in itself (rather than an effect of feature selection / SC-FC information overlap) - how do you interpret/argue for this shift of use?

Thank you for your comment. In this paper, we obtain reasonable SC-FC coupling by determining the optimal set of structural features to explain the function. The coupling essentially measures the direct correspondence between structure and function. To study the relationship between coupling and age and cognition is actually to study the age correlation and cognitive correlation of this direct correspondence between structure and function. 

** In a similar vein to the above comment, I am interested to hear what you think: on L305 you mention that 'perfect SC-FC coupling may be unlikely'. Would this reasoning suggest that functional activity takes place through other means than (and is therefore somehow independent of) biological (structural) substrates? For now, I think one can only say that we have imperfect descriptors of the structure so there is always information missing to explain function, this however does not mean the SC and FC are not perfectly coupled (only that we look at insufficient structural descriptors - limitations of what imaging can assess, what we measure etc). This is in line with L305 where you mention that 'Moreover, our results suggested that regional preferential contributions across different SCs lead to variations in the underlying communication process'. This suggests that locally different areas might use different communication models which are not reflected in the measures of SC-FC coupling that was employed, not that the 'coupling' is lower or higher (or coupling is not perfect). This is also a change in approach to L293: 'This configuration effectively releases the association cortex from strong structural constraints' - the 'release' might only be in light of the particular structural descriptors you use - is it conceivable that a different communication model would be more appropriate (and show high coupling) in these areas.

Thank you for your insightful comments. We have changed the description, please see lines 315317: “SC-FC coupling is dynamic and changes throughout the lifespan[7], particularly during adolescence[6,9], suggesting that perfect SC-FC coupling may require sufficient structural descriptors.” 

*Cognitive predictions:

** From a practical stand-point, do you think SC-FC coupling is a better (more accurate) indicator of cognitive outcomes (for example for future prediction studies) than each modality alone (which is practically easier to obtain and process)? It would be useful to check the behavioural outcome predictions for each modality separately (as suggested above for coupling estimates). In case SC-FC coupling does not outperform each modality separately, what is the benefit of using their coupling? Similarly, it would be useful to compare to using only cortical myelin for the prediction (which you showed to increase in importance for the coupling). In the case of myelin->coupling-> intelligence, if you are able to predict outcomes with the same performance from myelin without the need for coupling measures, what is the benefit of coupling?

From a predictive performance point of view, we do not believe that SC-FC coupling is a better indicator than a single mode (voxel, network or other indicator). Our starting point is to assess whether SC-FC coupling is related to the individual differences of cognitive performances rather than to prove its predictive power over other measures. As you suggest, it's a very interesting perspective on the predictive power of cognition by separating the various modalities and comparing them. We will continue to explore this issue in the future study.

** The statement on L187 'suggesting that increased SC-FC coupling during development is associated with higher intelligence' might not be completely appropriate before age corrections (especially given the large drop in performance that suggests confounding effects of age).

According to your comment, we have removed the statement.

** L188: it might be useful to report the range of R across the outer cross-validation folds as from Figure 4A it is not completely clear that the predictive performance is above the random (0) threshold. (For the sake of clarity, on L180 it might be useful for the reader if you directly report that other outcomes were not above the random threshold).

According to your comment, we have added the range of R and revised the description, please see lines 195-198: “Furthermore, even after controlling for age, SC-FC coupling remained a significant predictor of general intelligence better than at chance (Pearson’s r\=0.11±0.04, p\=0.01, FDR corrected, Figure 4A). For fluid intelligence and crystal intelligence, the predictive performances of SC-FC coupling were not better than at chance (Figure 4A).”

In a similar vein, in the text, you report Pearson's R for the predictive results but Figure 4A shows predictive accuracy - accuracy is a different (categorical) metric. It would be good to homogenise to clarify predictive results.

We have made the corresponding changes in Figure 4.

Author response image 6.

Encoding individual differences in intelligence using regional SC-FC coupling. (A) Predictive accuracy of fluid, crystallized, and general intelligence composite scores. (B) Regional distribution of predictive weight. (C) Predictive contribution of functional networks. The boxes show the median and interquartile range (IQR; 25–75%), and the whiskers depict the 1.5× IQR from the first or third quartile.

*Methods and QC:

-Parcellations

** It would be useful to mention briefly how the BNA was applied to the data and if any quality checks were performed for the resulting parcellations, especially for the youngest subjects which might be most dissimilar to the population used to derive the atlas (healthy adults HCP subjects) ~ question of parcellation quality.

We have added the description, please see lines 434-436: “The BNA[31] was projected on native space according to the official scripts (http://www.brainnetome.org/resource/) and the native BNA was checked by visual inspection.” 

** Additionally, the appropriateness of structurally defined regions for the functional analysis is also a topic of important debate. It might be useful to mention the above as limitations (which apply to most studies with similar focus).

We have added your comment to the methodological issues, please see lines 378-379: “Third, the appropriateness of structurally defined regions for the functional analysis is also a topic of important debate.”

- Tractography

** L432: it might be useful to name the method you used (probtrackx).

We have added this name to the description, please see lines 455-456: “probabilistic tractography (probtrackx)[78, 79] was implemented in the FDT toolbox …”

** L434: 'dividing the total fibres number in source region' - dividing by what?

We have revised the description, please see line 458: “dividing by the total fibres number in source region.”

** L436: 'connections in subcortical areas were removed' - why did you trace connections to subcortical areas in the first place if you then removed them (to match with cortical MPC areas I suspect)? Or do you mean there were spurious streamlines through subcortical regions that you filtered?

On the one hand we need to match the MPC, and on the other hand, as we stated in methodological issues, the challenge of accurately resolving the connections of small structures within subcortical regions using whole-brain diffusion imaging and tractography techniques[10, 11]. 

** Following on the above, did you use any exclusion masks during the tracing? In general, more information about quality checks for the tractography would be useful. For example, L437: did you do any quality evaluations based on the removed spurious streamlines? For example, were there any trends between spurious streamlines and the age of the subject? Distance between regions/size of the regions?

We did not use any exclusion masks. We performed visual inspection for the tractography quality and did not assess the relationship between spurious streamlines and age or distance between regions/size of the regions.

** L439: 'weighted probabilistic network' - this was weighted by the filtered connectivity densities or something else?

The probabilistic network is weighted by the filtered connectivity densities.

** I appreciate the short description of the communication models in Text S1, it is very useful.

Thank you for your comment.

** In addition to limitations mentioned in L368 - during reconstruction, have you noticed problems resolving short inter-hemispheric connections?

We have not considered this issue, we have added it to the limitation, please see lines 383-384: “In addition, the reconstruction of short connections between hemispheres is a notable challenge.”

- Functional analysis:

** There is a difference in acquisition times between participants below and above 8 years (21 vs 26 min), does the different length of acquisition affect the quality of the processed data?

We have made relatively strict quality control to ensure the quality of the processed data.  

** L446 'regressed out nuisance variables' - it would be informative to describe in more detail what you used to perform this.

We have provided more detail about the regression of nuisance variables, please see lines 476-477: “The nuisance variables were removed from time series based on general linear model.”

** L450-452: it would be useful to add the number of excluded participants to get an intuition for the overall quality of the functional data. Have you checked if the quality is associated with the age of the participant (which might be related to motion etc). Adding a distribution of remaining frames across participants (vs age) would be useful to see in the supplementary methods to better understand the data you are using.

We have supplemented the exclusion information of the subjects during the data processing, and the distribution and aged correlation of motion and remaining frames. Please see lines 481-485: “Quality control. The exclusion of participants in the whole multimodal data processing pipeline was depicted in Figure S13. In the context of fMRI data, we computed Pearson’s correlation between motion and age, as well as between the number of remaining frames and age, for the included participants aged 5 to 22 years and 8 to 22 years, respectively. These correlations were presented in Figure S14.”

Author response image 7.

Exclusion of participants in the whole multimodal data processing pipeline.  

Author response image 8.

Figure S14. Correlations between motion and age and number of remaining frames and age.

** L454: 'Pearson's correlation's... ' In contrast to MPC you did not remove negative correlations in the functional matrices. Why this choice?

Whether the negative correlation connection of functional signal is removed or not has always been a controversial issue. Referring to previous studies of SC-FC coupling[12-14], we find that the practice of retaining negative correlation connections has been widely used. In order to retain more information, we chose this strategy. Considering that MPC is a nascent approach to network modeling, we adopted a more conservative strategy that removing negative correlation by referring to the study [4] that proposed the approach.

- Gene expression:

** L635, you focus on the left cortex, is this common? Do you expect the gene expression to be fully symmetric (given reported functional hemispheric asymmetries)? It might be good to expand on the reasoning.

An important consideration regarding sample assignment arises from the fact that only two out of six brains were sampled from both hemispheres and four brains have samples collected only in the left. This sparse sampling should be carefully considered when combining data across donors[1]. We have supplemented the description, please see lines 569-571: “Restricting analyses to the left hemisphere will minimize variability across regions (and hemispheres) in terms of the number of samples available[40].”

** Paragraph of L537: you use evolution of coupling with age (correlation) and compare to gene expression with adults (cohort of Allen Human Brain Atlas - no temporal evolution to the gene expressions) and on L369 you mention that 'relative spatial patterns of gene expressions remain stable after birth'. Of course this is not a place to question previous studies, but would you really expect the gene expression associated with the temporary processes to remain stable throughout the development? For example, myelination would follow different spatiotemporal gradient across brain regions, is it reasonable to expect that the expression patterns remain the same? How do you then interpret a changing measure of coupling (correlation with age) with a gene expression assessed statically?

We agree with your comment that the spatial expression patterns is expected to vary at different periods. We have revised the previous description, please see lines 383-386: “Fifth, it is important to acknowledge that changes in gene expression levels during development may introduce bias in the results.”

- Reproducibility analyses:

** Paragraph L576: are we to understand that you performed the entire pipeline 3 times (WD, S1, S2) for both parcellations schemes and tractography methods (~12 times) including the selection of communication models and you always got the same best three communication models and gene expression etc? Or did you make some design choices (i.e. selection of communication models) only on a specific set-up and transfer to other settings?

The choice of communication model is established at the beginning, which we have clarified in the article, please see lines 106-108: “We used these three models to represent the extracortical connectivity properties in subsequent discovery and reproducibility analyses (Figure S1).” For reproducibility analyses (parcellation, tractography, and split-half validation), we fixed other settings and only assessed the impact of a single factor.

** Paragraph of L241: I really appreciate you evaluated the robustness of your results to different tractography strategies. It is reassuring to see the similarity in results for the two approaches. Did you notice any age-related effects on tractography quality for the two methods given the wide age range (did you check?)

In our study, the tractography quality was checked by visual inspection. Using quantifiable tools to tractography quality in future studies could answer this question objectively.

** Additionally, I wonder how much of that overlap is driven by the changes in MPC which is the same between the two methods... especially given its high weight in the SC-FC coupling you reported earlier in the paper. It might be informative to directly compare the connectivity matrices derived from the two tracto methods directly. Generally, as mentioned in the previous comments, I think it would be interesting to assess coupling using different input settings (with WM structural and MPC separate and then combined).

As your previous comment, we have examined the coupling patterns, coupling differences, coupling age correlation, and spatial correlations between the patterns based on different models, as shown in Figure S2. Please see our response to the previous comment for details.

** L251 - I also wonder if the random splitting is best adapted to validation in your case given you study relationships with age. Would it make more sense to make stratified splits to ensure a 'similar age coverage' across splits?

In our study, we adopt the random splitting process which repeated 1,000 times to minimize bias due to data partitioning. The stratification you mentioned is a reasonable method, and keeping the age distribution even will lead to higher verification similarity than our validation method. However, from the validation results of our method, the similarity is sufficient to explain the generalization of our findings.

Minor comments

L42: 'is regulated by genes'

** Coupling (if having a functional role and being regulated at all) is possibly resulting from a complex interplay of different factors in addition to genes, for example, learning/environment, it might be more cautious to use 'regulated in part by genes' or similar.

We have corrected it, please see line 42.

L43 (and also L377): 'development of SC-FC coupling'

** I know this is very nitpicky and depends on your opinion about the nature of SC-FC coupling, but 'development of SC-FC coupling' gives an impression of something maturing that has a role 'in itself' (for example development of eye from neuroepithelium to mature organ etc.). For now, I am not sure it is fully certain that SC-FC coupling is more than a byproduct of the comparison between SC and FC, using 'changes in SC-FC coupling with development' might be more apt.

We have corrected it, please see lines 43-44.

L261 'SC-FC coupling was stronger ... [] ... and followed fundamental properties of cortical organization.' vs L168 'No significant correlations were found between developmental changes in SC-FC coupling and the fundamental properties of cortical organization'.

**Which one is it? I think in the first you refer to mean coupling over all infants and in the second about correlation with age. How do you interpret the difference?

Between the ages of 5 and 22 years, we found that the mean SC-FC coupling pattern has become similar to that of adults, consistent with the fundamental properties of cortical organization. However, the developmental changes in SC-FC coupling are heterogeneous and sequential and do not follow the mean coupling pattern to change in the same magnitude.

L277: 'temporal and spatial complexity'

** Additionally, communication models have different assumptions about the flow within the structural network and will have different biological plausibility (they will be more or less

'realistic').

Here temporal and spatial complexity is from a computational point of view.

L283: 'We excluded a centralized model (shortest paths), which was not biologically plausible' ** But in Text S1 and Table S1 you specify the shortest paths models. Does this mean you computed them but did not incorporate them in the final coupling computations even if they were predictive?

** Generally, I find the selection of the final 3 communication models confusing. It would be very useful if you could clarify this further, for example in the methods section.

We used all twenty-seven communication models (including shortest paths) to predict FC at the node level for each participant. Then we identified three communication models that can significantly predict FC. For the shortest path, he was excluded because he did not meet the significance criteria. We have further added methodological details to this section, please see lines 503-507.

L332 'As we observed increasing coupling in these [frontoparietal network and default mode network] networks, this may have contributed to the improvements in general intelligence, highlighting the flexible and integrated role of these networks' vs L293 'SC-FC coupling in association areas, which have lower structural connectivity, was lower than that in sensory areas. This configuration effectively releases the association cortex from strong structural constraints imposed by early activity cascades, promoting higher cognitive functions that transcend simple sensori-motor exchanges'

** I am not sure I follow the reasoning. Could you expand on why it would be the decoupling promoting the cognitive function in one case (association areas generally), but on the reverse the increased coupling in frontoparietal promoting the cognition in the other (specifically frontoparietal)?

We tried to explain the problem, for general intelligence, increased coupling in frontoparietal could allow more effective information integration enable efficient collaboration between different cognitive processes.

* Formatting errors etc.

L52: maybe rephrase?

We have rephrased, please see lines 51-53: “The T1- to T2-weighted (T1w/T2w) ratio of MRI has been proposed as a means of quantifying microstructure profile covariance (MPC), which reflects a simplified recapitulation in cellular changes across intracortical laminar structure[6, 1215].”

L68: specialization1,[20].

We have corrected it.

L167: 'networks significantly increased with age and exhibited greater increased' - needs rephrasing.

We have corrected it.

L194: 'networks were significantly predicted the general intelligence' - needs rephrasing.

We have corrected it, please see lines 204-205: “we found that the weights of frontoparietal and default mode networks significantly contributed to the prediction of the general intelligence.”

L447: 'and temporal bandpass filtering' - there is a verb missing.

We have corrected it, please see line 471: “executed temporal bandpass filtering.”

L448: 'greater than 0.15' - unit missing.

We have corrected it, please see line 472: “greater than 0.15 mm”.

L452: 'After censoring, regression of nuisance variables, and temporal bandpass filtering,' - no need to repeat the steps as you mentioned them 3 sentences earlier.

We have removed it.

L458-459: sorry I find this description slightly confusing. What do you mean by 'modal'? Connectional -> connectivity profile. The whole thing could be simplified, if I understand correctly your vector of independent variables is a set of wm and microstructural 'connectivity' of the given node... if this is not the case, please make it clearer.

We have corrected it, please see line 488: “where 𝒔𝑖 is the 𝑖th SC profiles, 𝑛 is the number of SC profiles”.

L479: 'values and system-specific of 480 coupling'.

We have corrected it.

L500: 'regular' - regularisation.

We have changed it to “regularization”.

L567: Do you mean that in contrast to probabilistic with FSL you use deterministic methods within Camino? For L570, you introduce communication models through 'such as': did you fit all models like before? If not, it might be clearer to just list the ones you estimated rather than introduce through 'such as'.

We have changed the description to avoid ambiguity, please see lines 608-609: “We then calculated the communication properties of the WMC including communicability, mean first passage times of random walkers, and flow graphs (timescales=1).”

Citation [12], it is unusual to include competing interests in the citation, moreover, Dr. Bullmore mentioned is not in the authors' list - this is most likely an error with citation import, it would be good to double-check.

We have corrected it.

L590: Python scripts used to perform PLS regression can 591 be found at https://scikitlearn.org/. The link leads to general documentation for sklearn.

We have corrected it, please see lines 627-630: “Python scripts used to perform PLS regression can be found at https://scikit-learn.org/stable/modules/generated/sklearn.cross_decomposition.PLSRegression.html#sklearn.cro ss_decomposition.PLSRegression.”

P26 and 27 - there are two related sections: Data and code availability and Code availability - it might be worth merging into one section if possible.

We have corrected it, please see lines 623-633.

References

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(2) Zhong S, He Y, Gong G. Convergence and divergence across construction methods for human brain white matter networks: an assessment based on individual differences. Hum Brain Mapp. 2015;36(5):1995-2013. Epub 2015/02/03. doi: 10.1002/hbm.22751. PubMed PMID: 25641208; PubMed Central PMCID: PMCPMC6869604.

(3) Waehnert MD, Dinse J, Weiss M, Streicher MN, Waehnert P, Geyer S, et al. Anatomically motivated modeling of cortical laminae. Neuroimage. 2014;93 Pt 2:210-20. Epub 2013/04/23. doi: 10.1016/j.neuroimage.2013.03.078. PubMed PMID: 23603284.

(4) Paquola C, Vos De Wael R, Wagstyl K, Bethlehem RAI, Hong SJ, Seidlitz J, et al. Microstructural and functional gradients are increasingly dissociated in transmodal cortices. PLoS Biol. 2019;17(5):e3000284. Epub 2019/05/21. doi: 10.1371/journal.pbio.3000284. PubMed PMID: 31107870.

(5) Haufe S, Meinecke F, Gorgen K, Dahne S, Haynes JD, Blankertz B, et al. On the interpretation of weight vectors of linear models in multivariate neuroimaging. Neuroimage. 2014;87:96-110. Epub 2013/11/19. doi: 10.1016/j.neuroimage.2013.10.067. PubMed PMID: 24239590.

(6) Demirtas M, Burt JB, Helmer M, Ji JL, Adkinson BD, Glasser MF, et al. Hierarchical Heterogeneity across Human Cortex Shapes Large-Scale Neural Dynamics. Neuron. 2019;101(6):1181-94 e13. Epub 2019/02/13. doi: 10.1016/j.neuron.2019.01.017. PubMed PMID: 30744986; PubMed Central PMCID: PMCPMC6447428.

(7) Deco G, Kringelbach ML, Arnatkeviciute A, Oldham S, Sabaroedin K, Rogasch NC, et al. Dynamical consequences of regional heterogeneity in the brain's transcriptional landscape. Sci Adv. 2021;7(29). Epub 2021/07/16. doi: 10.1126/sciadv.abf4752. PubMed PMID: 34261652; PubMed Central PMCID: PMCPMC8279501.

(8) Chen J, Tam A, Kebets V, Orban C, Ooi LQR, Asplund CL, et al. Shared and unique brain network features predict cognitive, personality, and mental health scores in the ABCD study. Nat Commun. 2022;13(1):2217. Epub 2022/04/27. doi: 10.1038/s41467-022-29766-8. PubMed PMID: 35468875; PubMed Central PMCID: PMCPMC9038754.

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Author response:

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

Reviewer #1 (Public Review):

Summary:

In this study, the authors provide a new computational platform called Vermouth to automate topology generation, a crucial step that any biomolecular simulation starts with. Given a wide arrange of chemical structures that need to be simulated, varying qualities of structural models as inputs obtained from various sources, and diverse force fields and molecular dynamics engines employed for simulations, automation of this fundamental step is challenging, especially for complex systems and in case that there is a need to conduct high-throughput simulations in the application of computer-aided drug design (CADD). To overcome this challenge, the authors develop a programming library composed of components that carry out various types of fundamental functionalities that are commonly encountered in topological generation. These components are intended to be general for any type of molecules and not to depend on any specific force field and MD engines. To demonstrate the applicability of this library, the authors employ those components to re-assemble a pipeline called Martinize2 used in topology generation for simulations with a widely used coarse-grained model (CG) MARTINI. This pipeline can fully recapitulate the functionality of its original version Martinize but exhibit greatly enhanced generality, as confirmed by the ability of the pipeline to faithfully generate topologies for two high-complexity benchmarking sets of proteins.

Strengths:

The main strength of this work is the use of concepts and algorithms associated with induced subgraph in graph theory to automate several key but non-trivial steps of topology generation such as the identification of monomer residue units (MRU), the repair of input structures with missing atoms, the mapping of topologies between different resolutions, and the generation of parameters needed for describing interactions between MRUs.

Weaknesses:

Although the Vermouth library appears promising as a general tool for topology generation, there is insufficient information in the current manuscript and a lack of documentation that may allow users to easily apply this library. More detailed explanation of various classes such as Processor, Molecule, Mapping, ForceField etc. that are mentioned is still needed, including inputs, output and associated operations of these classes. Some simple demonstration of application of these classes would be of great help to users. The formats of internal databases used to describe reference structures and force fields may also need to be clarified. This is particularly important when the Vermouth needs to be adapted for other AA/CG force fields and other MD engines.

We thank the reviewer for pointing out the strengths of the presented work and agree that one of the current limitations is the lack of documentation about the library. In the revision, we point more clearly to the documentation page of the Vermouth library, which contains more detailed information on the various processors. The format of the internal databases has also been added to the documentation page. Providing a simple demonstration of applications of these classes is a great suggestion, however, we believe that it is more convenient to provide those in the form of code examples in the documentation or for instance jupyter notebooks rather than in the paper itself.  

The successful automation of the Vermouth relies on the reference structures that need to be pre-determined. In case of the study of 43 small ligands, the reference structures and corresponding mapping to MARTINIcompatible representations for all these ligands have been already defined in the M3 force field and added into the Vermouth library. However, the authors need to comment on the scenario where significantly more ligands need to be considered and other force fields need to be used as CG representations with a lack of reference structures and mapping schemes.

We acknowledge that vermouth/martinize2 is not capable of automatically generating Martini mappings or parameters on the fly for unknown structures that are not part of the database. However, this capability is not the purpose of the program, which is rather to distribute and manage existing parameters. Unlike atomistic force fields, which frequently have automated topology builders, Martini parameters are usually obtained for a set of specific molecules at a time and benchmarked accordingly. As more parameters are obtained by researchers, they can be added to the vermouth library via the GitHub interface in a controlled manner. This process allows the database to grow and in our opinion will quickly grow beyond the currently implemented parameters. Furthermore, the API of Vermouth is set up in a way that it can easily interface with automated topology builders which are currently being developed. Hence this limitation in our view does not diminish the applicability of vermouth to high-throughput applications with many ligands. The framework is existing and works, now only more parameters have to be added.

Reviewer #2 (Public Review):

Summary:

This manuscript by Kroon, Grunewald, Marrink and coworkers present the development of Vermouth library for coarse grain assignment and parameterization and an updated version of python script, the Martinize2 program, to build Martini coarse grained (CG) models, primarily for protein systems.

Strengths:

In contrast to many mature and widely used tools to build all-atom (AA) models, there are few well-accepted programs for CG model constructions and parameterization. The research reported in this manuscript is among the ongoing efforts to build such tools for Martini CG modeling, with a clear goal of high-throughput simulations of complex biomolecular systems and, ultimately, whole-cell simulations. Thus, this manuscript targets a practical problem in computational biophysics. The authors see such an effort to unify operations like CG mapping, parameterization, etc. as a vital step from the software engineering perspective.

Weaknesses:

However, the manuscript in this shape is unclear in the scientific novelty and appears incremental upon existing methods and tools. The only "validation" (more like an example application) is to create Martini models with two protein structure sets (I-TASSER and AlphaFold). The success rate in building the models was only 73%, while the significant failure is due to incomplete AA coordinates. This suggests a dependence on the input AA models, which makes the results less attractive for high-throughput applications (for example, preparation/creation of the AA models can become the bottleneck). There seems to be an improvement in considering the protonation state and chemical modification, but convincing validation is still needed. Besides, limitations in the existing Martini models remain (like the restricted dynamics due to the elastic network, the electrostatic interactions or polarizability).

We thank the reviewer for pointing out the strengths of the presented work, but respectfully disagree with the criticism that the presented work is only incremental upon existing methods and tools. All MD simulations of structured proteins regardless of the force field or resolution rely on a decent initial structure to produce valid results. Therefore, failure upon detection of malformed protein input structures is an essential feature for any high-throughput pipeline working with proteins, especially considering the computational cost of MD simulations. We note that programs such as the first version of Martinize generate reasonable-looking input parameters that lead to unphysical simulations and wasted CPU hours.

The alpha-fold database for which we surveyed 200,000 structures only contained 7 problematic structures, which means that the success rate was 99% for this database. This example simply shows that users potentially have to add the step of fixing atomistic protein input structures, if they seek to run a high-throughput pipeline.

But at least they can be assured that martinize2 will make sure to check that no issues persist.

Furthermore, we note that the manuscript does not aim to validate or improve the existing Martini (protein) models. All example cases presented in the paper are subject to the limitations of the protein models for the reason that martinize2 is only the program to generate those parameters. Future improvements in the protein model, which are currently underway, will immediately be available through the program to the broader community.  

Reviewer #3 (Public Review):

Summary:

The manuscript Kroon et al. described two algorithms, which when combined achieve high throughput automation of "martinizing" protein structures with selected protonation states and post-translational modifications.

Strengths:

A large scale protein simulation was attempted, showing strong evidence that authors' algorithms work smoothly.

The authors described the algorithms in detail and shared the open-source code under Apache 2.0 license on GitHub. This allows both reproducibility of extended usefulness within the field. These algorithms are potentially impactful if the authors can address some of the issues listed below.

We thank the reviewer for pointing out the strengths.  

Weaknesses:

One major caveat of the manuscript is that the authors claim their algorithms aim to "process any type of molecule or polymer, be it linear, cyclic, branched, or dendrimeric, and mixtures thereof" and "enable researchers to prepare simulation input files for arbitrary (bio)polymers". However, the examples provided by the manuscript only support one type of biopolymer, i.e. proteins. Despite the authors' recommendation of using polyply along with martinize2/vermouth, no concrete evidence has been provided to support the authors' claim. Therefore, the manuscript must be modified to either remove these claims or include new evidence.

We acknowledge that the current manuscript is largely protein-centric. To some extent this results from the legacy of martinize version 1, which was also only used for proteins. However, to show that martinize2 also works for cyclic as well as branched molecules we implemented two additional test cases and updated formerly Figure 6 and now Figure 7. Crown ether is used as an example of a cyclic molecule whereas a small branched polyethylene molecule is a test case for branching. Needless to say both molecules are neither proteins nor biomolecules. 

Method descriptions on Martinize2 and graph algorithms in SI should be core content of the manuscript. I argue that Figure S1 and Figure S2 are more important than Figure 3 (protonation state). I recommend the authors can make a workflow chart combining Figure S1 and S2 to explain Martinize2 and graph algorithms in main text.

The reviewer's critique is fair. Given the already rather large manuscript, we tried to strike a balance between describing benchmark test cases, some practical usage information (e.g. the Histidine modification), and the algorithmic library side of the program. In particular, we chose to add the figure on protonation state, because how to deal with protonation states—in particular, Histidines—was amongst the top three raised issues by users on our GitHub page. Due to this large community interest, we consider the figure equally important. However, we moved Figure S1 from the Supporting Information into the manuscript and annotated the already mentioned text with the corresponding panels to more clearly illustrate the underlying procedure. 

In Figure 3 (protonation state), the figure itself and the captions are ambiguous about whether at the end the residue is simply renamed from HIS to HIP, or if hydrogen is removed from HIP to recover HIS.

Using either of the two routes yields the same parameters in the end, which are for the protonated Histidine. In the second route, the extra hydrogen on Histidine is detected as an additional atom and therefore a different logic flow is triggered. Atoms are never removed, but only compounded to a base block plus modification atoms. We adjusted the figure caption to point this out more clearly.  

In "Incorporating a Ligand small-molecule Database", the authors are calling for a community effort to build a small-molecule database. Some guidance on when the current database/algorithm combination does or does not work will help the community in contributing.

Any small molecule not part of the database will not work. However, martinize2 will quickly identify if there are missing components of the system and alert the users. At that point, the users can decide to make their files, guided by the new documentation pages. 

A speed comparison is needed to compare Martinize2 and Martinize.

We respectfully disagree that a speed comparison is needed. We already alerted in the manuscript discussion that martinize2 is slower, since it does more checks, is more general, and does not only implement a single protein model.

Github 100 million developers

Absolutely decimated.

execute javascriptr after dom is parsed

Author response:

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

eLife assessment

This is a valuable study that develops a new model of the way muscle responds to perturbations, synthesizing models of how it responds to small and large perturbations, both of which are used to predict how muscles function for stability but also how they can be injured, and which tend to be predicted poorly by classic Hill-type models. The evidence presented to support the model is solid, since it outperforms Hill-type models in a variety of conditions. Although the combination of phenomenological and mechanistic aspects of the model may sometimes make it challenging to interpret the output, the work will be of interest to those developing realistic models of the stability and control of movement in humans or other animals.

Reviewer #1 (Public Review):

Muscle models are important tools in the fields of biomechanics and physiology. Muscle models serve a wide variety of functions, including validating existing theories, testing new hypotheses, and predicting forces produced by humans and animals in health and disease. This paper attempts to provide an alternative to Hill-type muscle models that includes contributions of titin to force enhancement over multiple time scales. Due to the significant limitations of Hill-type models, alternative models are needed and therefore the work is important and timely.

The effort to include a role for titin in muscle models is a major strength of the methods and results. The results clearly demonstrate the weaknesses of Hill models and the advantages of incorporating titin into theoretical treatments of muscle mechanics. Another strength is to address muscle mechanics over a large range of time scales.

The authors succeed in demonstrating the need to incorporate titin in muscle models, and further show that the model accurately predicts in situ force of cat soleus (Kirsch et al. 1994; Herzog & Leonard, 2002) and rabbit posts myofibrils (Leonard et al. 2010). However, it remains unclear whether the model will be practical for use with data from different muscles or preparations. Several ad hoc modifications were described in the paper, and the degree to which the model requires parameter optimization for different muscles, preparations and experiment types remains unclear.

I think the authors should state how many parameters require fitting to the data vs the total number of model parameters. It would also be interesting for the authors to discuss challenges associated with modeling ex vivo and in vivo data sets, due to differences in means of stimulation vs. model inputs.

(1) I think the authors should state how many parameters require fitting to the data vs the total number of model parameters.

The total number of model parameters are listed in Table 1. Each parameter has, in addition, references listed for the source of data (if one exists) along with how the data were used (’C’ calculate, ’F’ fit, ’E’ estimated, or ’S’ for scaled) for the specific simulations that appear in this paper. While this is a daunting number of parameters, only a few of these parameters must be updated when modeling a new musculotendon.

Similar to a Hill-type muscle model, at least 5 parameters are needed to fit the VEXAT model to a specific musculotendon: maximum isometric force (fiso), optimal contractile element (CE) length, pennation angle, maximum shortening velocity, and tendon slack length. However, similar to a Hill model, it is only possible to use this minimal set of parameters by making use of default values for the remaining set of parameters. The defaults we have used have been extracted from mammalian muscle (see Table 1) and may not be appropriate for modeling muscle tissue that differs widely in terms of the ratio of fast/slow twitch fibers, titin isoform, temperature, and scale.

Even when these defaults are appropriate, variation is the rule for biological data rather than the exception. It will always be the case that the best fit can only be obtained by fitting more of the model’s parameters to additional data. Standard measurements of the active force-length relation, passive forcelength relation, and force-velocity relations are quite helpful to improve the accuracy of the model to a specific muscle. It is challenging to improve the fit of the model’s cross-bridge (XE) and titin models because the data required are so rare. The experiments of Kirsch et al., Prado et al, and Trombitas et´ al. are unique to our knowledge. However, if more data become available, it is relatively straight forward to update the model’s parameters using the methods described in Appendix B or the code that appears online (https://github.com/mjhmilla/Millard2023VexatMuscle).

We have modified the manuscript to make it clear that, in some circumstances, the burden of parameter identification for the VEXAT model can be as low as a Hill model:

- Section 3: last two sentences of the 2nd paragraph, found at: Page 10, column 2, lines 1-12 of MillardFranklinHerzog v3.pdf and 05 MillardFranklinHerzog v2 v3 diff.pdf

- Table 1: last two sentences of the caption, found at: Page 11 of MillardFranklinHerzog v3.pdf and 05 MillardFranklinHerzog v2 v3 diff.pdf

(2) It would also be interesting for the authors to discuss challenges associated with modeling ex vivo and in vivo data sets, due to differences in means of stimulation vs. model inputs.

All of the experiments simulated in this work are in-situ or ex-vivo. So far the main challenges of simulating any experiment have been quite consistent across both in-situ and ex-vivo datasets: there are insufficient data to fit most model parameters to a specific specimen and, instead, defaults from the literature must be used. In an ideal case, a specimen would have roughly ten extra trials collected so that the maximum isometric force, optimal fiber length, active force-length relation, passive force-length relation (upto ≈ 0_._6_f_oM), and the force-velocity relations could be identified from measurements rather than relying on literature values. Since most lab specimens are viable for a small number of trials (with the exception of cat soleus), we don’t expect this situation to change in future.

However, if data are available the fitting process is pretty straight forward for either in-situ or ex-vivo data: use a standard numerical method (for example non-linear least squares, or the bisection method) to adjust the model parameters to reduce the errors between simulation and experiment. The main difficulty, as described in the previous paragraph, is the availability of data to fit as many parameters as possible for a specific specimen. As such, the fitting process really varies from experiment to experiment and depends mainly on the richness of measurements taken from a specific specimen, and from the literature in general.

Working from in-vivo data presents an entirely different set of challenges. When working with human data, for example, it’s just not possible to directly measure muscle force with tendon buckles, and so it is never completely clear how force is distributed across the many muscles that typically actuate a joint. Further, there is also uncertainty in the boundary condition of the muscle because optical motion capture markers will move with respect to the skeleton. Video fluoroscopy offers a method of improving the accuracy of measured boundary conditions, though only for a few labs due to its great expense. A final boundary condition remains impossible to measure in any case: the geometry and forces that act at the boundaries as muscle wraps over other muscles and bones. Fitting to in-vivo data are very difficult.

While this is an interesting topic, it is tangent to our already lengthy manuscript. Since these reviews are public, we’ll leave it to the motivated reader to find this text here.

Reviewer #2 (Public Review):

This model of skeletal muscle includes springs and dampers which aim to capture the effect of crossbridge and titin stiffness during the stretch of active muscle. While both crossbridge and titin stiffness have previously been incorporated, in some form, into models, this model is the first to simultaneously include both. The authors suggest that this will allow for the prediction of muscle force in response to short-, mid- and long-range stretches. All these types of stretch are likely to be experienced by muscle during in vivo perturbations, and are known to elicit different muscle responses. Hence, it is valuable to have a single model which can predict muscle force under all these physiologically relevant conditions. In addition, this model dramatically simplifies sarcomere structure to enable this muscle model to be used in multi-muscle simulations of whole-body movement.

In order to test this model, its force predictions are compared to 3 sets of experimental data which focus on short-, mid- and long-range perturbations, and to the predictions of a Hill-type muscle model. The choice of data sets is excellent and provide a robust test of the model’s ability to predict forces over a range of length perturbations. However, I find the comparison to a Hill-type muscle model to be somewhat limiting. It is well established that Hill-type models do not have any mechanism by which they can predict the effect of active muscle stretch. Hence, that the model proposed here represents an improvement over such a model is not a surprise. Many other models, some of which are also simple enough to be incorporated into whole-body simulations, have incorporated mechanistic elements which allow for the prediction of force responses to muscle stretch. And it is not clear from the results presented here that this model would outperform such models.

The paper begins by outlining the phenomenological vs mechanistic approaches taken to muscle modelling, historically. It appears, although is not directly specified, that this model combines these approaches. A somewhat mechanistic model of the response of the crossbridges and titin to active stretch is combined with a phenomenological implementation of force-length and force-velocity relationships. This combination of approaches may be useful improving the accuracy of predictions of muscle models and whole-body simulations, which is certainly a worthy goal. However, it also may limit the insight that can be gained. For example, it does not seem that this model could reflect any effect of active titin properties on muscle shortening. In addition, it is not clear to me, either physiologically or in the model, what drives the shift from the high stiffness in short-range perturbations to the somewhat lower stiffness in mid-range perturbations.

(1) It is well established that Hill-type models do not have any mechanism by which they can predict the effect of active muscle stretch.

While many muscle physiologists are aware of the limitations of the Hill model, these limitations are not so well known among computational biomechanists. There are at least two reasons for this gap: there are few comprehensive evaluations of Hill models against several experiments, and some of the differences are quite nuanced. For example, active lengthening experiments can be replicated reasonably well using a Hill model if the lengthening is done on the ascending limb of the force length curve. Clearly the story is quite different on the descending limb as shown in Figure 9. Similarly, as Figure 8 shows, by choosing the right combination of tendon model and perturbation bandwidth it is possible to get reasonably accurate responses from the Hill model to stochastic length changes. Yet when a wide variety of perturbation bandwidths, magnitudes, and tendon models are tested it is clear that the Hill model cannot, in general, replicate the response of muscle to stochastic perturbations. For these reasons we think many of the Hill model’s drawbacks have not been clearly understood by computational biomechanists for many years now.

(2) Many other models, some of which are also simple enough to be incorporated into whole-body simulations, have incorporated mechanistic elements which allow for the prediction of force responses to muscle stretch. And it is not clear from the results presented here that this model would outperform such models.

We agree that it will be valuable to benchmark other models in the literature using the same set of experiments. Hopefully we, or perhaps others, will have the good fortune to secure research funding to continue this benchmarking work. This will, however, be quite challenging: few muscle models are accompanied by a professional-quality open-source implementation. Without such an implementation it is often impossible to reproduce published results let alone provide a fair and objective evaluation of a model.

(3) For example, it does not seem that this model could reflect any effect of active titin properties on muscle shortening.

The titin model described in the paper will provide an enhancement of force during a stretch-shortening cycle. This certainly would be an interesting next experiment to simulate in a future paper.

(4) In addition, it is not clear to me, either physiologically or in the model, what drives the shift from the high stiffness in short-range perturbations to the somewhat lower stiffness in mid-range perturbations.

We can only respond to what drives the frequency dependent stiffness in the model, though we’re quite interested in what happens physiologically. Hopefully that there are some new experiments done to examine this phenomena in the future. In the case of the model, the reasons are pretty straight forward: the formulation of Eqn. 16 is responsible for this shift.

Equation 16 has been formulated so that the acceleration of the attachment point of the XE is driven by the force difference between the XE and a reference Hill model (numerator of the first term in Eqn. 16) which is then low pass filtered (denominator of the first term in Eqn. 16). Due to this formulation the attachment point moves less when the numerator is small, or when the differences in the numerator change rapidly and effectively become filtered out. When the attachment point moves less, more of the CE’s force output is determined by variations in the length of the XE and its stiffness.

On the other hand, the attachment point will move when the numerator of the first term in Eqn. 16 is large, or when those differences are not short lived. When the attachment point moves to reduce the strain in the XE, the force produced by the XE’s spring-damper is reduced. As a result, the CE’s force output is less influenced by variations of the length of the XE and its stiffness.

Reviewer #2 (Recommendations for the Authors):

I find the clarity of the manuscript to be much improved following revision. While I still find the combination of phenomenological and mechanistic approaches to be a little limiting with regards to our understanding of muscle contraction, the revised description of small length changes makes the interpretation much less confusing.

Similarly, while I agree that Hill-type models are widely used their limitations have been addressed extensively and are very well established. Hence, moving forward I think it would be much more valuable to start to compare these newer models to one another rather than just showing an improvement over a Hill model under (very biologically important) conditions which that model has no capacity to predict forces.

(1) While I still find the combination of phenomenological and mechanistic approaches to be a little limiting with regards to our understanding of muscle contraction ...

We have had to abstract some of the details of reality to have a model that can be used to simulate hundreds of muscles. In contrast, FiberSim produced by Kenneth Campbell’s group uses much less abstraction and might be of greater interest to you. FiberSim’s models include individual cross-bridges, titin molecules, and an explicit representation of the spatial geometry of a sarcomere. While this model is a great tool for testing muscle physiology questions through simulation, it is computationally expensive to use this model to simulate hundreds of muscles simultaneously.

Kosta S, Colli D, Ye Q, Campbell KS. FiberSim: A flexible open-source model of myofilament-level contraction. Biophysical journal. 2022 Jan 18;121(2):175-82.https://campbell-muscle-lab.github.io/FiberSim/

(2) Similarly, while I agree that Hill-type models are widely used their limitations have been addressed extensively and are very well established.

Please see our response 1 to Reviewer # 1.

(3) Hence, moving forward I think it would be much more valuable to start to compare these newer models to one another rather than just showing an improvement over a Hill model under (very biologically important) conditions which that model has no capacity to predict forces.

Please see our response to 2 to Reviewer #1.

The tabs on the top are very helpful to navigate the website easily

What kind of scenarios are there where people are scanning QR codes unnecessarily or haphazardly? The only time I use QR codes are when I need to scan the menu at a restaurant or if an event or a business would like me to get to a specific website via QR code to access a survey or something of that nature. While this scam is important to note and keep in mind for the future, it seems like the plausibility of people falling for this scam is lower than other scams.

1000000% agree, code is basically useless if you can't give it to someone else and they can work with your code as well or figure it out.

I actually do use ChatGPT to debug small errors, its great for when you've been staring at code for hours and can miss a small mistake

This is SO true! It's better to take a while meticulously writing the code in layers, making sure each respective step works before adding another layer. Otherwise debugging the whole thing is a nightmare! [ I'm in AME :') ]

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Reply to the reviewers

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

This manuscript investigates the dynamics of GC-content patterns in the 5'end of the transcription start sites (TSS) of protein-coding genes (pc-genes). The manuscript introduces a quite careful and comprehensive analysis of GC content in pc-genes in humans and other vertebrates, specially around the TSS. The result of this investigation states that "GC-content surrounding the TSS is largely influenced by patterns of recombination." (from end of Introduction)

My main concern with this manuscript is one of causal reasoning, whether intended or not. I hope the authors can follow my reasoning bellow on how the logic sometimes seems to fail, and that they introduce changes to clarify their suggested mechanisms of action.

The above quoted sentence form the end of the Intro is in conflict with this other sentence that appears at the end of the Abstract "the dynamics of GC-content in mammals are largely shaped by patterns of recombination". The sentence in the Intro seems to indicate that the effect is specific to TSSs, but the one in the abstract seem to indicate the opposite, that is, that the effect is ubiquitous.

We are sorry about the lack of clarity. We have now rewritten the abstract and intro to emphasize that our results are restricted to the 5' end of genes, and that by "patterns of recombination" we mean "historic patterns of recombination".

The observations as stated in the abstract are: "We observe that in primates and rodents, where recombination is directed away from TSSs by PRDM9, GC-content at protein-coding gene TSSs is currently undergoing mutational decay."

If I understand the measurements described in the manuscript correctly, and the arguments around them, you seem to show that the mutational decay of GC-content in humans is independent of location (TSSS or not), as noted here (also from the abstract) "These patterns extend into the open reading frame affecting protein-coding regions, and we show that changes in GC-content due to recombination affect synonymous codon position choices at the start of the open reading frame."

Again, we have rewritten this section to clarify these points.

There is one more result described in the manuscript, that in my mind is very important, but it is not given the relevance that it appears to me that it has. That is presented in Figure S3G. "we concluded that GC-content at the TSS of protein-coding genes is not at equilibrium, but in decay in primates and rodents. This decay rate is similar to the decay seen in intergenic regions that have the same GC-content (Figure S3G)"

Thus, if the decaying effect happens everywhere, how can it be related to "recombination being directed away from TSSs by PRDM9" as it is stated in the abstract and in the model described in Figure 7?

We make the argument that the GC-peak as likely caused by past recombination events. This is based on:

1) The change in GC-content at the TSS in Dogs and Fox, coupled to the fact that they perform recombination at the TSS

2) That the TSS can act as a default recombination site in mice when PRDM9 is knocked out

3) That some forms of PRDM9 allow for recombination at TSS (see Schield et al., 2020, Hoge et al. 2023, and Joseph et al., 2023) and that this is expected to cause an increase in GC-content

We thus speculate that the GC-peak in humans and rodents was caused by past recombination at TSSs that were permitted by ancient variants of PRDM9. We further point out that PRDM9 is undergoing rapid evolution, and some of the past versions of the protein may have had this property.

We have tried to clarify these points in the latest version of the text.

The fact that the decay rate is similar to any other region with similar GC-content should be an indication that the effect is not related to anything having to do with TSS or recombination being directed away from TSSs by PRDM9.

We are sorry about the lack of clarity. TSSs in humans, chimpanzees, mouse and rats are are experiencing GC-decay at the same rate as in non-functional DNA regions with high GC-content. Thus the GC-peak is not being maintained by selection. This is surprising, given the role that GC-content plays in gene expression. This is a critical point, and we added it to the "conclusion" section of the abstract.

I hope these paragraphs show my confusion about the relationship between the results presented which I think are very comprehensive and their interpretation and suggested model for GC-content dynamics around TSSs in human.

On another note, can you provided a bit more background on recombination and its mechanisms?

We have done our best to clarify these issues.

You seem to have confident sets of genes under high/low/med recombination. How are those determined.

We used the recombination rates per gene provided in Pouyet et al 2017 to identify the sets of genes under low/med/high recombination. Those rates were estimated from the HapMap genetic map (Frazer et al., 2007). This is now all specified in the methods section.

You also seem to concentrate the cause of recombination on PRDM9, please explain. Is PRDM9 the unique indicator of recombination?

PRDM9 has been shown to be the primary determinant of where recombination occurs in the genome (Grey et al., 2011, Brick et al., 2012). This is very well established. We now reword some of the introduction to make this clear.

specific comments

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Figure 1, it is very hard to understand the differences between the three rows. Please explain more clearly in the legend, and add more information to the figure itself.

We altered the axis titles to make this clearer. We also label "Upsream", "Exon 1" and "Part of Intron 1" in Figure 1C, F and I, and in Figure 2C. We now spell this out in the Figure Legend.

Figure 7, express somewhere in the figure that the y axis measures GC content.

We now added "GC Content" to the left of the first "graph" in Figure 7.

Figure seems to introduce a 'causal' model of GC-content dismissing (diminishing?) based on recombination being directed away from TSSs. How about the diminishing of GC-content on any other genomic regions as you have shown in Figure S3G?

Our focus in this model, and manuscript, is on TSSs. I think that to add the dynamics of other GC-rich regions is distracting. We do not know what caused these intergenic genomic regions to be high in GC-content prior to decay. After excluding known recombination sites and TSSs, these regions are very rare in the human genome. They may be ancient recombination sites that are decaying in GC-content. However, unlike TSSs, which have some connection to recombination (i.e. data from PRDM9 knockout mice and dogs and fox), we do not have any direct or indirect evidence that these other sites were used for recombination in the past. Alternatively, there could have been some other pressure on these sites in the past to increase GC-content that we are not aware of.

-- The title is too selective, as to the results, and it has the implication that the decay is exclusive to the surrounding of the TSSs.

Decay of GC-content towards equilibrium is the default state for non-functional DNA. That it is occurring at the TSS is surprising, as it indicates that the GC-peak is not maintained by selection. We now state this in the paper and include this in the "conclusion" portion of the abstract.

Reviewer #1 (Significance (Required)):

The statistical analysis is comprehensive and robust.

We thank the reviewer for this.

Their model interpretation as is describe induces confusion and needs to be clarified.

We are sorry about this. Hopefully our revised text will clear up the confusion.

I am an expert computational biologist, I do not have a deep knowledge of sequence implications of recombination, and it would be good if the manuscript could add some more background on that.

We thank the reviewer for their perspective, and we hope that our text changes better explain to the non-expert why our findings are so surprising. We further clarify how recombination affects DNA sequence by gBGC and some of these changes are detailed in our response to the other reviewers.

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

In this work, the author present various analyses suggesting that GC-content in TSS of coding genes is affected by recombination. The article findings are interesting and novel and are important to our understanding of how various non-adaptive evolutionary forces shape vertebrate genome evolutionary history.

We thank the reviewer for these kind words.

The Methods section includes most needed details (see comments below for missing information), and the scripts and data provided online help in transparency and usability of these analyses.

I have several comments, mostly regarding clarifications in the text and several suggestions:

1. In introduction: CpG islands, have been shown to activate transcription (Fenouil et al., 2012) - what is known about CpG Islands is somewhat inaccurately described. It should be rephrased more accurately, e.g. - CpG Islands found near TSS are associated with robust and high expression level of genes, including genes expressed in many tissues, such as housekeeping genes.

We thank the reviewer for that. We have rewrote this part of the introduction.

1. The following claim (in Introduction), regarding retrogenes and their GC content is not in agreement recent analyses: "Indeed, it has been observed that these genes have elevated GC-content at their 5' ends in comparison to their intron-containing counterparts, suggesting that elevation of GC-content can be driven by positive selection to drive their efficient export (Mordstein et al., 2020). Moreover, retrogenes tend to arise from parental genes that have high GC-content at their 5'ends (Kaessmann et al.,2009)." Recent work showed that retrogenes in mouse and human are significantly depleted of CpG islands in their promoters (PMID: 37055747). This follows the notion that young genes, such as these retrogenes, have simple promoters (PMID: 30395322) with few TF binding sites and without CpGs. The two reported trends should be both mentioned with some suggestions regarding why they seem to be contrasting each other and how they can be reconciled.

We thank the reviewer for this information. The previous report (Mordstein et al., 2020) indicated that the increase in GC-content occurs downstream of the TSS in retrogenes. Since sequences upstream of the TSS are not part of the retro-insertion, it is not surprising that GC-content may differ between the retrogene and the parental gene. That retrogenes have lower numbers of CpGs upstream of the TSS, bolsters the idea that GC-content is not required for transcription and that the GC-peak is not being maintained in most genes by purging selection.

1. In "Thus GC-content is expected, and is indeed observed to be higher near recombination hotspots due to gBGC (REF)." I think you forgot the reference...

We thank the reviewer for catching this.

1. In Results, regarding average GC content (Fig 2X): "Interestingly, this pattern is different in the nonamniotes examined, including anole lizard, coelacanth, shark and lamprey." - in lizard, it seems that the genomic average is lower (and lizards are amniotes)

You are absolutely right. We now fix this.

1. In Discussion, the statement: "This model is supported by findings in a recent preprint, which documents the equilibrium state of GC-content in TSS regions from numerous organisms" seems to contrast with the findings of the mentioned preprint. If "most mammals have a high GC-content equilibrium state" but still have a functional PRDM9, in the lack of evidence for functional differences between ortholog PRDM9 proteins (such as signatures for positive selection or functional assays), the authors' findings regarding the relationship between a lack of PRDM9 in canids and the trends observed in their TSS, are weakened.

We are sorry about the confusion. We were not exactly sure what points were being commented on. 1) whether GC-content is at equilibrium for most mammals or 2) that the equilibrium state is high for most mammals despite containing PRDM9. We rewrote this sentence to clarify both issues (especially given that these concepts may not be clear to non-experts, such as the first reviewer). To answer the first potential concern, the paper in question (Joseph et al., 2023), does not show that GC-content at the TSS in mammals is at equilibrium, rather, it calculates what the equilibrium state is given the nucleotide substitution rates. In most organisms, the TSS is not at equilibrium. To answer both 1 and 2, Joseph et al., show that the equilibrium GC-content at the TSS for canids is much higher than for other mammals. They and others infer that the diversity between other mammals (where the equilibrium state is higher than humans and rodents but lower than canids) has to do with the variation between PRDM9 orthologues, however this has yet to be tested. Although the action of PRDM9 has not been evaluated in most mammals, we do point out that in snakes PRDM9 allows for some recombination at the TSS.

1. In Methods, the ENSEMBL version (in addition of the per-species genome version) should be mentioned.

This has been fixed.

1. In Fig 1, it is worth clarifying in the legend that the differences between the first and second rows of panels is in the length of the plotted region.

We have now indicated this in the figure legend.

Reviewer #2 (Significance (Required)):

The manuscript provides a rigorous analysis of the possible processes that have impacted the TSS GC-content during evolution. It should be of interest to a diverse set of investigators in the genomics community, since it touches on different topics including genome evolution, transcription and gene structures.

Thank you.

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

This study analyzes the distribution of GC-content along genes in humans and vertebrates, and particularly the higher GC-content in the 5'-end than in the 3'-end of genes. The results suggest that this pattern is ancient in vertebrates, currently decaying in mouse and humans, and probably driven by recombination and GC-biased gene conversion. It is proposed that the 5'-3' gradient was generated during evolution when PRDM9 was less active (in which case recombination occurs mostly near transcription start sites), and decays when PRDM9 is very active, as it is currently in humans and mouse. This is a very interesting hypothesis, also corroborated by a recent, similar analysis in mammals (Joseph et al. 2023). These two preprints, which appeared around the same time, are, I think, quite novel and important. The analyses performed here are thorough and convincing. Source code and raw data sets are openly distributed. I only have a couple of minor comments and suggestions, which I hope might help improve the manuscript.

Thank you very much for the kind words.

A1. There has been quite some work on the 5'-3' GC-content gradient in plants (e.g. Clément et al. 2014 GBE, Ressayre et al. 2015 GBE, Brazier & Glemin 2023 biorxiv), which you might like to cite.

Thank you for pointing out these very interesting papers, we have incorporated them into the latest version.

A2. CpG-content and GC-content are related in various ways (e.g. see Galtier & Duret 2000 MBE, Fryxell & Moon 2005 MBE) that you might like to discuss; currently the manuscript discusses the CpG hypermutation rate as a driver of GC-content but the picture might be a bit more complex.

Thank you for this, we have incorporated these citations.

A3. The model introduced by this manuscript (figure 7) is dependent on the evolution of recombination determination in vertebrates and the role of PRDM9. A recent preprint by Raynaud et al (biorxiv) seems relevant to this issue.

Thank you for pointing out this pre-print. We have added a paragraph to the discussion that mentions this work. This also initiated a conversation with the authors, and we include some "personal communications" that illuminate what is going on in teleost fish.

Line-by-line comments

B1. "First, highly spliced mRNAs tend to have high GC-content at their 5' ends despite the fact that it is not required for export and does not affect expression levels (Mordstein et al., 2020)" -> I do not totally understand this sentence, which seems to imply some link between splicing and export/expression, could you please clarify?

We rewrote that sentence to make it clearer.

B2. "mismatches will form in the heteroduplex which are typically corrected in favor of Gs and Cs over As and Ts by about 70%" -> This 70% figure is human-specific, and varies a lot among species; I know in this introduction you're mainly reviewing the human literature but since this part of the text introduces gBGC as a process maybe clarify by adding "in humans" or refrain from giving this figure?

Thank you. This is a good point. We fixed this.

B3. "Thus GC-content is expected, and is indeed observed to be higher near recombination hotspots due to gBGC (REF)." -> reference missing here; actually I'm not sure you will find a good reference for this because PRDM9-dependent hotspots are so short-lived that GC-content would only respond weakly; mayber rather refer to the equilibrium GC-content (and cite, for instance, Pratto et al 2014 Science), or to high-recombining regions instead of hotspots (and you have plenty of papers to cite)?

Thanks for this.

B4. Paragraph starting: "PRDM9 and recombination hotspots also experience accelerated rates of evolution..." -> I would suggest removing the word "also" and moving this paragraph up, just before the sentence I'm commenting above (the one starting "Thus GC-content..."). This will justify my suggestion in comment B3 of mentioning high-recombining regions instead of hotspots, while also avoiding to have the important paragraph on recombination at TSS (the one starting "There are interesting connections...") being sandwiched between two sections on PRDM9.

We did not move this paragraph, although we did adjust the wording slightly.

B5. Paragraph starting "There are interesting connections..." is crucial to your discussion and might be emphasized a bit more in introduction, in my opinion. For instance, what about adding a sentence like "Also not directly relevant to humans, these observations suggest that gBGC might have played a role in shaping the observed 5'-3' GC-content gradient."

We did not alter the structure of this paragraph but we did reword sections of it.

1. "Interestingly, this pattern is different in the non-amniotes examined, including anole lizard, coelacanth, shark and lamprey. These organisms had clear differences in GC-content between their first exon and surrounding sequences (upstream and intronic sequences), which came close to the overall genomic GC-content." -> I'm not sure I got the point the authors are intending to make here. Also please note that lizards are amniotes.

We thank the reviewer for catching this error, we have fixed this.

Reviewer #3 (Significance (Required)):

This is one of two preprints having appeared ~at the same time (the other one being the cited Joseph et al 2023), which I think are quite important and convincing regarding the role of PRDM9-dependent and PRDM9-independent recombination on GC-content evolution in vertebrates. I support publication of this preprint in a molecular evolutionary journal.

We thank the reviewer for their kind assessment!

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

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Referee #3

Evidence, reproducibility and clarity

This study analyzes the distribution of GC-content along genes in humans and vertebrates, and particularly the higher GC-content in the 5'-end than in the 3'-end of genes. The results suggest that this pattern is ancient in vertebrates, currently decaying in mouse and humans, and probably driven by recombination and GC-biased gene conversion. It is proposed that the 5'-3' gradient hass generated during evolution when PRDM9 was less active (in which case recombination occurs mostly near transcription start sites), and decays when PRDM9 is very active, as it is currently in humans and mouse. This is a very interesting hypothesis, also corroborated by a recent, similar analysis in mammals (Joseph et al. 2023). These two preprints, which appeared around the same time, are, I think, quite novel and important. The analyses performed here are thorough and convincing. Source code and raw data sets are openly distributed. I only have a couple of minor comments and suggestions, which I hope might help improve the manuscript.

A1. There has been quite some work on the 5'-3' GC-content gradient in plants (e.g. Clément et al. 2014 GBE, Ressayre et al. 2015 GBE, Brazier & Glemin 2023 biorxiv), which you might like to cite.

A2. CpG-content and GC-content are related in various ways (e.g. see Galtier & Duret 2000 MBE, Fryxell & Moon 2005 MBE) that you might like to discuss; currently the manuscript discusses the CpG hypermutation rate as a driver of GC-content but the picture might be a bit more complex.

A3. The model introduced by this manuscript (figure 7) is dependent on the evolution of recombination determination in vertebrates and the role of PRDM9. A recent preprint by Raynaud et al (biorxiv) seems relevant to this issue.

Line-by-line comments

B1. "First, highly spliced mRNAs tend to have high GC-content at their 5' ends despite the fact that it is not required for export and does not affect expression levels (Mordstein et al., 2020)" -> I do not totally understand this sentence, which seems to imply some link between splicing and export/expression, could you please clarify?

B2. "mismatches will form in the heteroduplex which are typically corrected in favor of Gs and Cs over As and Ts by about 70%" -> This 70% figure is human-specific, and varies a lot among species; I know in this introduction you're mainly reviewing the human literature but since since this part of the text introduces gBGC as a process maybe clarify by adding "in humans" or refrain from giving this figure?

B3. "Thus GC-content is expected, and is indeed observed to be higher near recombination hotspots due to gBGC (REF)." -> reference missing here; actually I'm not sure you will find a good reference for this because PRDM9-dependent hotspots are so short-lived that GC-content would only respond weakly; mayber rather refer to the equilibrium GC-content (and cite, for instance, Pratto et al 2014 Science), or to high-recombining regions instead of hotspots (and you have plenty of papers to cite)?

B4. Paragraph starting: "PRDM9 and recombination hotspots also experience accelerated rates of evolution..." -> I would suggest removing the word "also" and moving this paragraph up, just before the sentence I'm commenting above (the one starting "Thus GC-content..."). This will justify my suggestion in comment B3 of mentioning high-recombining regions instead of hotspots, while also avoiding to have the important paragraph on recombination at TSS (the one starting "There are interesting connections...") being sandwiched between two sections on PRDM9.

B5. Paragraph starting "There are interesting connections..." is crucial to your discussion and might be emphasized a bit more in introduction, in my opinion. For instance, what about adding a sentence like "Also not directly relevant to humans, these observations suggest that gBGC might have played a role in shaping the observed 5'-3' GC-content gradient."

1. "Interestingly, this pattern is different in the non-amniotes examined, including anole lizard, coelacanth, shark and lamprey. These organisms had clear differences in GC-content between their first exon and surrounding sequences (upstream and intronic sequences), which came close to the overall genomic GC-content." -> I'm not sure I got the point the authors are intending to make here. Also please note that lizards are amniotes.

Significance

This is one of two preprints having appeared ~at the same time (the other one being the cited Joseph et al 2023), which I think are quite important and convincing regarding the role of PRDM9-dependent and PRDM9-independent recombination on GC-content evolution in vertebrates. I support publication of this preprint in a molecular evolutionary journal.

Name

Rolle

Beschreibung

Enthält die Rolle des Akteurs als Eintrag aus der MARC Code List for Relators mit lobid-spezifischem Label.

Verwendungsbeispiele

• Ressourcen mit "Robert Craft" als Dirigenten.
• Ressourcen mit Angabe von Schauspieler:innen und Dirigent:innen im Stadttheater zu Düsseldorf.
• Ressourcen mit Harry Rowohlt als Übersetzer

URI

http://id.loc.gov/ontologies/bibframe/role

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

The manuscript "Self-inhibiting percolation and viral spreading in epithelial tissue" describes a model based on 5-state cellular automata of development of an infection. The model is motivated and qualitatively justified by time-resolved measurements of expression levels of viral, interferon-producing, and antiviral genes. The model is set up in such a way that the crucial difference in outcomes (infection spreading vs. confinement) depends on the initial fraction of special virus-sensing cells. Those cells (denoted as 'type a') cannot be infected and do not support the propagation of infection, but rather inhibit it in a somewhat autocatalytic way. Presumably, such feedback makes the transition between two outcomes very sharp: a minor variation in concentration of ``a' cells results in qualitative change from one outcome to another. As in any percolation-like system, the transition between propagation and inhibition of infection goes through a critical state with all its attributes. A power-law distribution of the cluster size (corresponding to the fraction of infected cells) with a fairly universal exponent and a cutoff at the upper limit of this distribution.

Strengths:

The proposed model suggests an explanation for the apparent diversity of outcomes of viral infections such as COVID.

Author response: We thank the referee for the concise and accurate summary of our work.

Weaknesses:

Those are not real points of weakness, though I think addressing them would substantially improve the manuscript.

Author response: Below we will address these point by point.

The key point in the manuscript is the reduction of actual biochemical processes to the NOVAa rules. I think more could be said about it, be it referring to a set of well-known connections between expression states of cells and their reaction to infection or justifying it as an educated guess.

Author response: We have now improved this part in the model section. We have added a few sentences explaining how the cell state transitions are motivated by the UMAP results:

“The cell state transitions triggered by IFN signaling or viral replication are known in viral infection, but how exactly the transitions are orchestrated for specific infections is poorly understood. The UMAP cell state distribution hints at possible preferred transitions between states. The closer two cell states are on the UMAP, the more likely transitions between them are, all else being equal. For instance, the antiviral state (𝐴) is easily established from a susceptible cell (𝑂), but not from the fully virus-hijacked cell (𝑉 ). The IFN-secreting cell state (𝑁) requires the co-presence of the viral and antiviral genes and thus the cell cluster is located between the antiviral state (𝐴) and virus-infected state (𝑉 ) but distant from the susceptible cells (𝑂).

Inspired by the UMAP data visualization (Fig. 1a), we propose the following transitions between five main discrete cell states”

Another aspect where the manuscript could be improved would be to look a little beyond the strange and 'not-so-relevant for a biomedical audience' focus on the percolation critical state. While the presented calculation of the precise percolation threshold and the critical exponent confirm the numerical skills of the authors, the probability that an actual infected tissue is right at the threshold is negligible. So in addition to the critical properties, it would be interesting to learn about the system not exactly at the threshold: For example, how the speed of propagation of infection depends on subcritical p_a and what is the cluster size distribution for supercritical p_a.

Author response: We agree that further exploring the model away from the critical threshold is worthwhile. While our main focus has been on explaining the large degree of heterogeneity in outcomes – readily explained as a consequence of the sharp threshold-like behavior – we now include plots of the time-evolution of the infection (as well as the remaining states) over time for subcritical values of pa. The plots can be found in Figure S4 of the supplement.

Reviewer #2 (Public Review):

Xu et al. introduce a cellular automaton model to investigate the spatiotemporal spreading of viral infection. In this study, the author first analyzes the single-cell RNA sequencing data from experiments and identifies four clusters of cells at 48 hours post-viral infection, including susceptible cells (O), infected cells (V), IFN-secreting cells (N), and antiviral cells (A). Next, a cellular automaton model (NOVAa model) is introduced by assuming the existence of a transient pre-antiviral state (a). The model consists of an LxL lattice; each site represents one cell. The cells change their state following the rules depending on the interaction of neighboring cells. The model introduces a key parameter, p_a, representing the fraction of pre-antiviral state cells. Cell apoptosis is omitted in the model. Model simulations show a threshold-like behavior of the final attack rate of the virus when p_a changes continuously. There is a critical value p_c, so that when p_a < p_c, infections typically spread to the entire system, while at a higher p_a > p_c, the propagation of the infected state is inhibited. Moreover, the radius R that quantifies the diffusion range of N cells may affect the critical value p_c; a larger R yields a smaller value of the critical value p_c. The structure of clusters is different for different values of R; greater R leads to a different microscopic structure with fewer A and N cells in the final state. Compared with the single-cell RNA seq data, which implies a low fraction of IFN-positive cells - around 1.7% - the model simulation suggests R=5. The authors also explored a simplified version of the model, the OVA model, with only three states. The OVA model also has an outbreak size. The OVA model shows dynamics similar to the NOVAa model. However, the change in microstructure as a function of the IFN range R observed in the NOVAa model is not observed in the OVA model.

Author response: We thank the referee for the comprehensive summary of our work.

Data and model simulation mainly support the conclusions of this paper, but some weaknesses should be considered or clarified.

Author response: Thank you - we will address these point by point below.

(1) In the automaton model, the authors introduce a parameter p_a, representing the fraction of pre-antiviral state cells. The authors wrote: ``The parameter p_a can also be understood as the probability that an O cell will switch to the N or A state when exposed to the virus of IFNs, respectively.' Nevertheless, biologically, the fraction of pre-antiviral state cells does not mean the same value as the probability that an O cell switches to the N or A state. Moreover, in the numerical scheme, the cell state changes according to the deterministic role N(O)=a and N(a)=A. Hence, the probability p_a did not apply to the model simulation. It may need to clarify the exact meaning of the parameter p_a.

Author response: We acknowledge that this was an imprecise formulation, and have now changed it.

What we tried to convey with that comment was that, alternatively to having a certain fraction of cells be in the a state initially, one could instead have devised a model in which We should note that even the current model has a level of stochasticity, since we choose the cells to be updated with a constant probability rate - we choose N cells to update in each timestep, with replacement.

However, based on your suggestion, we simulated a version of the dynamics which included stochastic conversion, i.e. each action of a cell on a nearby cell happens only with a probability p_conv (and the original model is recovered as the p_conv=1 scenario). Of course, this slows down the dynamics (or effectively rescales time by a factor p_conv), but crucially we find that it does not appreciably affect the location of the threshold p_c. Below we include a parameter scan across p_a values for R=1 and p_conv=0.5, which shows that the threshold continues to appear at around p_a=27%. each O-state cell simply had a probability to act as an a-state cell upon exposure to the virus or to interferons, i.e. to switch to an N state (if exposed to virus) or to the A state (if exposed to interferons). In this simplified model, there would be no functional difference, since it would simply amount to whether each cell had a probability to be designated an a-cell initially (as in our model), or upon exposure. So our remark mainly served to explain that the role of the p_a parameter is simply to encode that a certain fraction of virus-naive cells behave this way (whether predetermined or not).

(2) The current model is deterministic. However, biologically, considering the probabilistic model may be more realistic. Are the results valid when the probability update strategy is considered? By the probability model, the cells change their state randomly to the state of the neighbor cells. The probability of cell state changes may be relevant for the threshold of p_a. It is interesting to know how the random response of cells may affect the main results and the critical value of p_a.

Author response: This is a good point - we are firm believers in the importance of stochasticity. We should note that even the current model has a level of stochasticity, since we choose the cells to be updated with a constant probability rate - we choose N cells to update in each timestep, with replacement.

However, based on your suggestion, we simulated a version of the dynamics which included stochastic conversion, i.e. each action of a cell on a nearby cell happens only with a probability p_conv (and the original model is recovered as the p_conv=1 scenario). Of course, this slows down the dynamics (or effectively rescales time by a factor p_conv), but crucially we find that it does not appreciably affect the location of the threshold p_c. Below we include a parameter scan across p_a values for R=1 and p_conv=0.5, which shows that the threshold continues to appear at around p_a=27%.

We now discuss these findings in the supplement and include the figure below as Fig. S5.

Author response image 1.

(3) Figure 2 shows a critical value p_c = 27.8% following a simulation on a lattice with dimension L = 1000. However, it is unclear if dimension changes may affect the critical value.

Author response: Re-running the simulations on a lattice 4x as large (i.e. L=2000) yields a similar critical value of 27-28% for R=1, so we are confident that finite size effects do not play a major role at L=1000 and beyond. For R=5, however, we find that a minimum lattice size greater than L=1000 is necessary to determine the critical threshold. Concretely, we find that the threshold value pc for R=5 changes somewhat when the lattice size is increased from 1000 to 2000, but is invariant under a change from 2000 to 3000, so we conclude that L=2000 is sufficient for R=5. The pc value for R=5 cited in the manuscript (~0.4%) was determined from simulations at L=2000.

Reviewer #3 (Public Review):

Summary:

This study considers how to model distinct host cell states that correspond to different stages of a viral infection: from naïve and susceptible cells to infected cells and a minority of important interferon-secreting cells that are the first line of defense against viral spread. The study first considers the distinct host cell states by analyzing previously published single-cell RNAseq data. Then an agent-based model on a square lattice is used to probe the dependence of the system on various parameters. Finally, a simplified version of the model is explored, and shown to have some similarity with the more complex model, yet lacks the dependence on the interferon range. By exploring these models one gains an intuitive understanding of the system, and the model may be used to generate hypotheses that could be tested experimentally, telling us "when to be surprised" if the biological system deviates from the model predictions.

Author response: Thank you for the summary! We agree with the role that you describe for a model such as this one.

Strengths:

-  Clear presentation of the experimental findings and a clear logical progression from these experimental findings to the modeling.

-  The modeling results are easy to understand, revealing interesting behavior and percolation-like features.

-  The scaling results presented span several decades and are therefore compelling. - The results presented suggest several interesting directions for theoretical follow-up work, as well as possible experiments to probe the system (e.g. by stimulating or blocking IFN secretion).

Weaknesses:

-  Since the "range" of IFN is an important parameter, it makes sense to consider lattice geometries other than the square lattice, which is somewhat pathological. Perhaps a hexagonal lattice would generalize better.

-  Tissues are typically three-dimensional, not two-dimensional. (Epithelium is an exception). It would be interesting to see how the modeling translates to the three-dimensional case. Percolation transitions are known to be very sensitive to the dimensionality of the system.

Author response: We agree that probing different lattice geometries (2- and 3-dimensional alike) would be interesting and worthwhile. However, for this manuscript, we prefer to confine the analysis to the current, simple case. We do agree, however, that an extensive exploration of the role of geometry is an interesting future possibility.

-  The fixed time-step of the agent-based modeling may introduce biases. I would consider simulating the system with Gillespie dynamics where the reaction rates depend on the ambient system parameters.

-  Single-cell RNAseq data typically involves data imputation due to the high sparsity of the measured gene expression. More information could be provided on this crucial data processing step since it may significantly alter the experimental findings.

Justification of claims and conclusions:

The claims and conclusions are well justified.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

It is necessary to explain what UMAP does. Is clustering done in the space of twenty-something original dimensions or 2D? How UMAP1 and UMAP2 are selected and are those the same in all plots?

Author response: We have now added a few sentences to clarify the point raised above - the second snippet explains how clustering is performed:

“As a dimension reduction algorithm, UMAP is a manifold learning technique that favors the preservation of local distances over global distances (McInnes et al., 2018; Becht et al., 2019). It constructs a weighted graph from the data points and optimizes the graph layout in the low-dimensional space.”

“We cluster the cells with the principal components analysis (PCA) results from their gene expression. With the first 16 principal components, we calculate k-nearest neighbors and construct the shared nearest neighbor graph of the cells then optimize the modularity function to determine clusters. We present the cluster information on the UMAP plane and use the same UMAP coordinates for all the plots in this paper hereafter.”

Figure 1, what do bars in the upper right corners of panels d,e,f, and g indicate? ``Averaged' refers to time average? Something is missing in ``Cell proportions are labeled with corresponding colors in a)' .

Author response: Thank you - we have now modified the figure caption. The bars in the upper right corners of panels d, e, f are color keys for gene expression, the brighter the color is, the higher the gene expression is.

“Averaged” gene expression refers to the mean expression of that particular gene across the cells within each indicated cluster.

The lines in c) correspond to cell proportions in different states at different time points. The same state in 1) and c) is shown in the same color.

Line 46, ``However' does not sound right in this context. Would ``Also' be better?

Author response: We agree and have corrected it in the revised manuscript.

Line 96``The viral genes are also partially expressed in these cells, but different from the 𝑁 cluster, the antiviral genes are fully expressed (Fig. S1 and S2).' The sentence needs to be rephrased.

Author response: We have rephrased the sentence: “As in the N cluster, the viral gene E is barely detected in these cells, indicating incomplete viral replication. However, in contrast to the N cluster, the antiviral genes are expressed to their full extent (Fig. S1 and S2).”

Line 126, missing "be", ``large' -> ``larger'.

Author response: Thank you, we have now corrected these typos.

Line 139-140 The logical link between ignoring apoptosis and the diffusion of IFN is unclear.

Author response: We modified the sentence as “Here, we assume that the secretion of IFNs by the 𝑁 cells is a faster process than possible apoptosis (Wen et al., 1997; Tesfaigzi, 2006) of these cells and that the diffusion of IFNs to the neighborhood is not significantly affected by apoptosis.”

Fig. 2a Do the yellow arrows show the effect of IFN and the purple arrows the propagation of viral infection?

Author response: That is correct. We have added this information to the figure caption: “The straight black arrows indicate transitions between cell states. The curved yellow arrows indicate the effects of IFNs on activating antiviral states. The curved purple arrows indicate viral spread to cells with 𝑂 and 𝑎 states.”

Fig. 3, n(s) as the axis label vs P(s) in the text? How do the curves in panel a) look when the p_a is well above or below p_c?

Author response: Thank you. We have edited the labels in the figure to reflect the symbols used in the text.

Boundary conditions? From Fig. 4, apparently periodic?

Author response: Yes, we use periodic boundary conditions in the model. We clarify it in the model section now (last sentence).

It will be good to see a plot with time dependences of all cell types for a couple of values of p_a, illustrating propagation and cessation of the infection.

Author response: We agree, and have added a Figure S4 in the supplement which explores exactly that. Thank you for the suggestion.

A verbal qualitative description of why p_a has such importance and how the infection is terminated for large p_a would help.

Reviewer #2 (Recommendations For The Authors):

Below are two minor comments:

(1) In the single-cell RNA sequencing data analysis, the authors describe the cell clusters O, V, A, and N. However, showing how the clusters are identified from the data might be more straightforward.

Author response: Technically, we cluster the cells using principal components analysis (PCA) results of their gene expression. With the first 16 principal components, we calculate k-nearest neighbors and construct the shared nearest neighbor graph of the cells and then optimize the modularity function to determine clusters. We manually annotate the clusters with O, V, A, and N based on the detected abundance of viral genes, antiviral genes, and IFNs.

(2) In Figure 3, what does n(s) mean in Figure 3a? And what is the meaning of the distribution P(s) of infection clusters? It may be stated clearly.

Author response: The use of n(s) was inconsistent, and we have now edited the figure to instead say P(s), to harmonize it with the text. P(s) is the distribution of cluster sizes, s, expressed as a fraction of the whole system. In other words, once a cluster has reached its final size, we record s=(N+V)/L^2 where N and V are the number of N and V state cells in the cluster (note that, by design, each simulation leads to a single cluster, since we seed the infection in one lattice point). We now indicate more clearly in the caption and the main text what exactly P(s) and s refer to.

Reviewer #3 (Recommendations For The Authors):

- Would the authors kindly share the simulation code with the community? Also, the data analysis code should be shared to follow current best practices. This needs to be standard practice in all publications. I would go as far as to say that in 2024 publishing a data analysis / simulation study without sharing the relevant code should be ostracized by the community.

Author response: We absolutely agree and have created a GitHub repository in which we share the C++ source code for the simulations and a Python notebook for plotting. The public repository can be found at https://github.com/BjarkeFN/ViralPercolation. We add this information in supplement under section “Code availability”.

­

- I would avoid the use of the wording "critical" threshold since this is almost guaranteed to infuriate a certain type of reader.

­

- Line 265 has a curious use of " ... " which should be replaced with something more appropriate.

Author response: Thank you for pointing it out! We have checked the typos.

Yes and Yes -- This indicates a client that received RUN services through the Tri (Jefferson) County Workforce Board. Several of the regional workforce boards had both a RUN grant and a WIG grant (slightly different). Given these frequencies, I think the best we can do is explore the data by Coaching Collaborative and Trade Association Training. However, before I ask you to do that, could you please run the frequencies by zip code? The final question on the survey is the participants' zip code. I'd like to see if there is value in looking at regional differences, but before we do that, let's see if there's enough variability to make that worth it. Thank you!

“ No contexto educacional, os alunosde diferentes lugares do mundo conseguem interagir entre eles, por meio da linguagem oral, gráfica e gestual, pois os avatares possibilitam manifestações de gestos e emoções”

Eu gosto de interagir no engage, uma plataforma profissional onde os avatares têm um dress code entre o casual e o executivo, Neste ambiente eu tenho formações interactivas, com exercícios um a um, com workshops , de tal forma imerso os que me esqueço que sou em casa. Temos a possibilidade de estar com pessoas de vários países, sem custos.

Uso, para trabalho a plataforma virtual speech para treino de entrevistas de embuscada, para treino em palco para plateias, enfim, nas áreas do public speaking e é impressionante o resultado de, após uma formação fora d emetaverso, os nossos clientes podem treinar no metaverso num role play imersivo como se na situação real se encontrassem.

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

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Reply to the reviewers

General Statements

We thank all three reviewers for their time and care in reviewing our manuscript, in particular Reviewer 3 for providing a detailed critique that was very useful for planning revisions. We are grateful that all three reviewers indicate that the new genome resources presented in this work are of high-quality and address an existing knowledge gap. We are also grateful for general assessments that the manuscript is 'well-written', and the analyses 'well performed' and 'thorough'.

We acknowledge Reviewer 3’s legitimate criticism that the assembly and annotation data is not already publicly available and would like to assure the reviewing team that we have been pressing NCBI to progress the submission status since before the preprint was submitted. We regret the delay but hope that we can resolve this issue promptly. Furthermore, as some additional fields in the REAT genome annotation are lost during the NCBI submission process, we will ensure that comprehensive annotation files are also added to Zenodo.

Reviewer 3 also made the general comment that 'the manuscript could greatly benefit from merging the result and discussion sections' and we would naturally be happy to make this adjustment if the journal in question uses that format.

Description of the planned revisions

• We will follow suggestions by Reviewer 3 to improve clarity of two figures:

Figure S9: Please use a more appropriate colour palette. It is difficult to know the copy number based on the colour gradient.

Figure 5: Consider changing panel B for a similar version of Fig S12. I think it gives a cleaner and more general perspective of the presence of starship elements.

• We will address the choice of LOESS versus linear regression for investigating the relationship between candidate secreted effector protein (CSEP) density and transposable element (TE) density, as queried by Reviewer 3:

Lines 140-144: LOESS smoothing functions are based on local regressions and usually find correlations when there are very weak associations. The authors have to justify the use of this model versus a simpler and more straightforward linear regression. My suspicion is that the latter would fail to find an association. Also, there is no significance of Kendall's Tau estimate (p-value).

We agree with the reviewer, that as we did not find an association with the more sensitive LOESS, we expect that linear regression would also not find an association, supporting our current conclusions. We will add this negative result into the text.

• We will check for other features associated with the distribution of CSEPs, as queried by Reviewer 3:

Lines 157-163: Was there any other feature associated with the CSEP enrichment? GC content? Repetitive content? Centromere likely localisation?

• We will integrate TE variation into the PERMANOVA lifestyle testing, as suggested by Reviewer 3:

Line 186: Why not to test the variation content of TEs as a factor for the PERMANOVA?

In reviewing this suggestion, we also spotted an error in our data plotting code, and the PERMANOVA lifestyle result for all genes will be corrected from 17% to 15% in Fig. 4a. Correcting this error does not impact our ultimate results or interpretation.

• To complement the current graphical-based assessment of approximate data normality, we will include additional tests (Shapiro-Wilk for sample sizes

Line 743: Q-Q plots are not a formal statistical test for normality.

• One of the main critiques from Reviewer 3 was that, although we already acknowledged low sample sizes being a limitation of this work, the manuscript could benefit from reframing with greater consideration of this factor. They also highlighted a few specific places in the text that could be rephrased in consideration of this:

Line 267: "Multiple strains" can be misleading about the magnitude.

Lines 305-307: The fact that there is significant copy number variation between the two GtA strains suggests that the variation in the GtA lineage has not been fully captured and that there may be an unsampled substructure. Although the authors acknowledge the need for pangenomic references, they should recognize this limitation in the sample size of their own study, especially when expressing its size as "multiple strains" (line 267).

Lines 314-317: Again, the sample size is still very small and likely not representative. It suggests UNSAMPLED substructure even for the UK populations.

Line 164 (and whole section): I would invite the authors to cautiously revisit the use of the terms "core", "soft core". The sample size is very low, as they themselves acknowledge, and probably not representative of the diversity of Gaeumannomyces.

We intend to edit the text to address this, including removal of both text and figure references to ‘soft-core’ genes, as we agree the term is likely not meaningful in this case, and removing it has no bearing on the results or interpretation.

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

• We have amended the text in a number of places for clarity/fluency as suggested by Reviewer 3:

ii) There need to be an explicit conclusion about the differences between pathogenic Gt and non-pathogenic Gh. Somehow, this is not entirely clear and is probably only a matter of rephrasing.

Please see new lines 477-478: ‘Regarding differences between pathogenic Gt and non-pathogenic Gh, we found that Gh has a larger overall genome size and greater number of genes.’

Lines 309-314: The message seems a bit out of context in the paragraph.

This is valid, these lines have now been removed.

Lines 392-395: The idea that crop pathogenic fungi are under pressure that favours heterothallism does not take into account the multiple cases of successful pathogenic clonal lineages in which sexual reproduction is absent. This paragraph seems very speculative to me. Please rephrase it.

Our intention here was the exact reverse, that crop pathogens are under pressure to favour homothallism (as Reviewer 3 points out, anecdotally this often seems to play out in nature). We have rephrased lines 386-390 to hopefully make our stance more explicit: 'Together, this could suggest a selective pressure towards homothallism for crop fungal pathogens, and a switch from heterothallism in Gh to homothallism in Gt and Ga may, therefore, have been a key innovation underlying lifestyle divergence between non-pathogenic Gh and pathogenic Gt and Ga.'

Lines 463-464: Please refer to the analyses when discussing the genetic divergence.

We have rephrased this sentence to make our intended point clearer, please see new lines 459-461: ‘If we compare Ga and Gt in terms of synteny, genome size and gene content, the magnitude of differences does not appear to be more pronounced than those between GtA and GtB.’

• We have also fixed the following typographic errors highlighted by Reviewer 3:

Line 399: You mean, Fig 4C?

Line 722: You missed "trimAI"

Lines 723-727: Missing citations for "AMAS" and RAxML-NG, "AHDR" and "OrthoFinder"

• We have added genome-wide RIP estimates to Supplementary Table S1 as requested by Reviewer 3:

Lines 416-422: Please provide the data related to the genome-wide estimates of RIP.

• We have added a note clarifying that differences in overall genome size between lineages are not fully explained by differences in gene copy-number (lines 406-408: 'We should note that the total length of HCN genes was not sufficiently large to account for the overall greater genome size of GtB compared to GtA (Supplemental Table S1).') in response to a comment from Reviewer 3:

Line 396: The difference in duplicated genes raises the question of whether there are differences in overall genome size between lineages and, if so, whether they can be explained by the presence of genes.

• We have made an alteration to the author order and added equal second-author contributions.

Description of analyses that authors prefer not to carry out

• In response to our analysis regarding the absence of TE-effector compartmentalisation in this system, Reviewer 1 requested additional analyses:

While TE enrichment is typically associated with accessory compartments, it is not a defining feature. To bolster the authors' claim, it is essential to demonstrate that there is no bias in the ratio of conserved and non-conserved genes across the genomes.

We believe that there are two slightly different compartmentalisation concepts being somewhat conflated here – (1) the idea of compartments where TEs and virulence proteins such as effectors are significantly colocalised in comparison with the rest of the genome, and (2) the idea of compartments containing gene content that is not shared in all strains (i.e. accessory). The two may overlap – as Reviewer 2 states, accessory compartments may also be enriched with TEs – but not necessarily. We specifically address the first concept in our text, and we appreciate Reviewer 3’s response on this subject:

There is a clear answer for the compartmentalisation question. The authors favour the idea of "one-compartment" with compelling analyses.

We believe that the second concept of accessory compartments is shown to be irrelevant in this case from our GENESPACE results (see Fig. 2), which demonstrate that gene content is conserved, broadly syntenic even, across strains, with no clear evidence of accessory compartments or chromosomes regarding gene content. We have already acknowledged that other mechanisms of compartmentalisation beyond TE-effector colocalisation may be at play (as seen from our exploration of effector distributions biased towards telomeres, see section from line 156: ‘Although CSEPs were not broadly colocalised with TEs, we did observe that they appeared to be non-randomly distributed in some pseudochromosomes (Fig. 3a)…’).

• Reviewer 1 questioned the statement that higher level of genome-wide RIP is consistent with lower levels of gene duplication:

L422: Is the highest RIP rate in GtA consistent with its low levels of gene duplication? Does this suggest that duplicated sequences in GtA are no longer recognizable due to RIP mutations? This seems counterintuitive, as RIP is primarily triggered by gene duplication.

Our understanding is that, while RIP can directly mutate coding regions, it predominantly acts on duplicated sequences within repetitive regions such as TEs (https://genomebiology.biomedcentral.com/articles/10.1186/s13059-020-02060-w), which has a knock-on effect of reducing TE-mediated gene duplication. In Neurospora crassa, where RIP was first discovered and thus the model species for much of our understanding of the process, a low number of gene duplicates has been linked to the activity of RIP (https://www.nature.com/articles/nature01554). We therefore believe the current text is reasonable.

• Reviewer 2 stated that experimental validation of gene function is required to make clear links to lifestyle or pathogenicity:

In my eyes, the study has two main limitations. First of all, the research only concerns genomics analyses, and therefore is rather descriptive and observational, and as such does not provide further mechanistic details into the pathogen biology and/or into pathogenesis. This is further enhanced by the lack of clear observations that discriminate particular species/lineages or life styles from others in the study. Some observations are made with respect to variations in candidate secreted effector proteins and biosynthetic gene clusters, but clear links to life style or pathogenicity are missing. To further substantiate such links, lab-based experimental work would be required.

We agree that in an ideal world supportive wet biology gene function experimental evidence would be included. Unfortunately, transformation has not been successfully developed yet in this system (see lines 33-35: ‘There have also been considerable difficulties in producing a reliable transformation system for Gt, preventing gene disruption experiments to elucidate function (Freeman and Ward 2004).’) not for lack of trying – after 18 months of effort using all available transformation techniques and selectable markers neither Gt or Gh was transformable. Undertaking that challenge has proven to be far beyond the scope of this paper, the purpose of which was to generate and analyse high-quality genomic data, a major task in itself. We again appreciate Reviewer 3’s response to this point, agreeing that it is out of scope for this work:

I just want to respectfully disagree with reviewer #2 about the need for more experimental laboratory work, as in my opinion it clearly goes beyond the intention and scope of the submitted work. This could be a limitation that would depend on the chosen journal and its specific format and requirements. Finally, I think it would suffice for the authors to discuss on the lack of in-depth experimental work as part of the limitations of their overall approach.

As per the suggestion by Reviewer 3, we will add text to address the absence of in-depth experimental work within the scope of this study.

• Reviewer 3 suggested we might 'consider including formal population differentiation estimators', however, as they previously highlighted above, our sample sizes are too small to produce reliable population-level statistics.

• Reviewer 3 raised the disparity in the appearance of branches at the root of phylogenetic trees in various figures:

Figure 4a (and Figs S5, S13): The depicted tree has a trichotomy at the basal node. Please correct it so Magnaporthiopsis poae is resolved as an outgroup, as in Fig. S17.

All the trees were rooted with M. poae as the outgroup, and although it may seem counterintuitive, a trifurcation at the root is the correct outcome in the case of rerooting a bifurcating tree, please see this discussion including the developers of both leading phylogeny visualisation tools ggtree and phytools (https://www.biostars.org/p/332030/). Although it is possible to force a bifurcating tree after rooting by positioning the root along an edge, the resulting branch lengths in the tree can be misleading, and so in cases where we wanted to include meaningful branch lengths in the figure (i.e. estimated from DNA substitute rates, in Figures 4a, S5 and S13) we have not circumvented the trifurcation. In Fig S17 meaningful branch lengths have not been included and the tree only represents the topology, resulting in the appearance of bifurcation at the root.

• Reviewer 3 suggested that the discussion on giant Starship TEs resembled more of a review:

Lines 434-451: This section resembles more a review than a discussion of the results of the present work. This also highlights the lack of analysis on the genetic composition and putative function of the identified starship-like elements.

The reviewer has a valid point. However, Starships are a recently discovered and thus underexplored genetic feature that readers from the wider mycology/plant pathology community may not yet be aware of. We believe it is warranted to include some additional exposition to give context for why their discovery here is novel, interesting and unexpected. We are naturally keen to investigate the make-up of the elements we have found in this lineage, however that will require a substantial amount of further work. Analysis of Starships is not trivial, for example the starfish tool is still under development and a limited number of species have been used to train it. How best to compare elements is also an active area of investigation – they are dynamic in their structure and may include genes originating from the host genome or a previous host – and for this reason we believe is out of scope to interrogate alongside the other foundational genomic data presented in this paper.

here, g is the gini index, not to be confused with the label g that tells the code what measures to use in the bootstrap

pause the machine

for - metaphor - genes - musical scores - Denis Noble

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Reply to the reviewers

Reply to the Reviewers

We thank the referees for their careful reading of the manuscript and their valuable suggestions for improvements.

General Statements:

Existing SMC-based loop extrusion models successfully predict and characterize mesoscale genome spatial organization in vertebrate organisms, providing a valuable computational tool to the genome organization and chromatin biology fields. However, to date this approach is highly limited in its application beyond vertebrate organisms. This limitation arises because existing models require knowledge of CTCF binding sites, which act as effective boundary elements, blocking loop-extruding SMC complexes and thus defining TAD boundaries. However, CTCF is the predominant boundary element only in vertebrates. On the other hand, vertebrates only contain a small proportion of species in the tree of life, while TADs are nearly universal and SMC complexes are largely conserved. Thus, there is a pressing need for loop extrusion models capable of predicting Hi-C maps in organisms beyond vertebrates.

The conserved-current loop extrusion (CCLE) model, introduced in this manuscript, extends the quantitative application of loop extrusion models in principle to any organism by liberating the model from the lack of knowledge regarding the identities and functions of specific boundary elements. By converting the genomic distribution of loop extruding cohesin into an ensemble of dynamic loop configurations via a physics-based approach, CCLE outputs three-dimensional (3D) chromatin spatial configurations that can be manifested in simulated Hi-C maps. We demonstrate that CCLE-generated maps well describe experimental Hi-C data at the TAD-scale. Importantly, CCLE achieves high accuracy by considering cohesin-dependent loop extrusion alone, consequently both validating the loop extrusion model in general (as opposed to diffusion-capture-like models proposed as alternatives to loop extrusion) and providing evidence that cohesin-dependent loop extrusion plays a dominant role in shaping chromatin organization beyond vertebrates.

The success of CCLE unambiguously demonstrates that knowledge of the cohesin distribution is sufficient to reconstruct TAD-scale 3D chromatin organization. Further, CCLE signifies a shifted paradigm from the concept of localized, well-defined boundary elements, manifested in the existing CTCF-based loop extrusion models, to a concept also encompassing a continuous distribution of position-dependent loop extrusion rates. This new paradigm offers greater flexibility in recapitulating diverse features in Hi-C data than strictly localized loop extrusion barriers.

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

This manuscript presents a mathematical model for loop extrusion called the conserved-current loop extrusion model (CCLE). The model uses cohesin ChIP-Seq data to predict the Hi-C map and shows broad agreement between experimental Hi-C maps and simulated Hi-C maps. They test the model on Hi-C data from interphase fission yeast and meiotic budding yeast. The conclusion drawn by the authors is that peaks of cohesin represent loop boundaries in these situations, which they also propose extends to other organism/situations where Ctcf is absent.

__Response: __

We would like to point out that the referee's interpretation of our results, namely that, "The conclusion drawn by the authors is that peaks of cohesin represent loop boundaries in these situations, ...", is an oversimplification, that we do not subscribe to. The referee's interpretation of our model is correct when there are strong, localized barriers to loop extrusion; however, the CCLE model allows for loop extrusion rates that are position-dependent and take on a range of values. The CCLE model also allows the loop extrusion model to be applied to organisms without known boundary elements. Thus, the strict interpretation of the positions of cohesin peaks to be loop boundaries overlooks a key idea to emerge from the CCLE model.

__ Major comments:__

1. More recent micro-C/Hi-C maps, particularly for budding yeast mitotic cells and meiotic cells show clear puncta, representative of anchored loops, which are not well recapitulated in the simulated data from this study. However, such punta are cohesin-dependent as they disappear in the absence of cohesin and are enhanced in the absence of the cohesin release factor, Wapl. For example - see the two studies below. The model is therefore missing some key elements of the loop organisation. How do the authors explain this discrepency? It would also be very useful to test whether the model can predict the increased strength of loop anchors when Wapl1 is removed and cohesin levels increase.

Costantino L, Hsieh TS, Lamothe R, Darzacq X, Koshland D. Cohesin residency determines chromatin loop patterns. Elife. 2020 Nov 10;9:e59889. doi: 10.7554/eLife.59889. PMID: 33170773; PMCID: PMC7655110. Barton RE, Massari LF, Robertson D, Marston AL. Eco1-dependent cohesin acetylation anchors chromatin loops and cohesion to define functional meiotic chromosome domains. Elife. 2022 Feb 1;11:e74447. doi: 10.7554/eLife.74447. Epub ahead of print. PMID: 35103590; PMCID: PMC8856730.

__Response: __

We are perplexed by this referee comment. While we agree that puncta representing loop anchors are a feature of Hi-C maps, as noted by the referee, we would reinforce that our CCLE simulations of meiotic budding yeast (Figs. 5A and 5B of the original manuscript) demonstrate an overall excellent description of the experimental meiotic budding yeast Hi-C map, including puncta arising from loop anchors. This CCLE model-experiment agreement for meiotic budding yeast is described and discussed in detail in the original manuscript and the revised manuscript (lines 336-401).

To further emphasize and extend this point we now also address the Hi-C of mitotic budding yeast, which was not included the original manuscript. We have now added an entire new section of the revised manuscript entitled "CCLE Describes TADs and Loop Configurations in Mitotic S. cerevisiae" including the new Figure 6, which presents a comparison between a portion of the mitotic budding yeast Hi-C map from Costantino et al. and the corresponding CCLE simulation at 500 bp-resolution. In this case too, the CCLE model well-describes the data, including the puncta, further addressing the referee's concern that the CCLE model is missing some key elements of loop organization.

Concerning the referee's specific comment about the role of Wapl, we note that in order to apply CCLE when Wapl is removed, the corresponding cohesin ChIP-seq in the absence of Wapl should be available. To our knowledge, such data is not currently available and therefore we have not pursued this explicitly. However, we would reinforce that as Wapl is a factor that promotes cohesin unloading, its role is already effectively represented in the optimized value for LEF processivity, which encompasses LEF lifetime. In other words, if Wapl has a substantial effect it will be captured already in this model parameter.

1. Related to the point above, the simulated data has much higher resolution than the experimental data (1kb vs 10kb in the fission yeast dataset). Given that loop size is in the 20-30kb range, a good resolution is important to see the structural features of the chromosomes. Can the model observe these details that are averaged out when the resolution is increased?

__Response: __

We agree with the referee that higher resolution is preferable to low resolution. In practice, however, there is a trade-off between resolution and noise. The first experimental interphase fission yeast Hi-C data of Mizuguchi et al 2014 corresponds to 10 kb resolution. To compare our CCLE simulations to these published experimental data, as described in the original manuscript, we bin our 1-kb-resolution simulations to match the 10 kb experimental measurements. Nevertheless, CCLE can readily predict the interphase fission yeast Hi-C map at higher resolution by reducing the bin size (or, if necessary, reducing the lattice site size of the simulations themselves). In the revised manuscript, we have added comparisons between CCLE's predicted Hi-C maps and newer Micro-C data for S. pombe from Hsieh et al. (Ref. [50]) in the new Supplementary Figures 5-9. We have chosen to present these comparisons at 2 kb resolution, which is the same resolution for our meiotic budding yeast comparisons. Also included in Supplementary Figures 5-9 are comparisons between the original Hi-C maps of Mizuguchi et al. and the newer maps of Hsieh et al., binned to 10 kb resolution. Inspection of these figures shows that CCLE provides a good description of Hsieh et al.'s experimental Hi-C maps and does not reveal any major new features in the interphase fission yeast Hi-C map on the 10-100 kb scale, that were not already apparent from the Hi-C maps of Mizuguchi et al 2014. Thus, the CCLE model performs well across this range of effective resolutions.

3. Transcription, particularly convergent has been proposed to confer boundaries to loop extrusion. Can the authors recapitulate this in their model?

__Response: __

In response to the suggestion of the reviewer we have now calculated the correlation between cohesin ChIP-seq and the locations of convergent gene pairs, which is now presented in Supplementary Figures 17 and 18. Accordingly, in the revised manuscript, we have added the following text to the Discussion (lines 482-498):

"In vertebrates, CTCF defines the locations of most TAD boundaries. It is interesting to ask what might play that role in interphase S. pombe as well as in meiotic and mitotic S. cerevisiae. A number of papers have suggested that convergent gene pairs are correlated with cohesin ChIP-seq in both S. pombe [65, 66] and S. cerevisiae [66-71]. Because CCLE ties TADs to cohesin ChIP-seq, a strong correlation between cohesin ChIP-seq and convergent gene pairs would be an important clue to the mechanism of TAD formation in yeasts. To investigate this correlation, we introduce a convergent-gene variable that has a nonzero value between convergent genes and an integrated weight of unity for each convergent gene pair. Supplementary Figure 17A shows the convergent gene variable, so-defined, alongside the corresponding cohesin ChIP-seq for meiotic and mitotic S. cerevisiae. It is apparent from this figure that a peak in the ChIP-seq data is accompanied by a non-zero value of the convergent-gene variable in about 80% of cases, suggesting that chromatin looping in meiotic and mitotic S. cerevisiae may indeed be tied to convergent genes. Conversely, about 50% of convergent genes match peaks in cohesin ChIP-seq. The cross-correlation between the convergent-gene variable and the ChIP-seq of meiotic and mitotic S. cerevisiae is quantified in Supplementary Figures 17B and C. By contrast, in interphase S. pombe, cross-correlation between convergent genes and cohesin ChIP-seq in each of five considered regions is unobservably small (Supplementary Figure 18A), suggesting that convergent genes per se do not have a role in defining TAD boundaries in interphase S. pombe."

Minor comments:

1. In the discussion, the authors cite the fact that Mis4 binding sites do not give good prediction of the HI-C maps as evidence that Mis4 is not important for loop extrusion. This can only be true if the position of Mis4 measured by ChIP is a true reflection of Mis4 position. However, Mis4 binding to cohesin/chromatin is very dynamic and it is likely that this is too short a time scale to be efficiently cross-linked for ChIP. Conversely, extensive experimental data in vivo and in vitro suggest that stimulation of cohesin's ATPase by Mis4-Ssl3 is important for loop extrusion activity.

__Response: __

We apologize for the confusion on this point. We actually intended to convey that the absence of Mis4-Psc3 correlations in S. pombe suggests, from the point of view of CCLE, that Mis4 is not an integral component of loop-extruding cohesin, during the loop extrusion process itself. We agree completely that Mis4/Ssl3 is surely important for cohesin loading, and (given that cohesin is required for loop extrusion) Mis4/Ssl3 is therefore important for loop extrusion. Evidently, this part of our Discussion was lacking sufficient clarity. In response to both referees' comments, we have re-written the discussion of Mis4 and Pds5 to more carefully explain our reasoning and be more circumspect in our inferences. The re-written discussion is described below in response to Referee #2's comments.

Nevertheless, on the topic of whether Nipbl-cohesin binding is too transient to be detected in ChIP-seq, the FRAP analysis presented by Rhodes et al. eLife 6:e30000 "Scc2/Nipbl hops between chromosomal cohesin rings after loading" indicates that, in HeLa cells, Nipbl has a residence time bound to cohesin of about 50 seconds. As shown in the bottom panel of Supplementary Fig. 7 in the original manuscript (and the bottom panel of Supplementary Fig. 20 in the revised manuscript), there is a significant cross-correlation (~0.2) between the Nipbl ChIP-seq and Smc1 ChIP-seq in humans, indicating that a transient association between Nipbl and cohesin can be (and in fact is) detected by ChIP-seq.

1. *Inclusion of a comparison of this model compared to previous models (for example bottom up models) would be extremely useful. What is the improvement of this model over existing models? *

__Response: __

As stated in the original manuscript, as far as we are aware, "bottom up" models, that quantitatively describe the Hi-C maps of interphase fission yeast or meiotic budding yeast or, indeed, of eukaryotes other than vertebrates, do not exist. Bottom-up models would require knowledge of the relevant boundary elements (e.g. CTCF sites), which, as stated in the submitted manuscript, are generally unknown for fission yeast, budding yeast, and other non-vertebrate eukaryotes. The absence of such models is the reason that CCLE fills an important need. Since bottom-up models for cohesin loop extrusion in yeast do not exist, we cannot compare CCLE to the results of such models.

In the revised manuscript we now explicitly compare the CCLE model to the only bottom-up type of model describing the Hi-C maps of non-vertebrate eukaryotes by Schalbetter et al. Nat. Commun. 10:4795 2019, which we did cite extensively in our original manuscript. Schalbetter et al. use cohesin ChIP-seq peaks to define the positions of loop extrusion barriers in meiotic S. cerevisiae, for which the relevant boundary elements are unknown. In their model, specifically, when a loop-extruding cohesin anchor encounters such a boundary element, it either passes through with a certain probability, as if no boundary element is present, or stops extruding completely until the cohesin unbinds and rebinds.

In the revised manuscript we refer to this model as the "explicit barrier" model and have applied it to interphase S. pombe, using cohesin ChIP-seq peaks to define the positions of loop extrusion barriers. The corresponding simulated Hi-C map is presented in Supplementary Fig. 19 in comparison with the experimental Hi-C. It is evident that the explicit barrier model provides a poorer description of the Hi-C data of interphase S. pombe compared to the CCLE model, as indicated by the MPR and Pearson correlation scores. While the explicit barrier model appears capable of accurately reproducing Hi-C data with punctate patterns, typically accompanied by strong peaks in the corresponding cohesin ChIP-seq, it seems less effective in several conditions including interphase S. pombe, where the Hi-C data lacks punctate patterns and sharp TAD boundaries, and the corresponding cohesin ChIP-seq shows low-contrast peaks. The success of the CCLE model in describing the Hi-C data of both S. pombe and S. cerevisiae, which exhibit very different features, suggests that the current paradigm of localized, well-defined boundary elements may not be the only approach to understanding loop extrusion. By contrast, CCLE allows for a concept of continuous distribution of position-dependent loop extrusion rates, arising from the aggregate effect of multiple interactions between loop extrusion complexes and chromatin. This paradigm offers greater flexibility in recapitulating diverse features in Hi-C data than strictly localized loop extrusion barriers.

We have also added the following paragraph in the Discussion section of the manuscript to elaborate this point (lines 499-521):

"Although 'bottom-up' models which incorporate explicit boundary elements do not exist for non-vertebrate eukaryotes, one may wonder how well such LEF models, if properly modified and applied, would perform in describing Hi-C maps with diverse features. To this end, we examined the performance of the model described in Ref. [49] in describing the Hi-C map of interphase S. cerevisiae. Reference [49] uses cohesin ChIP-seq peaks in meiotic S. cerevisiae to define the positions of loop extrusion barriers which either completely stall an encountering LEF anchor with a certain probability or let it pass. We apply this 'explicit barrier' model to interphase S. pombe, using its cohesin ChIP-seq peaks to define the positions of loop extrusion barriers, and using Ref. [49]'s best-fit value of 0.05 for the pass-through probability. Supplementary Figure 19A presents the corresponding simulated Hi-C map the 0.3-1.3 kb region of Chr 2 of interphase S. pombe in comparison with the corresponding Hi-C data. It is evident that the explicit barrier model provides a poorer description of the Hi-C data of interphase S. pombe compared to the CCLE model, as indicated by the MPR and Pearson correlation scores of 1.6489 and 0.2267, respectively. While the explicit barrier model appears capable of accurately reproducing Hi-C data with punctate patterns, typically accompanied by strong peaks in the corresponding cohesin ChIP-seq, it seems less effective in cases such as in interphase S. pombe, where the Hi-C data lacks punctate patterns and sharp TAD boundaries, and the corresponding cohesin ChIP-seq shows low-contrast peaks. The success of the CCLE model in describing the Hi-C data of both S. pombe and S. cerevisiae, which exhibit very different features, suggests that the current paradigm of localized, well-defined boundary elements may not be the only approach to understanding loop extrusion. By contrast, CCLE allows for a concept of continuous distribution of position-dependent loop extrusion rates, arising from the aggregate effect of multiple interactions between loop extrusion complexes and chromatin. This paradigm offers greater flexibility in recapitulating diverse features in Hi-C data than strictly localized loop extrusion barriers."

Reviewer #1 (Significance (Required)):

This simple model is useful to confirm that cohesin positions dictate the position of loops, which was predicted already and proposed in many studies. However, it should be considered a starting point as it does not faithfully predict all the features of chromatin organisation, particularly at better resolution.

Response:

As described in more detail above, we do not agree with the assertion of the referee that the CCLE model "does not faithfully predict all the features of chromatin organization, particularly at better resolution" and provide additional new data to support the conclusion that the CCLE model provides a much needed approach to model non-vertebrate contact maps and outperforms the single prior attempt to predict budding yeast Hi-C data using information from cohesin ChIP-seq.

*It will mostly be of interest to those in the chromosome organisation field, working in organisms or systems that do not have ctcf. *

__Response: __

We agree that this work will be of special interest to researchers working on chromatin organization of non-vertebrate organisms. We would reinforce that yeast are frequently used models for the study of cohesin, condensin, and chromatin folding more generally. Indeed, in the last two months alone there are two Molecular Cell papers, one Nature Genetics paper, and one Cell Reports paper where loop extrusion in yeast models is directly relevant. We also believe, however, that the model will be of interest for the field in general as it simultaneously encompasses various scenarios that may lead to slowing down or stalling of LEFs.

This reviewer is a cell biologist working in the chromosome organisation field, but does not have modelling experience and therefore does not have the expertise to determine if the modelling part is mathematically sound and has assumed that it is.

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

Summary: Yuan et al. report on their development of an analytical model ("CCLE") for loop extrusion with genomic-position-dependent speed, with the idea of accounting for barriers to loop extrusion. They write down master equations for the probabilities of cohesin occupancy at each genomic site and obtain approximate steady-state solutions. Probabilities are governed by cohesin translocation, loading, and unloading. Using ChIP-seq data as an experimental measurement of these probabilities, they numerically fit the model parameters, among which are extruder density and processivity. Gillespie simulations with these parameters combined with a 3D Gaussian polymer model were integrated to generate simulated Hi-C maps and cohesin ChIP-seq tracks, which show generally good agreement with the experimental data. The authors argue that their modeling provides evidence that loop extrusion is the primary mechanism of chromatin organization on ~10-100 kb scales in S. pombe and S. cerevisiae.

Major comments:

1. I am unconvinced that this analysis specifically is sufficient to demonstrate that extrusion is the primary organizer of chromatin on these scales; moreover, the need to demonstrate this is questionable, as extrusion is widely accepted, even if not universally so. How is the agreement of CCLE with experiments more demonstrative of loop extrusion than previous modeling?

__Response: __

We agree with the referee's statement that "loop extrusion is extrusion is widely accepted, even if not universally so". We disagree with the referee that this state of affairs means that "the need to demonstrate this (i.e. loop extrusion) is questionable". On the contrary, studies that provide further compelling evidence that cohesin-based loop extrusion is the primary organizer of chromatin, such as ours, must surely be welcomed, first, in order to persuade those who remain unconvinced by the loop extrusion mechanism in general, and, secondly, because, until the present work, quantitative models of loop extrusion, capable of reproducing Hi-C maps quantitatively, in yeasts and other non-vertebrate eukaryotes have been lacking, leaving open the question of whether loop extrusion can describe Hi-C maps beyond vertebrates. CCLE has now answered that question in the affirmative. Moreover, the existence of a robust model to predict contact maps in non-vertebrate models, which are extensively used in the pursuit of research questions in chromatin biology, will be broadly enabling to the field.

It is fundamental that if a simple, physically-plausible model/hypothesis is able to describe experimental data quantitatively, it is indeed appropriate to ascribe considerable weight to that model/hypothesis (until additional data become available to refute the model).

How is the agreement of CCLE with experiments more demonstrative of loop extrusion than previous modeling?

Response:

As noted above and in the original manuscript, we are unaware of previous quantitative modeling of cohesin-based loop extrusion and the resultant Hi-C maps in organisms that lack CTCF, namely non-vertebrate eukaryotic models such as fission yeast or budding yeast, as we apply here. As noted in the original manuscript, previous quantitative modeling of Hi-C maps based on cohesin loop extrusion and CTCF boundary elements has been convincing that loop extrusion is indeed relevant in vertebrates, but the restriction to vertebrates excludes most of the tree of life.

Below, the referee cites two examples of loop extrusion outside of vertebrates. The one that is suggested to correspond to yeast cells (Dequeker et al. Nature 606:197 2022) actually corresponds to mouse cells, which are vertebrate cells. The other one models the Hi-C map of the prokaryote, Bacillus subtilis, based on loop extrusion of the bacterial SMC complex thought to most resemble condensin (not cohesin), subject to barriers to loop extrusion that are related to genes or involving prokaryote-specific Par proteins (Brandao et al. PNAS 116:20489 2019). We have referenced this work in the revised manuscript but would reinforce that it lacks utility in predicting the contact maps for non-vertebrate eukaryotes.

Relatedly, similar best fit values for S. pombe and S. cerevisiae might not point to a mechanistic conclusion (same "underlying mechanism" of loop extrusion), but rather to similar properties for loop-extruding cohesins in the two species.

Response:

In the revised manuscript, we have replaced "suggesting that the underlying mechanism that governs loop extrusion by cohesin is identical in both species" with "suggesting loop-extruding cohesins possess similar properties in both species" (lines 367-368).

As an alternative, could a model with variable binding probability given by ChIP-seq and an exponential loop-size distribution work equally well? The stated lack of a dependence on extrusion timescale suggests that a static looping model might succeed. If not, why not?

Response:

A hypothetical mechanism that generates the same instantaneous loop distributions and correlations as loop extrusion would lead to the same Hi-C map as does loop extrusion. This circumstance is not confined to CCLE, but is equally applicable to previous CTCF-based loop extrusion models. It holds because Hi-C and ChIP-seq, and therefore models that seek to describe these measurements, provide a snapshot of the chromatin configuration at one instant of time.

We would reinforce that there is no physical basis for a diffusion capture model with an approximately-exponential loop size distributions. Nevertheless, one can reasonably ask whether a physically-sensible diffusion capture model can simultaneously match cohesin ChIP-seq and Hi-C. Motivated by the referee's comment we have addressed this question and, accordingly, in the revised manuscript, we have added (1) an entire subsection entitled "Diffusion capture does not reproduce experimental interphase S. pombe Hi-C maps" (lines 303-335) and (2) Supplementary Figure 15. As we now demonstrate, the CCLE model vastly outperforms an equilibrium binding model in reproducing the experimental Hi-C maps and measured P(s).

*2. I do not understand how the loop extrusion residence time drops out. As I understand it, Eq 9 converts ChIP-seq to lattice site probability (involving N_{LEF}, which is related to \rho, and \rho_c). Then, Eqs. 3-4 derive site velocities V_n and U_n if we choose rho, L, and \tau, with the latter being the residence time. This parameter is not specified anywhere and is claimed to be unimportant. It may be true that the choice of timescale is arbitrary in this procedure, but can the authors please clarify? *

__Response: __

As noted above, Hi-C and ChIP-seq both capture chromatin configuration at one instant in time. Therefore, such measurements cannot and do not provide any time-scale information, such as the loop extrusion residence time (LEF lifetime) or the mean loop extrusion rate. For this reason, neither our CCLE simulations, nor other researchers' previous simulations of loop extrusion in vertebrates with CTCF boundary elements, provide any time-scale information, because the experiments they seek to describe do not contain time-scale information. The Hi-C map simulations can and do provide information concerning the loop size, which is the product of the loop lifetime and the loop extrusion rate. Lines 304-305 of the revised manuscript include the text: "Because Hi-C and ChIP-seq both characterize chromatin configuration at a single instant of time, and do not provide any direct time-scale information, ..."

In practice, we set the LEF lifetime to be some explicit value with arbitrary time-unit. We have added a sentence in the Methods that reads, "In practice, however, we set the LEF dissociation rate to 5e-4 time-unit-1 (equivalent to a lifetime of 2000 time-units), and the nominal LEF extrusion rate (aka \rho*L/\tau, see Supplementary Methods) can be determined from the given processivity" (lines 599-602), to clarify this point. We have also changed the terminology from "timesteps" to "LEF events" in the manuscript as the latter is more accurate for our purpose.

1. The assumptions in the solution and application of the CCLE model are potentially constraining to a limited number of scenarios. In particular the authors specify that current due to binding/unbinding, A_n - D_n, is small. This assumption could be problematic near loading sites (centromeres, enhancers in higher eukaryotes, etc.) (where current might be dominated by A_n and V_n), unloading sites (D_n and V_{n-1}), or strong boundaries (D_n and V_{n-1}). The latter scenario is particularly concerning because the manuscript seems to be concerned with the presence of unidentified boundaries. This is partially mitigated by the fact that the model seems to work well in the chosen examples, but the authors should discuss the limitations due to their assumptions and/or possible methods to get around these limitations.

4. Related to the above concern, low cohesin occupancy is interpreted as a fast extrusion region and high cohesin occupancy is interpreted as a slow region. But this might not be true near cohesin loading and unloading sites.

__Response: __

Our response to Referee 2's Comments 3. and 4. is that both in the original manuscript and in the revised manuscript we clearly delineate the assumptions underlying CCLE and we carefully assess the extent to which these assumptions are violated (lines 123-126 and 263-279 in the revised manuscript). For example, Supplementary Figure 12 shows that across the S. pombe genome as a whole, violations of the CCLE assumptions are small. Supplementary Figure 13 shows that violations are similarly small for meiotic S. cerevisiae. However, to explicitly address the concern of the referee, we have added the following sentences to the revised manuscript:

Lines 277-279:

"While loop extrusion in interphase S. pombe seems to well satisfy the assumptions underlying CCLE, this may not always be the case in other organisms."

Lines 359-361:

"In addition, the three quantities, given by Eqs. 6, 7, and 8, are distributed around zero with relatively small fluctuations (Supplementary Fig. 13), indicating that CCLE model is self-consistent in this case also."

In the case of mitotic S. cerevisiae, Supplementary Figure 14 shows that these quantities are small for most of genomic locations, except near the cohesin ChIP-seq peaks. We ascribe these greater violations of CCLE's assumptions at the locations of cohesin peaks in part to the low processivity of mitotic cohesin in S. cerevisiae, compared to that of meiotic S. cerevisiae and interphase S. pombe, and in part to the low CCLE loop extrusion rate at the cohesin peaks. We have added a paragraph at the end of the Section "CCLE Describes TADs and Loop Configurations in Mitotic S. cerevisiae" to reflect these observations (lines 447-461).

1. *The mechanistic insight attempted in the discussion, specifically with regard to Mis4/Scc2/NIPBL and Pds5, is problematic. First, it is not clear how the discussion of Nipbl and Pds5 is connected to the CCLE method; the justification is that CCLE shows cohesin distribution is linked to cohesin looping, which is already a questionable statement (point 1) and doesn't really explain how the model offers new insight into existing Nipbl and Pds5 data. *

Furthermore, I believe that the conclusions drawn on this point are flawed, or at least, stated with too much confidence. The authors raise the curious point that Nipbl ChIP-seq does not correlate well with cohesin ChIP-seq, and use this as evidence that Nipbl is not a part of the loop-extruding complex in S. pombe, and it is not essential in humans. Aside from the molecular evidence in human Nipbl/cohesin (acknowledged by authors), there are other reasons to doubt this conclusion. First, depletion of Nipbl (rather than binding partner Mau2 as in ref 55) in mouse cells strongly inhibits TAD formation (Schwarzer et al. Nature 551:51 2017). Second, at least two studies have raised concerns about Nibpl ChIP-seq results: 1) Hu et al. Nucleic Acids Res 43:e132 2015, which shows that uncalibrated ChIP-seq can obscure the signal of protein localization throughout the genome due to the inability to distinguish from background * and 2) Rhodes et al. eLife 6:e30000, which uses FRAP to show that Nipbl binds and unbinds to cohesin rapidly in human cells, which could go undetected in ChIP-seq, especially when uncalibrated. It has not been shown that these dynamics are present in yeast, but there is no reason to rule it out yet.*

Similar types of critiques could be applied to the discussion of Pds5. There is cross-correlation between Psc3 and Pds5 in S. pombe, but the authors are unable to account for whether Pds5 binding is transient and/or necessary to loop extrusion itself or, more importantly, whether Pds5 ChIP is associated with extrusive or cohesive cohesins; cross-correlation peaks at about 0.6, but note that by the authors own estimates, cohesive cohesins are approximately half of all cohesins in S. pombe (Table 3).

*Due to the above issues, I suggest that the authors heavily revise this discussion to better reflect the current experimental understanding and the limited ability to draw such conclusions based on the current CCLE model. *

__Response: __

As stated above, our study demonstrates that the CCLE approach is able to take as input cohesin (Psc3) ChIP-seq data and produce as output simulated Hi-C maps that well reproduce the experimental Hi-C maps of interphase S. pombe and meiotic S. cerevisiae. This result is evident from the multiple Hi-C comparison figures in both the original and the revised manuscripts. In light of this circumstance, the referee's statement that it is "questionable", that CCLE shows that cohesin distribution (as quantified by cohesin ChIP-seq) is linked to cohesin looping (as quantified by Hi-C), is demonstrably incorrect.

However, we did not intend to suggest that Nipbl and Pds5 are not crucial for cohesin loading, as the reviewer states. Rather, our inquiries relate to a more nuanced question of whether these factors only reside at loading sites or, instead, remain as a more long-lived constituent component of the loop extrusion complex. We regret any confusion and have endeavored to clarify this point in the revised manuscript in response to Referee 2's Comment 5. as well as Referee 1's Minor Comment 1. We have now better explained how the CCLE model may offer new insight from existing ChIP-seq data in general and from Mis4/Nipbl and Pds5 ChIP-seq, in particular. Accordingly, we have followed Referee 2's advice to heavily revise the relevant section of the Discussion.

To this end, we have removed the following text from the original manuscript:

"The fact that the cohesin distribution along the chromatin is strongly linked to chromatin looping, as evident by the success of the CCLE model, allows for new insights into in vivo LEF composition and function. For example, recently, two single-molecule studies [37, 38] independently found that Nipbl, which is the mammalian analogue of Mis4, is an obligate component of the loop-extruding human cohesin complex. Ref. [37] also found that cohesin complexes containing Pds5, instead of Nipbl, are unable to extrude loops. On this basis, Ref. [32] proposed that, while Nipbl-containing cohesin is responsible for loop extrusion, Pds5-containing cohesin is responsible for sister chromatid cohesion, neatly separating cohesin's two functions according to composition. However, the success of CCLE in interphase S. pombe, together with the observation that the Mis4 ChIP-seq signal is uncorrelated with the Psc3 ChIP-seq signal (Supplementary Fig. 7) allows us to infer that Mis4 cannot be a component of loop-extruding cohesin in S. pombe. On the other hand, Pds5 is correlated with Psc3 in S. pombe (Supplementary Fig. 7) suggesting that both proteins are involved in loop-extruding cohesin, contradicting a hypothesis that Pds5 is a marker for cohesive cohesin in S. pombe. In contrast to the absence of Mis4-Psc3 correlation in S. pombe, in humans, Nipbl ChIP-seq and Smc1 ChIP-seq are correlated (Supplementary Fig. 7), consistent with Ref. [32]'s hypothesis that Nipbl can be involved in loop-extruding cohesin in humans. However, Ref. [55] showed that human Hi-C contact maps in the absence of Nipbl's binding partner, Mau2 (Ssl3 in S. pombe [56]) show clear TADs, consistent with loop extrusion, albeit with reduced long-range contacts in comparison to wild-type maps, indicating that significant loop extrusion continues in live human cells in the absence of Nipbl-Mau2 complexes. These collected observations suggest the existence of two populations of loop-extruding cohesin complexes in vivo, one that involves Nipbl-Mau2 and one that does not. Both types are present in mammals, but only Mis4-Ssl3-independent loop-extruding cohesin is present in S. pombe."

And we have replaced it by the following text in the revised manuscript (lines 533-568):

"As noted above, the input for our CCLE simulations of chromatin organization in S. pombe, was the ChIP-seq of Psc3, which is a component of the cohesin core complex [75]. Accordingly, Psc3 ChIP-seq represents how the cohesin core complex is distributed along the genome. In S. pombe, the other components of the cohesin core complex are Psm1, Psm3, and Rad21. Because these proteins are components of the cohesin core complex, we expect that the ChIP-seq of any of these proteins would closely match the ChIP-seq of Psc3, and would equally well serve as input for CCLE simulations of S. pombe genome organization. Supplementary Figure 20C confirms significant correlations between Psc3 and Rad21. In light of this observation, we then reason that the CCLE approach offers the opportunity to investigate whether other proteins beyond the cohesin core are constitutive components of the loop extrusion complex during the extrusion process (as opposed to cohesin loading or unloading). To elaborate, if the ChIP-seq of a non-cohesin-core protein is highly correlated with the ChIP-seq of a cohesin core protein, we can infer that the protein in question is associated with the cohesin core and therefore is a likely participant in loop-extruding cohesin, alongside the cohesin core. Conversely, if the ChIP-seq of a putative component of the loop-extruding cohesin complex is uncorrelated with the ChIP-seq of a cohesin core protein, then we can infer that the protein in question is unlikely to be a component of loop-extruding cohesin, or at most is transiently associated with it.

For example, in S. pombe, the ChIP-seq of the cohesin regulatory protein, Pds5 [74], is correlated with the ChIP-seq of Psc3 (Supplementary Fig. 20B) and with that of Rad21 (Supplementary Fig. 20D), suggesting that Pds5 can be involved in loop-extruding cohesin in S. pombe, alongside the cohesin core proteins. Interestingly, this inference concerning fission yeast cohesin subunit, Pds5, stands in contrast to the conclusion from a recent single-molecule study [38] concerning cohesin in vertebrates. Specifically, Reference [38] found that cohesin complexes containing Pds5, instead of Nipbl, are unable to extrude loops.

Additionally, as noted above, in S. pombe the ChIP-seq signal of the cohesin loader, Mis4, is uncorrelated with the Psc3 ChIP-seq signal (Supplementary Fig. 20A), suggesting that Mis4 is, at most, a very transient component of loop-extruding cohesin in S. pombe, consistent with its designation as a "cohesin loader". However, both References [38] and [39] found that Nipbl (counterpart of S. pombe's Mis4) is an obligate component of the loop-extruding human cohesin complex, more than just a mere cohesin loader. Although CCLE has not yet been applied to vertebrates, from a CCLE perspective, the possibility that Nipbl may be required for the loop extrusion process in humans is bolstered by the observation that in humans Nipbl ChIP-seq and Smc1 ChIP-seq show significant correlations (Supplementary Fig. 20G), consistent with Ref. [32]'s hypothesis that Nipbl is involved in loop-extruding cohesin in vertebrates. A recent theoretical model of the molecular mechanism of loop extrusion by cohesin hypothesizes that transient binding by Mis4/Nipbl is essential for permitting directional reversals and therefore for two-sided loop extrusion [41]. Surprisingly, there are significant correlations between Mis4 and Pds5 in S. pombe (Supplementary Fig. 20E), indicating Pds5-Mis4 association, outside of the cohesin core complex."

In response to Referee 2's specific comment that "at least two studies have raised concerns about Nibpl ChIP-seq results", we note (1) that, while Hu et al. Nucleic Acids Res 43:e132 2015 present a general method for calibrating ChIP-seq results, they do not measure Mis4/Nibpl ChIP-seq, nor do they raise any specific concerns about Mis4/Nipbl ChIP-seq, and (2) that (as noted above, in response to Referee 1's comment) while the FRAP analysis presented by Rhodes et al. eLife 6:e30000 indicates that, in HeLa cells, Nipbl has a residence time bound to cohesin of about 50 seconds, nevertheless, as shown in Supplementary Fig. 20G in the revised manuscript, there is a significant cross-correlation between the Nipbl ChIP-seq and Smc1 ChIP-seq in humans, indicating that a transient association between Nipbl and cohesin is detected by ChIP-seq, the referees' concerns notwithstanding.

We thank the referee for pointing out Schwarzer et al. Nature 551:51 2017. However, our interpretation of these data is different than the referee's. As noted in our original manuscript, Nipbl has traditionally been considered to be a cohesin loading factor. If the role of Nipbl was solely to load cohesin, then we would expect that depleting Nipbl would have a major effect on the Hi-C map, because fewer cohesins are loaded onto the chromatin. Figure 2 of Schwarzer et al. Nature 551:51 2017, shows the effect of depleting Nibpl on a vertebrate Hi-C map. Even in this case when Nibpl is absent, this figure (Figure 2 of Schwarzer et al. Nature 551:51 2017) shows that TADs persist, albeit considerably attenuated. According to the authors' own analysis associated with Fig. 2 of their paper, these attenuated TADs correspond to a smaller number of loop-extruding cohesin complexes than in the presence of Nipbl. Since Nipbl is depleted, these loop-extruding cohesins necessarily cannot contain Nipbl. Thus, the data and analysis of Schwarzer et al. Nature 551:51 2017 actually seem consistent with the existence of a population of loop-extruding cohesin complexes that do not contain Nibpl.

Concerning the referee's comment that we cannot be sure whether Pds5 ChIP is associated with extrusive or cohesive cohesin, we note that, as explained in the manuscript, we assume that the cohesive cohesins are uniformly distributed across the genome, and therefore that peaks in the cohesin ChIP-seq are associated with loop-extruding cohesins. The success of CCLE in describing Hi-C maps justifies this assumption a posteriori. Supplementary Figure 20B shows that the ChIP-seq of Pds5 is correlated with the ChIP-seq of Psc3 in S. pombe, that is, that peaks in the ChIP-seq of Psc3, assumed to derive from loop-extruding cohesin, are accompanied by peaks in the ChIP-seq of Pds5. This is the reasoning allowing us to associate Pds5 with loop-extruding cohesin in S. pombe.

1. I suggest that the authors recalculate correlations for Hi-C maps using maps that are rescaled by the P(s) curves. As currently computed, most of the correlation between maps could arise from the characteristic decay of P(s) rather than smaller scale features of the contact maps. This could reduce the surprising observed correlation between distinct genomic regions in pombe (which, problematically, is higher than the observed correlation between simulation and experiment in cervisiae).

Response:

We thank the referee for this advice. Following this advice, throughout the revised manuscript, we have replaced our original calculation of the Pearson correlation coefficient of unscaled Hi-C maps with a calculation of the Pearson correlation coefficient of rescaled Hi-C maps. Since the MPR is formed from ratios of simulated to experimental Hi-C maps, this metric is unchanged by the proposed rescaling.

As explained in the original manuscript, we attribute the lower experiment-simulation correlation in the meiotic budding yeast Hi-C maps to the larger statistical errors of the meiotic budding yeast dataset, which arises because of its higher genomic resolution - all else being equal we can expect 25 times the counts in a 10 kb x10 kb bin as in a 2 kb x 2 kb bin. For the same reason, we expect larger statistical errors in the mitotic budding yeast dataset as well. Lower correlations for noisier data are to be expected in general.

*7. Please explain why the difference between right and left currents at any particular site, (R_n-L_n) / Rn+Ln, should be small. It seems easy to imagine scenarios where this might not be true, such as directional barriers like CTCF or transcribed genes. *

__Response: __

For simplicity, the present version of CCLE sets the site-dependent loop extrusion rates by assuming that the cohesin ChIP-seq signal has equal contributions from left and right anchors. Then, we carry out our simulations which subsequently allow us to examine the simulated left and right currents and their difference at every site. The distributions of normalized left-right difference currents are shown in Supplementary Figures 12B, 13B, and 14D, for interphase S. pombe, meiotic S. cerevisiae, and mitotic S. cerevisiae, respectively. They are all centered at zero with standard deviations of 0.12, 0.16, and 0.33. Thus, it emerges from our simulations that the difference current is indeed generally small.

8. Optional, but I think would greatly improve the manuscript, but can the authors: a) analyze regions of high cohesin occupancy (assumed to be slow extrusion regions) to determine if there's anything special in these regions, such as more transcriptional activity

__Response: __

In response to Referee 1's similar comment, we have calculated the correlation between the locations of convergent genes and cohesin ChIP-seq. Supplementary Figure 18A in the revised manuscript shows that for interphase S. pombe no correlations are evident, whereas for both of meiotic and mitotic S. cerevisiae, there are significant correlations between these two quantities (Supplementary Fig. 17).

*b) apply this methodology to vertebrate cell data *

__Response: __

The application of CCLE to vertebrate data is outside the scope of this paper which, as we have emphasized, has the goal of developing a model that can be robustly applied to non-vertebrate eukaryotic genomes. Nevertheless, CCLE is, in principle, applicable to all organisms in which loop extrusion by SMC complexes is the primary mechanism for chromatin spatial organization.

1. *A Github link is provided but the code is not currently available. *

__Response: __

The code is now available.

Minor Comments:

1. Please state the simulated LEF lifetime, since the statement in the methods that 15000 timesteps are needed for equilibration of the LEF model is otherwise not meaningful. Additionally, please note that backbone length is not necessarily a good measure of steady state, since the backbone can be compacted to its steady-state value while the loop distribution continues to evolve toward its steady state.

__Response: __

The terminology "timesteps" used in the original manuscript in fact should mean "the number of LEF events performed" in the simulation. Therefore, we have changed the terminology from "timesteps" to "LEF events".

The choice of 15000 LEF events is empirically determined to ensure that loop extrusion steady state is achieved, for the range of parameters considered. To address the referee's concern regarding the uncertainty of achieving steady state after 15000 LEF events, we compared two loop size distributions: each distribution encompasses 1000 data points, equally separated in time, one between LEF event 15000 and 35000, and the other between LEF event 80000 and 100000. The two distributions are within-errors identical, suggesting that the loop extrusion steady state is well achieved within 15000 LEF events.

2. How important is the cohesive cohesin parameter in the model, e.g., how good are fits with \rho_c = 0?

__Response: __

As stated in the original manuscript, the errors on \rho_c on the order of 10%-20% (for S. pombe). Thus, fits with \rho_c=0 are significantly poorer than with the best-fit values of \rho_c.

*3. A nice (but non-essential) supplemental visualization might be to show a scatter of sim cohesin occupancy vs. experiment ChIP. *

__Response: __

We have chosen not to do this, because we judge that the manuscript is already long enough. Figures 3A, 5D, and 6C already compare the experimental and simulated ChIP-seq, and these figures already contain more information than the figures proposed by the referee.

1. *A similar calculation of Hi-C contacts based on simulated loop extruder positions using the Gaussian chain model was previously presented in Banigan et al. eLife 9:e53558 2020, which should be cited. *

__Response: __

We thank the referee for pointing out this citation. We have added it to the revised manuscript.

1. It is stated that simulation agreement with experiments for cerevisiae is worse in part due to variability in the experiments, with MPR and Pearson numbers for cerevisiae replicates computed for reference. But these numbers are difficult to interpret without, for example, similar numbers for duplicate pombe experiments. Again, these numbers should be generated using Hi-C maps scaled by P(s), especially in case there are systematic errors in one replicate vs. another.

__Response: __

As noted above, throughout the revised manuscript, we now give the Pearson correlation coefficients of scaled-by-P(s) Hi-C maps.

1. *In the model section, it is stated that LEF binding probabilities are uniformly distributed. Did the authors mean the probability is uniform across the genome or that the probability at each site is a uniformly distributed random number? Please clarify, and if the latter, explain why this unconventional assumption was made. *

__Response: __

It is the former. We have modified the manuscript to clarify that LEFs "initially bind to empty, adjacent chromatin lattice sites with a binding probability, that is uniformly distributed across the genome." (lines 587-588).

*7. Supplement p4 line 86 - what is meant by "processivity of loops extruded by isolated LEFs"? "size of loops extruded by..." or "processivity of isolated LEFs"? *

__Response: __

Here "processivity of isolated LEFs" is defined as the processivity of one LEF without the interference (blocking) from other LEFs. We have changed "processivity of loops extruded by isolated LEFs" to "processivity of isolated LEFs" for clarity.

1. The use of parentheticals in the caption to Table 2 is a little confusing; adding a few extra words would help.

__Response: __

In the revised manuscript, we have added an additional sentence, and have removed the offending parentheses.

1. *Page 12 sentence line 315-318 is difficult to understand. The barrier parameter is apparently something from ref 47 not previously described in the manuscript. *

__Response: __

In the revised manuscript, we have removed mention of the "barrier parameter" from the discussion.

1. *Statement on p14 line 393-4 is false: prior LEF models have not been limited to vertebrates, and the authors have cited some of them here. There are also non-vertebrate examples with extrusion barriers: genes as boundaries to condensin in bacteria (Brandao et al. PNAS 116:20489 2019) and MCM complexes as boundaries to cohesin in yeast (Dequeker et al. Nature 606:197 2022). *

__Response: __

In fact, Dequeker et al. Nature 606:197 2022 concerns the role of MCM complexes in blocking cohesin loop extrusion in mouse zygotes. Mouse is a vertebrate. The sole aspect of this paper, that is associated with yeast, is the observation of cohesin blocking by the yeast MCM bound to the ARS1 replication origin site, which is inserted on a piece of lambda phage DNA. No yeast genome is used in the experiment. Therefore, the referee is mistaken to suggest that this paper models yeast genome organization.

We thank the referee for pointing out Brandao et al. PNAS 116:20489 2019, which includes the development of a tour-de-force model of condensin-based loop extrusion in the prokaryote, Bacillus subtilis, in the presence of gene barriers to loop extrusion. To acknowledge this paper, we have changed the objectionable sentence to now read (lines 571-575):

"... prior LEF models have been overwhelmingly limited to vertebrates, which express CTCF and where CTCF is the principal boundary element. Two exceptions, in which the LEF model was applied to non-vertebrates, are Ref. [49], discussed above, and Ref. [76] (Brandao et al.), which models the Hi-C map of the prokaryote, Bacillus subtilis, on the basis of condensin loop extrusion with gene-dependent barriers."

*Referees cross-commenting *

I agree with the comments of Reviewer 1, which are interesting and important points that should be addressed.

*Reviewer #2 (Significance (Required)):

Analytically approaching extrusion by treating cohesin translocation as a conserved current is an interesting approach to modeling and analysis of extrusion-based chromatin organization. It appears to work well as a descriptive model. But I think there are major questions concerning the mechanistic value of this model, possible applications of the model, the provided interpretations of the model and experiments, and the limitations of the model under the current assumptions. I am unconvinced that this analysis specifically is sufficient to demonstrate that extrusion is the primary organizer of chromatin on these scales; moreover, the need to demonstrate this is questionable, as extrusion is widely accepted, even if not universally so. It is also unclear that the minimal approach of the CCLE necessarily offers an improved physical basis for modeling extrusion, as compared to previous efforts such as ref 47, as claimed by the authors. There are also questions about significance due to possible limitations of the model (detailed above). Applying the CCLE model to identify barriers would be interesting, but is not attempted. Overall, the work presents a reasonable analytical model and numerical method, but until the major comments above are addressed and some reasonable application or mechanistic value or interpretation is presented, the overall significance is somewhat limited.*

__Response: __

We agree with the referee that analytically approaching extrusion by treating cohesin translocation as a conserved current is an interesting approach to modeling and analysis of extrusion-based chromatin organization. We also agree with the referee that it works well as a descriptive model (of Hi-C maps in S. pombe and S. cerevisiae). Obviously, we disagree with the referee's other comments. For us, being able to describe the different-appearing Hi-C maps of interphase S. pombe (Fig. 1 and Supplementary Figures 1-9), meiotic S. cerevisiae (Fig. 5) and mitotic S. cerevisiae (Fig. 6), all with a common model with just a few fitting parameters that differ between these examples, is significant and novel. The reviewer prematurely ignores the fact that there are still debates about whether "diffusion-capture"-like model is the more dominant mechanism that shape chromatin spatial organization at the TAD-scale. Many works have argued that such models could describe TAD-scale chromatin organization, as cited in the revised manuscript (Refs. [11, 14, 15, 17, 20, 22-24, 55]). However, in contrast to the poor description of the Hi-C map using diffusion capture model (as demonstrated in the revised manuscript and Supplementary Fig. 15), the excellent experiment-simulation agreement achieved by CCLE provides compelling evidence that cohesin-based loop extrusion is indeed the primary organizer of TAD-scale chromatin.

Importantly, CCLE provides a theoretical base for how loop extrusion models can be generalized and applied to organisms without known loop extrusion barriers. Our model also highlights that (and provides means to account for) distributed barriers that impede but do not strictly block LEFs could also impact chromatin configurations. This case might be of importance to organisms with CTCF motifs that infrequently coincide with TAD boundaries, for instance, in the case of Drosophila melanogaster. Moreover, CCLE promises theoretical descriptions of the Hi-C maps of other non-vertebrates in the future, extending the quantitative application of the LEF model across the tree of life. This too would be highly significant if successful.

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Referee #2

Evidence, reproducibility and clarity

Summary:

Yuan et al. report on their development of an analytical model ("CCLE") for loop extrusion with genomic-position-dependent speed, with the idea of accounting for barriers to loop extrusion. They write down master equations for the probabilities of cohesin occupancy at each genomic site and obtain approximate steady-state solutions. Probabilities are governed by cohesin translocation, loading, and unloading. Using ChIP-seq data as an experimental measurement of these probabilities, they numerically fit the model parameters, among which are extruder density and processivity. Gillespie simulations with these parameters combined with a 3D Gaussian polymer model were integrated to generate simulated Hi-C maps and cohesin ChIP-seq tracks, which show generally good agreement with the experimental data. The authors argue that their modeling provides evidence that loop extrusion is the primary mechanism of chromatin organization on ~10-100 kb scales in S. pombe and S. cerevisiae.

Major comments:

1. I am unconvinced that this analysis specifically is sufficient to demonstrate that extrusion is the primary organizer of chromatin on these scales; moreover, the need to demonstrate this is questionable, as extrusion is widely accepted, even if not universally so. How is the agreement of CCLE with experiments more demonstrative of loop extrusion than previous modeling? Relatedly, similar best fit values for S. pombe and S. cerevisiae might not point to a mechanistic conclusion (same "underlying mechanism" of loop extrusion), but rather to similar properties for loop-extruding cohesins in the two species. As an alternative, could a model with variable binding probability given by ChIP-seq and an exponential loop-size distribution work equally well? The stated lack of a dependence on extrusion timescale suggests that a static looping model might succeed. If not, why not?
2. I do not understand how the loop extrusion residence time drops out. As I understand it, Eq 9 converts ChIP-seq to lattice site probability (involving N_{LEF}, which is related to \rho, and \rho_c). Then, Eqs. 3-4 derive site velocities V_n and U_n if we choose rho, L, and \tau, with the latter being the residence time. This parameter is not specified anywhere and is claimed to be unimportant. It may be true that the choice of timescale is arbitrary in this procedure, but can the authors please clarify?
3. The assumptions in the solution and application of the CCLE model are potentially constraining to a limited number of scenarios. In particular the authors specify that current due to binding/unbinding, A_n - D_n, is small. This assumption could be problematic near loading sites (centromeres, enhancers in higher eukaryotes, etc.) (where current might be dominated by A_n and V_n), unloading sites (D_n and V_{n-1}), or strong boundaries (D_n and V_{n-1}). The latter scenario is particularly concerning because the manuscript seems to be concerned with the presence of unidentified boundaries. This is partially mitigated by the fact that the model seems to work well in the chosen examples, but the authors should discuss the limitations due to their assumptions and/or possible methods to get around these limitations.
4. Related to the above concern, low cohesin occupancy is interpreted as a fast extrusion region and high cohesin occupancy is interpreted as a slow region. But this might not be true near cohesin loading and unloading sites.
5. The mechanistic insight attempted in the discussion, specifically with regard to Mis4/Scc2/NIPBL and Pds5, is problematic. First, it is not clear how the discussion of Nipbl and Pds5 is connected to the CCLE method; the justification is that CCLE shows cohesin distribution is linked to cohesin looping, which is already a questionable statement (point 1) and doesn't really explain how the model offers new insight into existing Nipbl and Pds5 data.

Furthermore, I believe that the conclusions drawn on this point are flawed, or at least, stated with too much confidence. The authors raise the curious point that Nipbl ChIP-seq does not correlate well with cohesin ChIP-seq, and use this as evidence that Nipbl is not a part of the loop-extruding complex in S. pombe, and it is not essential in humans. Aside from the molecular evidence in human Nipbl/cohesin (acknowledged by authors), there are other reasons to doubt this conclusion. First, depletion of Nipbl (rather than binding partner Mau2 as in ref 55) in mouse cells strongly inhibits TAD formation (Schwarzer et al. Nature 551:51 2017). Second, at least two studies have raised concerns about Nibpl ChIP-seq results: 1) Hu et al. Nucleic Acids Res 43:e132 2015, which shows that uncalibrated ChIP-seq can obscure the signal of protein localization throughout the genome due to the inability to distinguish from background and 2) Rhodes et al. eLife 6:e30000, which uses FRAP to show that Nipbl binds and unbinds to cohesin rapidly in human cells, which could go undetected in ChIP-seq, especially when uncalibrated. It has not been shown that these dynamics are present in yeast, but there is no reason to rule it out yet.

Similar types of critiques could be applied to the discussion of Pds5. There is cross-correlation between Psc3 and Pds5 in S. pombe, but the authors are unable to account for whether Pds5 binding is transient and/or necessary to loop extrusion itself or, more importantly, whether Pds5 ChIP is associated with extrusive or cohesive cohesins; cross-correlation peaks at about 0.6, but note that by the authors own estimates, cohesive cohesins are approximately half of all cohesins in S. pombe (Table 3).

Due to the above issues, I suggest that the authors heavily revise this discussion to better reflect the current experimental understanding and the limited ability to draw such conclusions based on the current CCLE model. 6. I suggest that the authors recalculate correlations for Hi-C maps using maps that are rescaled by the P(s) curves. As currently computed, most of the correlation between maps could arise from the characteristic decay of P(s) rather than smaller scale features of the contact maps. This could reduce the surprising observed correlation between distinct genomic regions in pombe (which, problematically, is higher than the observed correlation between simulation and experiment in cervisiae). 7. Please explain why the difference between right and left currents at any particular site, (R_n-L_n) / Rn+Ln, should be small. It seems easy to imagine scenarios where this might not be true, such as directional barriers like CTCF or transcribed genes. 8. Optional, but I think would greatly improve the manuscript, but can the authors: a) analyze regions of high cohesin occupancy (assumed to be slow extrusion regions) to determine if there's anything special in these regions, such as more transcriptional activity

b) apply this methodology to vertebrate cell data 9. A Github link is provided but the code is not currently available.

Minor Comments:

1. Please state the simulated LEF lifetime, since the statement in the methods that 15000 timesteps are needed for equilibration of the LEF model is otherwise not meaningful. Additionally, please note that backbone length is not necessarily a good measure of steady state, since the backbone can be compacted to its steady-state value while the loop distribution continues to evolve toward its steady state.
2. How important is the cohesive cohesin parameter in the model, e.g., how good are fits with \rho_c = 0?
3. A nice (but non-essential) supplemental visualization might be to show a scatter of sim cohesin occupancy vs. experiment ChIP.
4. A similar calculation of Hi-C contacts based on simulated loop extruder positions using the Gaussian chain model was previously presented in Banigan et al. eLife 9:e53558 2020, which should be cited.
5. It is stated that simulation agreement with experiments for cerevisiae is worse in part due to variability in the experiments, with MPR and Pearson numbers for cerevisiae replicates computed for reference. But these numbers are difficult to interpret without, for example, similar numbers for duplicate pombe experiments. Again, these numbers should be generated using Hi-C maps scaled by P(s), especially in case there are systematic errors in one replicate vs. another.
6. In the model section, it is stated that LEF binding probabilities are uniformly distributed. Did the authors mean the probability is uniform across the genome or that the probability at each site is a uniformly distributed random number? Please clarify, and if the latter, explain why this unconventional assumption was made.
7. Supplement p4 line 86 - what is meant by "processivity of loops extruded by isolated LEFs"? "size of loops extruded by..." or "processivity of isolated LEFs"?
8. The use of parentheticals in the caption to Table 2 is a little confusing; adding a few extra words would help.
9. Page 12 sentence line 315-318 is difficult to understand. The barrier parameter is apparently something from ref 47 not previously described in the manuscript.
10. Statement on p14 line 393-4 is false: prior LEF models have not been limited to vertebrates, and the authors have cited some of them here. There are also non-vertebrate examples with extrusion barriers: genes as boundaries to condensin in bacteria (Brandao et al. PNAS 116:20489 2019) and MCM complexes as boundaries to cohesin in yeast (Dequeker et al. Nature 606:197 2022).

Referees cross-commenting

I agree with the comments of Reviewer 1, which are interesting and important points that should be addressed.

Significance

Analytically approaching extrusion by treating cohesin translocation as a conserved current is an interesting approach to modeling and analysis of extrusion-based chromatin organization. It appears to work well as a descriptive model. But I think there are major questions concerning the mechanistic value of this model, possible applications of the model, the provided interpretations of the model and experiments, and the limitations of the model under the current assumptions. I am unconvinced that this analysis specifically is sufficient to demonstrate that extrusion is the primary organizer of chromatin on these scales; moreover, the need to demonstrate this is questionable, as extrusion is widely accepted, even if not universally so. It is also unclear that the minimal approach of the CCLE necessarily offers an improved physical basis for modeling extrusion, as compared to previous efforts such as ref 47, as claimed by the authors. There are also questions about significance due to possible limitations of the model (detailed above). Applying the CCLE model to identify barriers would be interesting, but is not attempted. Overall, the work presents a reasonable analytical model and numerical method, but until the major comments above are addressed and some reasonable application or mechanistic value or interpretation is presented, the overall significance is somewhat limited.

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Hmm! Sounds like a plan

Author response:

eLife assessment 

This important study provides evidence for a combination of the latest generation of Oxford Nanopore Technology long reads with state-of-the art variant callers enabling bacterial variant discovery at accuracy that matches or exceeds the current "gold standard" with short reads. The evidence supporting the claims of the authors is convincing, although the inclusion of a larger number of reference genomes would further strengthen the study. The work will be of interest to anyone performing sequencing for outbreak investigations, bacterial epidemiology, or similar studies. 

We thank the editor and reviewers for the accurate summary and positive assessment. We address the comment about increasing the number of reference genomes in the response to reviewer 2.

Public Reviews: 

Reviewer #1 (Public Review): 

Summary: 

The authors assess the accuracy of short variant calling (SNPs and indels) in bacterial genomes using Oxford Nanopore reads generated on R10.4 flow cells from a very similar genome (99.5% ANI), examining the impact of variant caller choice (three traditional variant callers: bcftools, freebayes, and longshot, and three deep learning based variant callers: clair3, deep variant, and nano caller), base calling model (fast, hac and sup) and read depth (using both simplex and duplex reads). 

Strengths: 

Given the stated goal (analysis of variant calling for reads drawn from genomes very similar to the reference), the analysis is largely complete and results are compelling. The authors make the code and data used in their analysis available for re-use using current best practices (a computational workflow and data archived in INSDC databases or Zenodo as appropriate). 

Weaknesses: 

While the medaka variant caller is now deprecated for diploid calling, it is still widely used for haploid variant calling and should at least be mentioned (even if the mention is only to explain its exclusion from the analysis). 

We agree that this would be an informative addition to the study and will add it to the benchmarking.

Appraisal: 

The experiments the authors engaged in are well structured and the results are convincing. I expect that these results will be incorporated into "best practice" bacterial variant calling workflows in the future. 

Thank you for the positive appraisal.

Reviewer #2 (Public Review): 

Summary: 

Hall et al describe the superiority of ONT sequencing and deep learning-based variant callers to deliver higher SNP and Indel accuracy compared to previous gold-standard Illumina short-read sequencing. Furthermore, they provide recommendations for read sequencing depth and computational requirements when performing variant calling. 

Strengths: 

The study describes compelling data showing ONT superiority when using deep learning-based variant callers, such as Clair3, compared to Illumina sequencing. This challenges the paradigm that Illumina sequencing is the gold standard for variant calling in bacterial genomes. The authors provide evidence that homopolymeric regions, a systematic and problematic issue with ONT data, are no longer a concern in ONT sequencing. 

Weaknesses: 

(1) The inclusion of a larger number of reference genomes would have strengthened the study to accommodate larger variability (a limitation mentioned by the authors). 

Our strategic selection of 14 genomes—spanning a variety of bacterial genera and species, diverse GC content, and both gram-negative and gram-positive species (including M. tuberculosis, which is neither)—was designed to robustly address potential variability in our results. Moreover, all our genome assemblies underwent rigorous manual inspection as the quality of the true genome sequences is the foundation this research is built upon. Given this, the fundamental conclusions regarding the accuracy of variant calls would likely remain unchanged with the addition of more genomes.  However, we do acknowledge that a substantially larger sample size, which is beyond the scope of this study, would enable more fine-grained analysis of species differences in error rates.

(2) In Figure 2, there are clearly one or two samples that perform worse than others in all combinations (are always below the box plots). No information about species-specific variant calls is provided by the authors but one would like to know if those are recurrently associated with one or two species. Species-specific recommendations could also help the scientific community to choose the best sequencing/variant calling approaches.

Thank you for highlighting this observation. The precision, recall, and F1 scores for each sample and condition can be found in Supplementary Table S4. We will investigate the samples that consistently perform below expectation to determine if this is associated with specific species, which may necessitate tailored recommendations for those species. Additionally, we will produce a species-segregated version of Figure 2 for a clearer interpretation and will place it in the supplementary materials.

(3) The authors support that a read depth of 10x is sufficient to achieve variant calls that match or exceed Illumina sequencing. However, the standard here should be the optimal discriminatory power for clinical and public health utility (namely outbreak analysis). In such scenarios, the highest discriminatory power is always desirable and as such an F1 score, Recall and Precision that is as close to 100% as possible should be maintained (which changes the minimum read sequencing depth to at least 25x, which is the inflection point).

We agree that the highest discriminatory power is always desirable for clinical or public health applications. In which case, 25x is probably a better minimum recommendation. However, we are also aware that there are resource-limited settings where parity with Illumina is sufficient. In these cases, 10x depth from ONT would provide sufficient data.

The manuscript currently emphasises the latter scenario, but we will revise the text to clearly recommend 25x depth as a conservative aim in settings where resources are not a constraint, ensuring the highest possible discriminatory power for applications like outbreak analysis.

(4) The sequencing of the samples was not performed with the same Illumina and ONT method/equipment, which could have introduced specific equipment/preparation artefacts that were not considered in the study. See for example https://academic.oup.com/nargab/article/3/1/lqab019/6193612. 

To our knowledge, there is no evidence that sequencing on different ONT machines or barcoding kits leads to a difference in read characteristics or accuracy. To ensure consistency and minimise potential variability, we used the same ONT flowcells for all samples and performed basecalling on the same Nvidia A100 GPU. We will update the methods to emphasise this.

For Illumina and ONT, the exact machines used for which samples will be added as a supplementary table. We will also add a comment about possible Illumina error rate differences in the ‘Limitations’ section of the Discussion.

In summary, while there may be specific equipment or preparation artifacts to consider, we took steps to minimise these effects and maintain consistency across our sequencing methods.

Reviewer #3 (Public Review): 

Hall et al. benchmarked different variant calling methods on Nanopore reads of bacterial samples and compared the performance of Nanopore to short reads produced with Illumina sequencing. To establish a common ground for comparison, the authors first generated a variant truth set for each sample and then projected this set to the reference sequence of the sample to obtain a mutated reference. Subsequently, Hall et al. called SNPs and small indels using commonly used deep learning and conventional variant callers and compared the precision and accuracy from reads produced with simplex and duplex Nanopore sequencing to Illumina data. The authors did not investigate large structural variation, which is a major limitation of the current manuscript. It will be very interesting to see a follow-up study covering this much more challenging type of variation. 

We fully agree that investigating structural variations (SVs) would be a very interesting and important follow-up. Identifying and generating ground truth SVs is a nontrivial task and we feel it deserves its own space and study. We hope to explore this in the future.

In their comprehensive comparison of SNPs and small indels, the authors observed superior performance of deep learning over conventional variant callers when Nanopore reads were basecalled with the most accurate (but also computationally very expensive) model, even exceeding Illumina in some cases. Not surprisingly, Nanopore underperformed compared to Illumina when basecalled with the fastest (but computationally much less demanding) method with the lowest accuracy. The authors then investigated the surprisingly higher performance of Nanopore data in some cases and identified lower recall with Illumina short read data, particularly from repetitive regions and regions with high variant density, as the driver. Combining the most accurate Nanopore basecalling method with a deep learning variant caller resulted in low error rates in homopolymer regions, similar to Illumina data. This is remarkable, as homopolymer regions are (or, were) traditionally challenging for Nanopore sequencing. 

Lastly, Hall et al. provided useful information on the required Nanopore read depth, which is surprisingly low, and the computational resources for variant calling with deep learning callers. With that, the authors established a new state-of-the-art for Nanopore-only variant, calling on bacterial sequencing data. Most likely these findings will be transferred to other organisms as well or at least provide a proof-of-concept that can be built upon. 

As the authors mention multiple times throughout the manuscript, Nanopore can provide sequencing data in nearly real-time and in remote regions, therefore opening up a ton of new possibilities, for example for infectious disease surveillance. 

However, the high-performing variant calling method as established in this study requires the computationally very expensive sup and/or duplex Nanopore basecalling, whereas the least computationally demanding method underperforms. Here, the manuscript would greatly benefit from extending the last section on computational requirements, as the authors determine the resources for the variant calling but do not cover the entire picture. This could even be misleading for less experienced researchers who want to perform bacterial sequencing at high performance but with low resources. The authors mention it in the discussion but do not make clear enough that the described computational resources are probably largely insufficient to perform the high-accuracy basecalling required. 

We have provided runtime benchmarks for basecalling in Supplementary Figure S16 and detailed these times in Supplementary Table S7. In addition, we state in the Results section (P10 L228-230) “Though we do note that if the person performing the variant calling has received the raw (pod5) ONT data, basecalling also needs to be accounted for, as depending on how much sequencing was done, this step can also be resource-intensive.”

Even with super-accuracy basecalling considered, our analysis shows that variant calling remains the most resource-intensive step for Clair3, DeepVariant, FreeBayes, and NanoCaller. Therefore, the statement “the described computational resources are probably largely insufficient to perform the high-accuracy basecalling required”, is incorrect. However, we will endeavour to make the basecalling component and considerations more prominent in the Results and Discussion.

Reviewer #1 (Public Review):

Summary:

The authors assess the accuracy of short variant calling (SNPs and indels) in bacterial genomes using Oxford Nanopore reads generated on R10.4 flow cells from a very similar genome (99.5% ANI), examining the impact of variant caller choice (three traditional variant callers: bcftools, freebayes, and longshot, and three deep learning based variant callers: clair3, deep variant, and nano caller), base calling model (fast, hac and sup) and read depth (using both simplex and duplex reads).

Strengths:

Given the stated goal (analysis of variant calling for reads drawn from genomes very similar to the reference), the analysis is largely complete and results are compelling. The authors make the code and data used in their analysis available for re-use using current best practices (a computational workflow and data archived in INSDC databases or Zenodo as appropriate).

Weaknesses:

While the medaka variant caller is now deprecated for diploid calling, it is still widely used for haploid variant calling and should at least be mentioned (even if the mention is only to explain its exclusion from the analysis).

Appraisal:

The experiments the authors engaged in are well structured and the results are convincing. I expect that these results will be incorporated into "best practice" bacterial variant calling workflows in the future.

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

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Reply to the reviewers

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

I have trialled the package on my lab's data and it works as advertised. It was straightforward to use and did not require any special training. I am confident this is a tool that will be approachable even to users with limited computational experience. The use of artificial data to validate the approach - and to provide clear limits on applicability - is particularly helpful.

The main limitation of the tool is that it requires the user to manually select regions. This somewhat limits the generalisability and is also more subjective - users can easily choose "nice" regions that better match with their hypothesis, rather than quantifying the data in an unbiased manner. However, given the inherent challenges in quantifying biological data, such problems are not easily circumventable.

*

* I have some comments to clarify the manuscript:

1. A "straightforward installation" is mentioned. Given this is a Method paper, the means of installation should be clearly laid out.*

__This sentence is now modified. In the revised manuscript we now describe how to install the toolset and we give the link to the toolset website if further information is needed. __On this website, we provide a full video tutorial and a user manual. The user manual is provided as a supplementary material of the manuscript.

* It would be helpful if there was an option to generate an output with the regions analysed (i.e., a JPG image with the data and the drawn line(s) on top). There are two reasons for this: i) A major problem with user-driven quantification is accidental double counting of regions (e.g., a user quantifies a part of an image and then later quantifies the same region). ii) Allows other users to independently verify measurements at a later time.*

We agree that it is helpful to save the analyzed regions. To answer this comment and the other two reviewers' comments pointing at a similar feature, we have now included an automatic saving of the regions of interest. The user will be able to reopen saved regions of interest using a new function we included in the new version of PatternJ.

* 3. Related to the above point, it is highlighted that each time point would need to be analysed separately (line 361-362). It seems like it should be relatively straightforward to allow a function where the analysis line can be mapped onto the next time point. The user could then adjust slightly for changes in position, but still be starting from near the previous timepoint. Given how prevalent timelapse imaging is, this seems like (or something similar) a clear benefit to add to the software.*

We agree that the analysis of time series images can be a useful addition. We have added the analysis of time-lapse series in the new version of PatternJ. The principles behind the analysis of time-lapse series and an example of such analysis are provided in Figure 1 - figure supplement 3 and Figure 5, with accompanying text lines 140-153 and 360-372. The analysis includes a semi-automated selection of regions of interest, which will make the analysis of such sequences more straightforward than having to draw a selection on each image of the series. The user is required to draw at least two regions of interest in two different frames, and the algorithm will automatically generate regions of interest in frames in which selections were not drawn. The algorithm generates the analysis immediately after selections are drawn by the user, which includes the tracking of the reference channel.

* Line 134-135. The level of accuracy of the searching should be clarified here. This is discussed later in the manuscript, but it would be helpful to give readers an idea at this point what level of tolerance the software has to noise and aperiodicity.

*

We agree with the reviewer that a clarification of this part of the algorithm will help the user better understand the manuscript.__ We have modified the sentence to clarify the range of search used and the resulting limits in aperiodicity (now lines 176-181). __Regarding the tolerance to noise, it is difficult to estimate it a priori from the choice made at the algorithm stage, so we prefer to leave it to the validation part of the manuscript. We hope this solution satisfies the reviewer and future users.

*

**Referees cross-commenting**

I think the other reviewer comments are very pertinent. The authors have a fair bit to do, but they are reasonable requests. So, they should be encouraged to do the revisions fully so that the final software tool is as useful as possible.

Reviewer #1 (Significance (Required)):

Developing software tools for quantifying biological data that are approachable for a wide range of users remains a longstanding challenge. This challenge is due to: (1) the inherent problem of variability in biological systems; (2) the complexity of defining clearly quantifiable measurables; and (3) the broad spread of computational skills amongst likely users of such software.

In this work, Blin et al., develop a simple plugin for ImageJ designed to quickly and easily quantify regular repeating units within biological systems - e.g., muscle fibre structure. They clearly and fairly discuss existing tools, with their pros and cons. The motivation for PatternJ is properly justified (which is sadly not always the case with such software tools).

Overall, the paper is well written and accessible. The tool has limitations but it is clearly useful and easy to use. Therefore, this work is publishable with only minor corrections.

*We thank the reviewer for the positive evaluation of PatternJ and for pointing out its accessibility to the users.

*

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

# Summary

The authors present an ImageJ Macro GUI tool set for the quantification of one-dimensional repeated patterns that are commonly occurring in microscopy images of muscles.

# Major comments

In our view the article and also software could be improved in terms of defining the scope of its applicability and user-ship. In many parts the article and software suggest that general biological patterns can be analysed, but then in other parts very specific muscle actin wordings are used. We are pointing this out in the "Minor comments" sections below. We feel that the authors could improve their work by making a clear choice here. One option would be to clearly limit the scope of the tool to the analysis of actin structures in muscles. In this case we would recommend to also rename the tool, e.g. MusclePatternJ. The other option would be to make the tool about the generic analysis of one-dimensional patterns, maybe calling the tool LinePatternJ. In the latter case we would recommend to remove all actin specific wordings from the macro tool set and also the article should be in parts slightly re-written.

*

We agree with the reviewer that our initial manuscript used a mix of general and muscle-oriented vocabulary, which could make the use of PatternJ confusing especially outside of the muscle field. To make PatternJ useful for the largest community, we corrected the manuscript and the PatternJ toolset to provide the general vocabulary needed to make it understandable for every biologist. We modified the manuscript accordingly.

* # Minor/detailed comments

# Software

We recommend considering the following suggestions for improving the software.

## File and folder selection dialogs

In general, clicking on many of the buttons just opens up a file-browser dialog without any further information. For novel users it is not clear what the tool expects one to select here. It would be very good if the software could be rewritten such that there are always clear instructions displayed about which file or folder one should open for the different buttons.*

We experienced with the current version of macOS that the file-browser dialog does not display any message; we suspect this is the issue raised by the reviewer. This is a known issue of Fiji on Mac and all applications on Mac since 2016. We provided guidelines in the user manual and on the tutorial video to correct this issue by changing a parameter in Fiji. Given the issues the reviewer had accessing the material on the PatternJ website, which we apologize for, we understand the issue raised. We added an extra warning on the PatternJ website to point at this problem and its solution. Additionally, we have limited the file-browser dialog appearance to what we thought was strictly necessary. Thus, the user will experience fewer prompts, speeding up the analysis.

*

## Extract button

The tool asks one to specify things like whether selections are drawn "M-line-to-M-line"; for users that are not experts in muscle morphology this is not understandable. It would be great to find more generally applicable formulations. *

We agree that this muscle-oriented vocabulary can make the use of PatternJ confusing. We have now corrected the user interface to provide both general and muscle-specific vocabulary ("center-to-center or edge-to-edge (M-line-to-M-line or Z-disc-to-Z-disc)").*

## Manual selection accuracy

The 1st step of the analysis is always to start from a user hand-drawn profile across intensity patterns in the image. However, this step can cause inaccuracy that varies with the shape and curve of the line profile drawn. If not strictly perpendicular to for example the M line patterns, the distance between intensity peaks will be different. This will be more problematic when dealing with non-straight and parallelly poised features in the image. If the structure is bended with a curve, the line drawn over it also needs to reproduce this curve, to precisely capture the intensity pattern. I found this limits the reproducibility and easy-usability of the software.*

We understand the concern of the reviewer. On curved selections this will be an issue that is difficult to solve, especially on "S" curved or more complex selections. The user will have to be very careful in these situations. On non-curved samples, the issue may be concerning at first sight, but the errors go with the inverse of cosine and are therefore rather low. For example, if the user creates a selection off by 5 degrees, which is visually obvious, lengths will be affected by an increase of only 0.38%. The point raised by the reviewer is important to discuss, and we therefore added a paragraph to comment on the choice of selection (lines 94-98) and a supplementary figure to help make it clear (Figure 1 - figure supplement 1).*

### Reproducibility

Since the line profile drawn on the image is the first step and very essential to the entire process, it should be considered to save together with the analysis result. For example, as ImageJ ROI or ROIset files that can be re-imported, correctly positioned, and visualized in the measured images. This would greatly improve the reproducibility of the proposed workflow. In the manuscript, only the extracted features are being saved (because the save button is also just asking for a folder containing images, so I cannot verify its functionality). *

We agree that this is a very useful and important feature. We have added ROI automatic saving. Additionally, we now provide a simplified import function of all ROIs generated with PatternJ and the automated extraction and analysis of the list of ROIs. This can be done from ROIs generated previously in PatternJ or with ROIs generated from other ImageJ/Fiji algorithms. These new features are described in the manuscript in lines 120-121 and 130-132.

*

## ? button

It would be great if that button would open up some usage instructions.

*

We agree with the reviewer that the "?" button can be used in a better way. We have replaced this button with a Help menu, including a simple tutorial showing a series of images detailing the steps to follow by the user, a link to the user website, and a link to our video tutorial.

* ## Easy improvement of workflow

I would suggest a reasonable expansion of the current workflow, by fitting and displaying 2D lines to the band or line structure in the image, that form the "patterns" the author aims to address. Thus, it extracts geometry models from the image, and the inter-line distance, and even the curve formed by these sets of lines can be further analyzed and studied. These fitted 2D lines can be also well integrated into ImageJ as Line ROI, and thus be saved, imported back, and checked or being further modified. I think this can largely increase the usefulness and reproducibility of the software.

*

We hope that we understood this comment correctly. We had sent a clarification request to the editor, but unfortunately did not receive an answer within the requested 4 weeks of this revision. We understood the following: instead of using our 1D approach, in which we extract positions from a profile, the reviewer suggests extracting the positions of features not as a single point, but as a series of coordinates defining its shape. If this is the case, this is a major modification of the tool that is beyond the scope of PatternJ. We believe that keeping our tool simple, makes it robust. This is the major strength of PatternJ. Local fitting will not use line average for instance, which would make the tool less reliable.

* # Manuscript

We recommend considering the following suggestions for improving the manuscript. Abstract: The abstract suggests that general patterns can be quantified, however the actual tool quantifies specific subtypes of one-dimensional patterns. We recommend adapting the abstract accordingly.

*

We modified the abstract to make this point clearer.

* Line 58: Gray-level co-occurrence matrix (GLCM) based feature extraction and analysis approach is not mentioned nor compared. At least there's a relatively recent study on Sarcomeres structure based on GLCM feature extraction: https://github.com/steinjm/SotaTool with publication: *https://doi.org/10.1002/cpz1.462

• *

We thank the reviewer for making us aware of this publication. We cite it now and have added it to our comparison of available approaches.

* Line 75: "...these simple geometrical features will address most quantitative needs..." We feel that this may be an overstatement, e.g. we can imagine that there should be many relevant two-dimensional patterns in biology?!*

We have modified this sentence to avoid potential confusion (lines 76-77).

• *

• Line 83: "After a straightforward installation by the user, ...". We think it would be convenient to add the installation steps at this place into the manuscript. *

__This sentence is now modified. We now mention how to install the toolset and we provide the link to the toolset website, if further information is needed (lines 86-88). __On the website, we provide a full video tutorial and a user manual.

* Line 87: "Multicolor images will give a graph with one profile per color." The 'Multicolor images' here should be more precisely stated as "multi-channel" images. Multi-color images could be confused with RGB images which will be treated as 8-bit gray value (type conversion first) images by profile plot in ImageJ. *

We agree with the reviewer that this could create some confusion. We modified "multicolor" to "multi-channel".

* Line 92: "...such as individual bands, blocks, or sarcomeric actin...". While bands and blocks are generic pattern terms, the biological term "sarcomeric actin" does not seem to fit in this list. Could a more generic wording be found, such as "block with spike"? *

We agree with the reviewer that "sarcomeric actin" alone will not be clear to all readers. We modified the text to "block with a central band, as often observed in the muscle field for sarcomeric actin" (lines 103-104). The toolset was modified accordingly.

* Line 95: "the algorithm defines one pattern by having the features of highest intensity in its centre". Could this be rephrased? We did not understand what that exactly means.*

We agree with the reviewer that this was not clear. We rewrote this paragraph (lines 101-114) and provided a supplementary figure to illustrate these definitions (Figure 1 - figure supplement 2).

* Line 124 - 147: This part the only description of the algorithm behind the feature extraction and analysis, but not clearly stated. Many details are missing or assumed known by the reader. For example, how it achieved sub-pixel resolution results is not clear. One can only assume that by fitting Gaussian to the band, the center position (peak) thus can be calculated from continuous curves other than pixels. *

Note that the two sentences introducing this description are "Automated feature extraction is the core of the tool. The algorithm takes multiple steps to achieve this (Fig. S2):". We were hoping this statement was clear, but the reviewer may refer to something else. We agree that the description of some of the details of the steps was too quick. We have now expanded the description where needed.

* Line 407: We think the availability of both the tool and the code could be improved. For Fiji tools it is common practice to create an Update Site and to make the code available on GitHub. In addition, downloading the example file (https://drive.google.com/file/d/1eMazyQJlisWPwmozvyb8VPVbfAgaH7Hz/view?usp=drive_link) required a Google login and access request, which is not very convenient; in fact, we asked for access but it was denied. It would be important for the download to be easier, e.g. from GitHub or Zenodo.

*

We are sorry for issues encountered when downloading the tool and additional material. We thank the reviewer for pointing out these issues that limited the accessibility of our tool. We simplified the downloading procedure on the website, which does not go through the google drive interface nor requires a google account. Additionally, for the coder community the code, user manual and examples are now available from GitHub at github.com/PierreMangeol/PatternJ, and are provided as supplementary material with the manuscript. To our knowledge, update sites work for plugins but not for macro toolsets. Having experience sharing our codes with non-specialists, a classical website with a tutorial video is more accessible than more coder-oriented websites, which deter many users.

* Reviewer #2 (Significance (Required)):

The strength of this study is that a tool for the analysis of one-dimensional repeated patterns occurring in muscle fibres is made available in the accessible open-source platform ImageJ/Fiji. In the introduction to the article the authors provide an extensive review of comparable existing tools. Their new tool fills a gap in terms of providing an easy-to-use software for users without computational skills that enables the analysis of muscle sarcomere patterns. We feel that if the below mentioned limitations could be addressed the tool could indeed be valuable to life scientists interested in muscle patterning without computational skills.

In our view there are a few limitations, including the accessibility of example data and tutorials at sites.google.com/view/patternj, which we had trouble to access. In addition, we think that the workflow in Fiji, which currently requires pressing several buttons in the correct order, could be further simplified and streamlined by adopting some "wizard" approach, where the user is guided through the steps.

*As answered above, the links on the PatternJ website are now corrected. Regarding the workflow, we now provide a Help menu with:

1. __a basic set of instructions to use the tool, __
2. a direct link to the tutorial video in the PatternJ toolset
3. a direct link to the website on which both the tutorial video and a detailed user manual can be found. We hope this addresses the issues raised by this reviewer.

*Another limitation is the reproducibility of the analysis; here we recommend enabling IJ Macro recording as well as saving of the drawn line ROIs. For more detailed suggestions for improvements please see the above sections of our review. *

We agree that saving ROIs is very useful. It is now implemented in PatternJ.

We are not sure what this reviewer means by "enabling IJ Macro recording". The ImageJ Macro Recorder is indeed very useful, but to our knowledge, it is limited to built-in functions. Our code is open and we hope this will be sufficient for advanced users to modify the code and make it fit their needs.*

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

Summary In this manuscript, the authors present a new toolset for the analysis of repetitive patterns in biological images named PatternJ. One of the main advantages of this new tool over existing ones is that it is simple to install and run and does not require any coding skills whatsoever, since it runs on the ImageJ GUI. Another advantage is that it does not only provide the mean length of the pattern unit but also the subpixel localization of each unit and the distributions of lengths and that it does not require GPU processing to run, unlike other existing tools. The major disadvantage of the PatternJ is that it requires heavy, although very simple, user input in both the selection of the region to be analyzed and in the analysis steps. Another limitation is that, at least in its current version, PatternJ is not suitable for time-lapse imaging. The authors clearly explain the algorithm used by the tool to find the localization of pattern features and they thoroughly test the limits of their tool in conditions of varying SNR, periodicity and band intensity. Finally, they also show the performance of PatternJ across several biological models such as different kinds of muscle cells, neurons and fish embryonic somites, as well as different imaging modalities such as brightfield, fluorescence confocal microscopy, STORM and even electron microscopy.

This manuscript is clearly written, and both the section and the figures are well organized and tell a cohesive story. By testing PatternJ, I can attest to its ease of installation and use. Overall, I consider that PatternJ is a useful tool for the analysis of patterned microscopy images and this article is fit for publication. However, i do have some minor suggestions and questions that I would like the authors to address, as I consider they could improve this manuscript and the tool:

*We are grateful to this reviewer for this very positive assessment of PatternJ and of our manuscript.

* Minor Suggestions: In the methodology section is missing a more detailed description about how the metric plotted was obtained: as normalized intensity or precision in pixels. *

We agree with the reviewer that a more detailed description of the metric plotted was missing. We added this information in the method part and added information in the Figure captions where more details could help to clarify the value displayed.

* The validation is based mostly on the SNR and patterns. They should include a dataset of real data to validate the algorithm in three of the standard patterns tested. *

We validated our tool using computer-generated images, in which we know with certainty the localization of patterns. This allowed us to automatically analyze 30 000 images, and with varying settings, we sometimes analyzed 10 times the same image, leading to about 150 000 selections analyzed. From these analyses, we can provide with confidence an unbiased assessment of the tool precision and the tool capacity to extract patterns. We already provided examples of various biological data images in Figures 4-6, showing all possible features that can be extracted with PatternJ. In these examples, we can claim by eye that PatternJ extracts patterns efficiently, but we cannot know how precise these extractions are because of the nature of biological data: "real" positions of features are unknown in biological data. Such validation will be limited to assessing whether a pattern was found or not, which we believe we already provided with the examples in Figures 4-6.

* The video tutorial available in the PatternJ website is very useful, maybe it would be worth it to include it as supplemental material for this manuscript, if the journal allows it. *

As the video tutorial may have been missed by other reviewers, we agree it is important to make it more prominent to users. We have now added a Help menu in the toolset that opens the tutorial video. Having the video as supplementary material could indeed be a useful addition if the size of the video is compatible with the journal limits.

* An example image is provided to test the macro. However, it would be useful to provide further example images for each of the three possible standard patterns suggested: Block, actin sarcomere or individual band.*

We agree this can help users. We now provide another multi-channel example image on the PatternJ website including blocks and a pattern made of a linear intensity gradient that can be extracted with our simpler "single pattern" algorithm, which were missing in the first example. Additionally, we provide an example to be used with our new time-lapse analysis.

* Access to both the manual and the sample images in the PatternJ website should be made publicly available. Right now they both sit in a private Drive account. *

As mentioned above, we apologize for access issues that occurred during the review process. These files can now be downloaded directly on the website without any sort of authentication. Additionally, these files are now also available on GitHub.

* Some common errors are not properly handled by the macro and could be confusing for the user: When there is no selection and one tries to run a Check or Extraction: "Selection required in line 307 (called from line 14). profile=getProfile( ;". A simple "a line selection is required" message would be useful there. When "band" or "block" is selected for a channel in the "Set parameters" window, yet a 0 value is entered into the corresponding "Number of bands or blocks" section, one gets this error when trying to Extract: "Empty array in line 842 (called from line 113). if ( ( subloc . length == 1 ) & ( subloc [ 0 == 0) ) {". This error is not too rare, since the "Number of bands or blocks" section is populated with a 0 after choosing "sarcomeric actin" (after accepting the settings) and stays that way when one changes back to "blocks" or "bands".*

We thank the reviewer for pointing out these bugs. These bugs are now corrected in the revised version.

* The fact that every time one clicks on the most used buttons, the getDirectory window appears is not only quite annoying but also, ultimately a waste of time. Isn't it possible to choose the directory in which to store the files only once, from the "Set parameters" window?*

We have now found a solution to avoid this step. The user is only prompted to provide the image folder when pressing the "Set parameter" button. We kept the prompt for directory only when the user selects the time-lapse analysis or the analysis of multiple ROIs. The main reason is that it is very easy for the analysis to end up in the wrong folder otherwise.

* The authors state that the outputs of the workflow are "user friendly text files". However, some of them lack descriptive headers (like the localisations and profiles) or even file names (like colors.txt). If there is something lacking in the manuscript, it is a brief description of all the output files generated during the workflow.*

PatternJ generates multiple files, several of which are internal to the toolset. They are needed to keep track of which analyses were done, and which colors were used in the images, amongst others. From the user part, only the files obtained after the analysis All_localizations.channel_X.txt and sarcomere_lengths.txt are useful. To improve the user experience, we now moved all internal files to a folder named "internal", which we think will clarify which outputs are useful for further analysis, and which ones are not. We thank the reviewer for raising this point and we now mention it in our Tutorial.

I don't really see the point in saving the localizations from the "Extraction" step, they are even named "temp".

We thank the reviewer for this comment, this was indeed not necessary. We modified PatternJ to delete these files after they are used.

* In the same line, I DO see the point of saving the profiles and localizations from the "Extract & Save" step, but I think they should be deleted during the "Analysis" step, since all their information is then grouped in a single file, with descriptive headers. This deleting could be optional and set in the "Set parameters" window.*

We understand the point raised by the reviewer. However, the analysis depends on the reference channel picked, which is asked for when starting an analysis, and can be augmented with additional selections. If a user chooses to modify the reference channel or to add a new profile to the analysis, deleting all these files would mean that the user will have to start over again, which we believe will create frustration. An optional deletion at the analysis step is simple to implement, but it could create problems for users who do not understand what it means practically.

* Moreover, I think it would be useful to also save the linear roi used for the "Extract & Save" step, and eventually combine them during the "Analysis step" into a single roi set file so that future re-analysis could be made on the same regions. This could be an optional feature set from the "Set parameters" window. *

We agree with the reviewer that saving ROIs is very useful. ROIs are now saved into a single file each time the user extracts and saves positions from a selection. Additionally, the user can re-use previous ROIs and analyze an image or image series in a single step.

* In the "PatternJ workflow" section of the manuscript, the authors state that after the "Extract & Save" step "(...) steps 1, 2, 4, and 5 can be repeated on other selections (...)". However, technically, only steps 1 and 5 are really necessary (alternatively 1, 4 and 5 if the user is unsure of the quality of the patterning). If a user follows this to the letter, I think it can lead to wasted time.

*

We agree with the reviewer and have corrected the manuscript accordingly (line 119-120).

• *

*I believe that the "Version Information" button, although important, has potential to be more useful if used as a "Help" button for the toolset. There could be links to useful sources like the manuscript or the PatternJ website but also some tips like "whenever possible, use a higher linewidth for your line selection" *

We agree with the reviewer as pointed out in our previous answers to the other reviewers. This button is now replaced by a Help menu, including a simple tutorial in a series of images detailing the steps to follow, a link to the user website, and a link to our video tutorial.

* It would be interesting to mention to what extent does the orientation of the line selection in relation to the patterned structure (i.e. perfectly parallel vs more diagonal) affect pattern length variability?*

As answered to reviewer 1, we understand this concern, which needs to be clarified for readers. The issue may be concerning at first sight, but the errors grow only with the inverse of cosine and are therefore rather low. For example, if the user creates a selection off by 3 degrees, which is visually obvious, lengths will be affected by an increase of only 0.14%. The point raised by the reviewer is important to discuss, and we therefore have added a comment on the choice of selection (lines 94-98) as well as a supplementary figure (Figure 1 - figure supplement 1).

* When "the algorithm uses the peak of highest intensity as a starting point and then searches for peak intensity values one spatial period away on each side of this starting point" (line 133-135), does that search have a range? If so, what is the range? *

We agree that this information is useful to share with the reader. The range is one pattern size. We have modified the sentence to clarify the range of search used and the resulting limits in aperiodicity (now lines 176-181).

* Line 144 states that the parameters of the fit are saved and given to the user, yet I could not find such information in the outputs. *

The parameters of the fits are saved for blocks. We have now clarified this point by modifying the manuscript (lines 186-198) and modifying Figure 1 - figure supplement 5. We realized we made an error in the description of how edges of "block with middle band" are extracted. This is now corrected.

* In line 286, authors finish by saying "More complex patterns from electron microscopy images may also be used with PatternJ.". Since this statement is not backed by evidence in the manuscript, I suggest deleting it (or at the very least, providing some examples of what more complex patterns the authors refer to). *

This sentence is now deleted.

* In the TEM image of the fly wing muscle in fig. 4 there is a subtle but clearly visible white stripe pattern in the original image. Since that pattern consists of 'dips', rather than 'peaks' in the profile of the inverted image, they do not get analyzed. I think it is worth mentioning that if the image of interest contains both "bright" and "dark" patterns, then the analysis should be performed in both the original and the inverted images because the nature of the algorithm does not allow it to detect "dark" patterns. *

We agree with the reviewer's comment. We now mention this point in lines 337-339.

* In line 283, the authors mention using background correction. They should explicit what method of background correction they used. If they used ImageJ's "subtract background' tool, then specify the radius.*

We now describe this step in the method section.

*

Reviewer #3 (Significance (Required)):

• Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field. Being a software paper, the advance proposed by the authors is technical in nature. The novelty and significance of this tool is that it offers quick and simple pattern analysis at the single unit level to a broad audience, since it runs on the ImageJ GUI and does not require any programming knowledge. Moreover, all the modules and steps are well described in the paper, which allows easy going through the analysis.
• Place the work in the context of the existing literature (provide references, where appropriate). The authors themselves provide a good and thorough comparison of their tool with other existing ones, both in terms of ease of use and on the type of information extracted by each method. While PatternJ is not necessarily superior in all aspects, it succeeds at providing precise single pattern unit measurements in a user-friendly manner.
• State what audience might be interested in and influenced by the reported findings. Most researchers working with microscopy images of muscle cells or fibers or any other patterned sample and interested in analyzing changes in that pattern in response to perturbations, time, development, etc. could use this tool to obtain useful, and otherwise laborious, information. *

We thank the reviewer for these enthusiastic comments about how straightforward for biologists it is to use PatternJ and its broad applicability in the bio community.

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

Learn more at Review Commons

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Referee #2

Evidence, reproducibility and clarity

Summary

The authors present an ImageJ Macro GUI tool set for the quantification of one-dimensional repeated patterns that are commonly occurring in microscopy images of muscles.

Major comments

In our view the article and also software could be improved in terms of defining the scope of its applicability and user-ship. In many parts the article and software suggest that general biological patterns can be analysed, but then in other parts very specific muscle actin wordings are used. We are pointing this out in the "Minor comments" sections below. We feel that the authors could improve their work by making a clear choice here. One option would be to clearly limit the scope of the tool to the analysis of actin structures in muscles. In this case we would recommend to also rename the tool, e.g. MusclePatternJ. The other option would be to make the tool about the generic analysis of one-dimensional patterns, maybe calling the tool LinePatternJ. In the latter case we would recommend to remove all actin specific wordings from the macro tool set and also the article should be in parts slightly re-written.

Minor/detailed comments

Software

We recommend considering the following suggestions for improving the software.

File and folder selection dialogs

In general, clicking on many of the buttons just opens up a file-browser dialog without any further information. For novel users it is not clear what the tool expects one to select here. It would be very good if the software could be rewritten such that there are always clear instructions displayed about which file or folder one should open for the different buttons.

Extract button

The tool asks one to specify things like whether selections are drawn "M-line-to-M-line"; for users that are not experts in muscle morphology this is not understandable. It would be great to find more generally applicable formulations.

Manual selection accuracy

The 1st step of the analysis is always to start from a user hand-drawn profile across intensity patterns in the image. However, this step can cause inaccuracy that varies with the shape and curve of the line profile drawn. If not strictly perpendicular to for example the M line patterns, the distance between intensity peaks will be different. This will be more problematic when dealing with non-straight and parallelly poised features in the image. If the structure is bended with a curve, the line drawn over it also needs to reproduce this curve, to precisely capture the intensity pattern. I found this limits the reproducibility and easy-usability of the software.

Reproducibility

Since the line profile drawn on the image is the first step and very essential to the entire process, it should be considered to save together with the analysis result. For example, as ImageJ ROI or ROIset files that can be re-imported, correctly positioned, and visualized in the measured images. This would greatly improve the reproducibility of the proposed workflow. In the manuscript, only the extracted features are being saved (because the save button is also just asking for a folder containing images, so I cannot verify its functionality).

? button

It would be great if that button would open up some usage instructions.

Easy improvement of workflow

I would suggest a reasonable expansion of the current workflow, by fitting and displaying 2D lines to the band or line structure in the image, that form the "patterns" the author aims to address. Thus, it extracts geometry models from the image, and the inter-line distance, and even the curve formed by these sets of lines can be further analyzed and studied. These fitted 2D lines can be also well integrated into ImageJ as Line ROI, and thus be saved, imported back, and checked or being further modified. I think this can largely increase the usefulness and reproducibility of the software.

Manuscript

We recommend considering the following suggestions for improving the manuscript. Abstract: The abstract suggests that general patterns can be quantified, however the actual tool quantifies specific subtypes of one-dimensional patterns. We recommend adapting the abstract accordingly.

Line 58: Gray-level co-occurrence matrix (GLCM) based feature extraction and analysis approach is not mentioned nor compared. At least there's a relatively recent study on Sarcomeres structure based on GLCM feature extraction: https://github.com/steinjm/SotaTool with publication: https://doi.org/10.1002/cpz1.462

Line 75: "...these simple geometrical features will address most quantitative needs..." We feel that this may be an overstatement, e.g. we can imagine that there should be many relevant two-dimensional patterns in biology?!

Line 83: "After a straightforward installation by the user, ...". We think it would be convenient to add the installation steps at this place into the manuscript.

Line 87: "Multicolor images will give a graph with one profile per color." The 'Multicolor images' here should be more precisely stated as "multi-channel" images. Multi-color images could be confused with RGB images which will be treated as 8-bit gray value (type conversion first) images by profile plot in ImageJ.

Line 92: "...such as individual bands, blocks, or sarcomeric actin...". While bands and blocks are generic pattern terms, the biological term "sarcomeric actin" does not seem to fit in this list. Could a more generic wording be found, such as "block with spike"?

Line 95: "the algorithm defines one pattern by having the features of highest intensity in its centre". Could this be rephrased? We did not understand what that exactly means.

Line 124 - 147: This part the only description of the algorithm behind the feature extraction and analysis, but not clearly stated. Many details are missing or assumed known by the reader. For example, how it achieved sub-pixel resolution results is not clear. One can only assume that by fitting Gaussian to the band, the center position (peak) thus can be calculated from continuous curves other than pixels.

Line 407: We think the availability of both the tool and the code could be improved. For Fiji tools it is common practice to create an Update Site and to make the code available on GitHub. In addition, downloading the example file (https://drive.google.com/file/d/1eMazyQJlisWPwmozvyb8VPVbfAgaH7Hz/view?usp=drive_link) required a Google login and access request, which is not very convenient; in fact, we asked for access but it was denied. It would be important for the download to be easier, e.g. from GitHub or Zenodo.

Significance

The strength of this study is that a tool for the analysis of one-dimensional repeated patterns occurring in muscle fibres is made available in the accessible open-source platform ImageJ/Fiji. In the introduction to the article the authors provide an extensive review of comparable existing tools. Their new tool fills a gap in terms of providing an easy-to-use software for users without computational skills that enables the analysis of muscle sarcomere patterns. We feel that if the below mentioned limitations could be addressed the tool could indeed be valuable to life scientists interested in muscle patterning without computational skills.

In our view there are a few limitations, including the accessibility of example data and tutorials at sites.google.com/view/patternj, which we had trouble to access. In addition, we think that the workflow in Fiji, which currently requires pressing several buttons in the correct order, could be further simplified and streamlined by adopting some "wizard" approach, where the user is guided through the steps. Another limitation is the reproducibility of the analysis; here we recommend enabling IJ Macro recording as well as saving of the drawn line ROIs. For more detailed suggestions for improvements please see the above sections of our review.

You need tap the pencil icon next to "Single Posts" and enter editing mode and then find Options button at top-right.

Does this apply to .qmd documents?

Author response:

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

eLife assessment

The authors discuss an effect, "diffusive lensing", by which particles would accumulate in high-viscosity regions, for instance in the intracellular medium. To obtain these results, the authors rely on agent-based simulations using custom rules performed with the Ito stochastic calculus convention. The "lensing effect" discussed is a direct consequence of the choice of the Ito convention without spurious drift which has been discussed before and is likely to be inadequate for the intracellular medium, causing the presented results to likely have little relevance for biology.

We thank the editors and the reviewers for their consideration of our manuscript. We argue in this rebuttal and revision that our results and conclusions are in fact likely to have relevance for biology. While we use the Itô convention for ease of modeling considering its non-anticipatory nature upon discretization (see (Volpe and Wehr 2016) for the discretization schemes), we refer to Figure S1B to emphasize that diffusive lensing occurs not only under the Itô convention but across a wide parameter space. Indeed, it is absent only in the normative isothermal convention; note that even a stochastic differential equation conforming to the isothermal convention may be reformulated into the Itô convention by adding suitable drift terms, allowing for diffusive lensing to be seen even in case of the isothermal convention. We note in particular that the choice of the convention is a highly context-dependent one (Sokolov 2010); there is not a universally correct choice, and one can obtain stochastic differential equations consistent with Ito or Stratonovich interpretations in different regimes. Lastly, space-dependent diffusivity is now an experimentally well-recognized feature of the cellular interior, as noted in our references and as discussed further later in this response. This fact points towards the potential relevance of our model for subcellular diffusion.

In our revised preprint, we have made changes to the text and minor changes to figures to address reviewer concerns.

Responses to the Reviewers

We thank the reviewers for their feedback and address the issues they raised in this rebuttal and in the revised manuscript. The central point that the reviewers raise concerns the validity of the drift-less Itô interpretation in modeling potential nonequilibrium types of subcellular transport arising from space-dependent diffusivity. If the drift term were considered, the resulting stochastic differential equation stochastic differential equation (SDE) is equivalent to one arising from the isothermal interpretation of heterogeneous diffusivity (Volpe and Wehr 2016), wherein no diffusive lensing is seen (as shown in Fig. S1B). That is, the isothermal interpretation and the drift-comprising Itô SDE produce the same uniform steady-state particle densities.

While we agree with the reviewers that for a given interpretation, equivalent stochastic differential equations (SDEs) arising from other interpretations may be drawn, we disagree with the generalization that all types of subcellular diffusion conform to the isothermal interpretation. That is, there is no reason why any and all instances of nonequilibrium subcellular particle diffusion must be modeled using isothermal-conforming SDEs (such as the drift-comprising Itô SDE, for instance). We refer to (Sokolov 2010) which prescribes choosing a convention in a context-dependent manner. In this regard, we disagree with the second reviewer’s characterization of making such a choice merely a “choice of writing” considering that it is entirely dependent on the choice of microscopic parameters, as detailed in the discussion section of the manuscript. The following references have also been added to the manuscript: the reference from the first reviewer (Kupferman et al. 2004) proposes a prescription for choosing an appropriate convention based upon comparing the noise correlation time and the particle relaxation time. The reference notes that the Itô convention is appropriate when the particle relaxation time is large when compared to the noise correlation time and the Stratonovich convention is appropriate in the converse scenario. In (Rupprecht et al. 2018), active noise is considered and the resulting Fokker-Planck equation conforms to the Stratonovich convention when thermal noise was negligible. The related reference, (Vishen et al. 2019) compares three timescales: those of particle relaxation, noise correlation and viscoelastic relaxation, to make the choice. Indeed, as noted in the manuscript, lensing is seen in all but one interpretation (without drift additions); only its magnitude is altered by the interpretation/choice of the drift term. The appendix has been modified to include a subsection on the interchangeability of the conventions.

Separately, with regards to the discussion on anomalous diffusion, the section on mean squared displacement calculation has been amended to avoid confusing our model with canonical anomalous diffusion which considers the anomalous exponent; how the anomalous exponent varies with space-dependent diffusivity offers an interesting future area of study.

Responses to specific reviewer comments appear below.

Reviewer #1 (Public Review):

The manuscript "Diffusive lensing as a mechanism of intracellular transport and compartmentalization", explores the implications of heterogeneous viscosity on the diffusive dynamics of particles. The authors analyze three different scenarios:

(i)   diffusion under a gradient of viscosity,

(ii)  clustering of interacting particles in a viscosity gradient, and

(iii) diffusive dynamics of non-interacting particles with circular patches of heterogeneous viscous medium.

The implications of a heterogeneous environment on phase separation and reaction kinetics in cells are under-explored. This makes the general theme of this manuscript very relevant and interesting. However, the analysis in the manuscript is not rigorous, and the claims in the abstract are not supported by the analysis in the main text.

Following are my main comments on the work presented in this manuscript:

(a) The central theme of this work is that spatially varying viscosity leads to position-dependent diffusion constant. This, for an overdamped Langevin dynamics with Gaussian white noise, leads to the well-known issue of the interpretation of the noise term.

The authors use the Ito interpretation of the noise term because their system is non-equilibrium.

One of the main criticisms I have is on this central point. The issue of interpretation arises only when there are ill-posed stochastic dynamics that do not have the relevant timescales required to analyze the noise term properly. Hence, if the authors want to start with an ill-posed equation it should be mentioned at the start. At least the Langevin dynamics considered should be explicitly mentioned in the main text. Since this work claims to be relevant to biological systems, it is also of significance to highlight the motivation for using the ill-posed equation rather than a well-posed equation. The authors refer to the non-equilibrium nature of the dynamics but it is not mentioned what non-equilibrium dynamics to authors have in mind. To properly analyze an overdamped Langevin dynamics a clear source of integrated timescales must be provided. As an example, one can write the dynamics as Eq. (1) \dot x = f(x) + g(x) \eta , which is ill-defined if the noise \eta is delta correlated in time but well-defined when \eta is exponentially correlated in time. One can of course look at the limit in which the exponential correlation goes to a delta correlation which leads to Eq. (1) interpreted in Stratonovich convention. The choice to use the Ito convention for Eq. (1) in this case is not justified.

We thank the reviewer for detailing their concerns with our model’s assumptions. We have addressed them in the common rebuttal.

(b) Generally, the manuscript talks of viscosity gradient but the equations deal with diffusion which is a combination of viscosity, temperature, particle size, and particle-medium interaction. There is no clear motivation provided for focus on viscosity (cytoplasm as such is a complex fluid) instead of just saying position-dependent diffusion constant. Maybe authors should use viscosity only when talking of a context where the existence of a viscosity gradient is established either in a real experiment or in a thought experiment.

The manuscript has been amended to use only “diffusivity” to avoid confusion.

(c) The section "Viscophoresis drives particle accumulation" seems to not have new results. Fig. 1 verifies the numerical code used to obtain the results in the later sections. If that is the case maybe this section can be moved to supplementary or at least it should be clearly stated that this is to establish the correctness of the simulation method. It would also be nice to comment a bit more on the choice of simulation methods with changing hopping sizes instead of, for example, numerically solving stochastic ODE.

The main point of this section and of Fig. 1 is the diffusive lensing effect itself: the accumulation of particles in lower-diffusivity areas. To the best of our knowledge, diffusive lensing has not been reported elsewhere as a specific outcome of non-isothermal interpretations of diffusion, with potential relevance to nonequilibrium subcellular motilities. The simulation method has been fully described in the Methods section, and the code has also been shared (see Code Availability).

A minor comment, the statement "the physically appropriate convention to use depends upon microscopic parameters and timescale hierarchies not captured in a coarse-grained model of diffusion." is not true as is noted in the references that authors mention, a correct coarse-grained model provides a suitable convention (see also Phys. Rev. E, 70(3), 036120., Phys. Rev. E, 100(6), 062602.).

This has been addressed in the common rebuttal.

(d) The section "Interaction-mediated clustering is affected by viscophoresis" makes an interesting statement about the positioning of clusters by a viscous gradient. As a theoretical calculation, the interplay between position-dependent diffusivity and phase separation is indeed interesting, but the problem needs more analysis than that offered in this manuscript. Just a plot showing clustering with and without a gradient of diffusion does not give enough insight into the interplay between density-dependent diffusion and position-dependent diffusion. A phase plot that somehow shows the relative contribution of the two effects would have been nice. Also, it should be emphasized in the main text that the inter-particle interaction is through a density-dependent diffusion constant and not a conservative coupling by an interaction potential.

The density-dependence has been added from the Methods to the main text. The goal of the work is to present lensing as a natural outcome of the parameter choices we make and present its effects as they relate to clustering and commonly used biophysical methods to probe dynamics within cells. A dense sampling of the phase space and how it is altered as a function of diffusivity, and the subsequent interpretation, lie beyond the scope of the present work but offer exciting future directions of study.

(e) The section "In silico microrheology shows that viscophoresis manifests as anomalous diffusion" the authors show that the MSD with and without spatial heterogeneity is different. This is not a surprise - as the underlying equations are different the MSD should be different.

The goal here is to compare and contrast the ways in which homogeneous and heterogeneous diffusion manifest in simulated microrheology measurements. We hope that an altered saturation MSD, as is observed in our simulations, provokes interest in considering lensing while modeling experimental data.

There are various analogies drawn in this section without any justification:

(i) "the saturation MSD was higher than what was seen in the homogeneous diffusion scenario possibly due to particles robustly populating the bulk milieu followed by directed motion into the viscous zone (similar to that of a Brownian ratchet, (Peskin et al., 1993))."

In case of i), the Brownian ratchet is invoked as a model to explain directed accumulation. We have removed this analogy to avoid confusion as it is not delved into further over the course of our work.

(ii) "Note that lensing may cause particle displacements to deviate from a Gaussian distribution, which could explain anomalous behaviors observed both in our simulations and in experiments in cells (Parry et al., 2014)." Since the full trajectory of the particles is available, it can be analyzed to check if this is indeed the case.

This has been addressed in the common rebuttal.

(f) The final section "In silico FRAP in a heterogeneously viscous environment ... " studies the MSD of the particles in a medium with heterogeneous viscous patches which I find the most novel section of the work. As with the section on inter-particle interaction, this needs further analysis.

We thank the reviewer for their appreciation. In presenting these three sections discussing the effects of diffusive lensing, we intend to broadly outline the scope of this phenomenon in influencing a range of behaviors. Exploring the directions further comprise promising future directions of study that lie beyond the scope of this manuscript.

To summarise, as this is a theory paper, just showing MSD or in silico FRAP data is not sufficient. Unlike experiments where one is trying to understand the systems, here one has full access to the dynamics either analytically or in simulation. So just stating that the MSD in heterogeneous and homogeneous environments are not the same is not sufficient. With further analysis, this work can be of theoretical interest. Finally, just as a matter of personal taste, I am not in favor of the analogy with optical lensing. I don't see the connection.

We value the reviewer’s interest in investigating the causes underlying the differences in the MSDs and agree that it represents a promising future area of study. The main point of this section of the manuscript was to make a connection to experimentally measurable quantities.

Reviewer #2 (Public Review):

Summary:

The authors study through theory and simulations the diffusion of microscopic particles and aim to account for the effects of inhomogeneous viscosity and diffusion - in particular regarding the intracellular environment. They propose a mechanism, termed "Diffusive lensing", by which particles are attracted towards high-viscosity regions where they remain trapped. To obtain these results, the authors rely on agent-based simulations using custom rules performed with the Ito stochastic calculus convention, without spurious drift. They acknowledge the fact that this convention does not describe equilibrium systems, and that their results would not hold at equilibrium - and discard these facts by invoking the fact that cells are out-of-equilibrium. Finally, they show some applications of their findings, in particular enhanced clustering in the high-viscosity regions. The authors conclude that as inhomogeneous diffusion is ubiquitous in life, so must their mechanism be, and hence it must be important.

Strengths:

The article is well-written, and clearly intelligible, its hypotheses are stated relatively clearly and the models and mathematical derivations are compatible with these hypotheses.

We thank the reviewer for their appreciation.

Weaknesses:

The main problem of the paper is these hypotheses. Indeed, it all relies on the Ito interpretation of the stochastic integrals. Stochastic conventions are a notoriously tricky business, but they are both mathematically and physically well-understood and do not result in any "dilemma" [some citations in the article, such as (Lau and Lubensky) and (Volpe and Wehr), make an unambiguous resolution of these]. Conventions are not an intrinsic, fixed property of a system, but a choice of writing; however, whenever going from one to another, one must include a "spurious drift" that compensates for the effect of this change - a mathematical subtlety that is entirely omitted in the article: if the drift is zero in one convention, it will thus be non-zero in another in the presence of diffusive gradients. It is well established that for equilibrium systems obeying fluctuation-dissipation, the spurious drift vanishes in the anti-Ito stochastic convention (which is not "anticipatory", contrarily to claims in the article, are the "steps" are local and infinitesimal). This ensures that the diffusion gradients do not induce currents and probability gradients, and thus that the steady-state PDF is the Gibbs measure. This equilibrium case should be seen as the default: a thermal system NOT obeying this law should warrant a strong justification (for instance in the Volpe and Wehr review this can occur through memory effects in robotic dynamics, or through strong fluctuation-dissipation breakdown). In near-equilibrium thermal systems such as the intracellular medium (where, although out-of-equilibrium, temperature remains a relevant and mostly homogeneous quantity), deviations from this behavior must be physically justified and go to zero when going towards equilibrium.

Considering that the physical phenomena underlying diffusion span a range of timescales (particle relaxation, noise, environmental correlation, et cetera), we disagree with the assertion that all types of subcellular diffusion processes can be modeled as occurring at thermal equilibrium: for example, one can easily imagine memory effects arising in the presence of an appropriate hierarchy of timescales. We have added references that describe in more detail the way in which the comparison of timescales can dictate the applicability of different conventions. We also refer the referee to the common rebuttal section of our response in which we discuss factors that govern the choice of the interpretation. The adiabatic elimination arguments highlighted in (Kupferman et al. 2004) provide a clear description of how relevant particle and environment-related timescales can inform the choice of stochastic calculus to use.

With regards to the use of the term “anticipatory” to refer to the isothermal interpretation, we refer to the comment in (Volpe and Wehr 2016) of the Itô interpretation “not looking into the future”. In any case, whether anticipatory or otherwise, the interpretation’s effect on our model remains unchanged, as highlighted in the section in the Appendix on the conversion between different conventions; this section has been added to minimize confusion about the effects of the choice of convention on lensing.

Here, drifts are arbitrarily set to zero in the Ito convention (the exact opposite of the equilibrium anti-Ito), which is the equilibrium equivalent to adding a force (with drift $- grad D$) exactly compensating the spurious drift. If we were to interpret this as a breakdown of detailed balance with inhomogeneous temperature, the "hot" region would be effectively at 4x higher temperature than the cold region (i.e. 1200K) in Fig 1A.

Our work is based on existing observations of space-dependent diffusivity in cells (Garner et al., 2023; Huang et al., 2021; Parry et al., 2014; Śmigiel et al., 2022; Xiang et al., 2020). These papers support a definitive model for the existence of space-dependent diffusivity without invoking space-dependent temperature.

It is the effects of this arbitrary force (exactly compensating the Ito spurious drift) that are studied in the article. The fact that it results in probability gradients is trivial once formulated this way (and in no way is this new - many of the references, for instance, Volpe and Wehr, mention this).

Addressed in the common rebuttal.

Enhanced clustering is also a trivial effect of this probability gradient (the local concentration is increased by this force field, so phase separation can occur). As a side note the "neighbor sensing" scheme to describe interactions is very peculiar and not physically motivated - it violates stochastic thermodynamics laws too, as the detailed balance is apparently not respected.

The neighbor-sensing scheme used here is just one possible model of an effective attractive potential between particles. Other models that lead to density-dependent attraction between particles should also provide qualitatively similar results as ours; this offers an interesting prospect for future research.

Finally, the "anomalous diffusion" discussion is at odds with what the literature on this subject considers anomalous (the exponent does not appear anomalous).

This has been addressed in the common rebuttal, and the relevant part of the manuscript has been modified to avoid confusion.

The authors make no further justification of their choice of convention than the fact that cells are out-of-equilibrium, leaving the feeling that this is a detail. They make mentions of systems (eg glycogen, prebiotic environment) for which (near-)equilibrium physics should mostly prevail, and of fluctuation-dissipation ("Diffusivity varies inversely with viscosity", in the introduction). Yet the "phenomenon" they discuss is entirely reliant on an undiscussed mechanism by which these assumptions would be completely violated (the citations they make for this - Gnesotto '18 and Phillips '12 - are simply discussions of the fact that cells are out-of-equilibrium, not on any consequences on the convention).

Finally, while inhomogeneous diffusion is ubiquitous, the strength of this effect in realistic conditions is not discussed (this would be a significant problem if the effect were real, which it isn't). Gravitational attraction is also an ubiquitous effect, but it is not important for intracellular compartmentalization.

The manuscript text has been supplemented with additional references that detail the ways in which the comparison of timescales can dictate how one can apply different conventions. We refer the reviewer to the common rebuttal section of our response where we detail factors that dictate the choice of the convention to use. As previously noted, the adiabatic elimination arguments highlighted in (Kupferman et al., 2004) provide a prescription for how different timescales are to be considered in deciding the choice of stochastic calculus to use.

With regards to the strength of space-dependent diffusivity in subcellular milieu, various measurements of heterogeneous diffusivity have been made both across different model systems and via different modalities, as cited in our manuscript. (Garner et al. 2023) used single-particle tracking to determine over 100-fold variability in diffusivity within individual S. pombe cells. Single-molecule measurements in (Xiang et al. 2020) and (Śmigiel et al. 2022) reveal an order-of-magnitude variation in tracer diffusion in mammalian cells and multi-fold variation in E. coli cytoplasm respectively. Fluorescence correlation spectroscopy measurements in (Huang et al. 2022) have found a two-fold increase in short-range diffusion of protein-sized tracers in X. laevis extracts. We have also added a reference to a study that uses 3D single particle tracking in the cytosol of a multinucleate fungus, A. gossypii, to identify regions of low-diffusivity near nuclei and hyphal tips (McLaughlin et al. 2020). Many of these references deploy particle tracking and investigate how mesoscale-sized particles (i.e. tracers spanning biologically relevant size scales) are directly impacted by space-dependent diffusivity. Therefore, we base our model on not only space-dependent diffusivity being a well-recognized feature of the cellular interior, but also on these observations pertaining to mesoscale-sized particles’ motion along relevant timescales.

These measurements are also relevant to the reviewer’s question about the strength of the effect, which depends directly on the variability in diffusivity: for ten- or a hundred-fold diffusivity variations, the effect would be expected to be significant. In case of using the Itô convention directly, the contrast in concentration gradient is, in fact, that of the diffusivity gradient.

To conclude, the "diffusive lensing" effect presented here is not a deep physical discovery, but a well-known effect of sticking to the wrong stochastic convention.

As detailed in the various responses above, we respectfully disagree with the notion that there exists a singular correct stochastic convention that is applicable for all cases of subcellular heterogeneous diffusion. Further, as detailed in (Volpe and Wehr 2016) and as detailed in the Appendix, it is possible to convert between conventions and that an isothermal-abiding stochastic differential equation may be suitably altered, by means of adding a drift term, to an Itô-abiding stochastic differential equation; therefore, one can observe diffusive lensing without discarding the isothermal convention if the latter were modified. Indeed, it is only the driftless (or canonical) isothermal convention that does not allow for diffusive lensing.

Author response:

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

Reviewer #1: 

This is my first review of the article entitled "The canonical stopping network: Revisiting the role of the subcortex in response inhibition" by Isherwood and colleagues. This study is one in a series of excellent papers by the Forstmann group focusing on the ability of fMRI to reliably detect activity in small subcortical nuclei - in this case, specifically those purportedly involved in the hyper- and indirect inhibitory basal ganglia pathways. I have been very fond of this work for a long time, beginning with the demonstration of De Hollander, Forstmann et al. (HBM 2017) of the fact that 3T fMRI imaging (as well as many 7T imaging sequences) do not afford sufficient signal to noise ratio to reliably image these small subcortical nuclei. This work has done a lot to reshape my view of seminal past studies of subcortical activity during inhibitory control, including some that have several thousand citations.

In the current study, the authors compiled five datasets that aimed to investigate neural activity associated with stopping an already initiated action, as operationalized in the classic stop-signal paradigm. Three of these datasets are taken from their own 7T investigations, and two are datasets from the Poldrack group, which used 3T fMRI.

The authors make six chief points: 

(1) There does not seem to be a measurable BOLD response in the purportedly critical subcortical areas in contrasts of successful stopping (SS) vs. going (GO), neither across datasets nor within each individual dataset. This includes the STN but also any other areas of the indirect and hyperdirect pathways.

(2) The failed-stop (FS) vs. GO contrast is the only contrast showing substantial differences in those nodes.

(3) The positive findings of STN (and other subcortical) activation during the SS vs. GO contrast could be due to the usage of inappropriate smoothing kernels.

(4) The study demonstrates the utility of aggregating publicly available fMRI data from similar cognitive tasks. 

(5) From the abstract: "The findings challenge previous functional magnetic resonance (fMRI) of the stop-signal task" 

(6) and further: "suggest the need to ascribe a separate function to these networks." 

I strongly and emphatically agree with points 1-5. However, I vehemently disagree with point 6, which appears to be the main thrust of the current paper, based on the discussion, abstract, and - not least - the title.

To me, this paper essentially shows that fMRI is ill-suited to study the subcortex in the specific context of the stop-signal task. That is not just because of the issues of subcortical small-volume SNR (the main topic of this and related works by this outstanding group), but also because of its limited temporal resolution (which is unacknowledged, but especially impactful in the context of the stop-signal task). I'll expand on what I mean in the following.

First, the authors are underrepresenting the non-fMRI evidence in favor of the involvement of the subthalamic nucleus (STN) and the basal ganglia more generally in stopping actions. 

- There are many more intracranial local field potential recording studies that show increased STN LFP (or even single-unit) activity in the SS vs. FS and SS vs. GO contrast than listed, which come from at least seven different labs. Here's a (likely non-exhaustive) list of studies that come to mind:

Ray et al., NeuroImage 2012 <br /> Alegre et al., Experimental Brain Research 2013 <br /> Benis et al., NeuroImage 2014 <br /> Wessel et al., Movement Disorders 2016 <br /> Benis et al., Cortex 2016 <br /> Fischer et al., eLife 2017 <br /> Ghahremani et al., Brain and Language 2018 <br /> Chen et al., Neuron 2020 <br /> Mosher et al., Neuron 2021 <br /> Diesburg et al., eLife 2021 

- Similarly, there is much more evidence than cited that causally influencing STN via deep-brain stimulation also influences action-stopping. Again, the following list is probably incomplete: 

Van den Wildenberg et al., JoCN 2006 <br /> Ray et al., Neuropsychologia 2009 <br /> Hershey et al., Brain 2010 <br /> Swann et al., JNeuro 2011 <br /> Mirabella et al., Cerebral Cortex 2012 <br /> Obeso et al., Exp. Brain Res. 2013 <br /> Georgiev et al., Exp Br Res 2016 <br /> Lofredi et al., Brain 2021 <br /> van den Wildenberg et al, Behav Brain Res 2021 <br /> Wessel et al., Current Biology 2022 

- Moreover, evidence from non-human animals similarly suggests critical STN involvement in action stopping, e.g.: 

Eagle et al., Cerebral Cortex 2008 <br /> Schmidt et al., Nature Neuroscience 2013 <br /> Fife et al., eLife 2017 <br /> Anderson et al., Brain Res 2020 

Together, studies like these provide either causal evidence for STN involvement via direct electrical stimulation of the nucleus or provide direct recordings of its local field potential activity during stopping. This is not to mention the extensive evidence for the involvement of the STN - and the indirect and hyperdirect pathways in general - in motor inhibition more broadly, perhaps best illustrated by their damage leading to (hemi)ballism. 

Hence, I cannot agree with the idea that the current set of findings "suggest the need to ascribe a separate function to these networks", as suggested in the abstract and further explicated in the discussion of the current paper. For this to be the case, we would need to disregard more than a decade's worth of direct recording studies of the STN in favor of a remote measurement of the BOLD response using (provably) sub ideal imaging parameters. There are myriads of explanations of why fMRI may not be able to reveal a potential ground-truth difference in STN activity between the SS and FS/GO conditions, beginning with the simple proposition that it may not afford sufficient SNR, or that perhaps subcortical BOLD is not tightly related to the type of neurophysiological activity that distinguishes these conditions (in the purported case of the stop-signal task, specifically the beta band). But essentially, this paper shows that a specific lens into subcortical activity is likely broken, but then also suggests dismissing existing evidence from superior lenses in favor of the findings from the 'broken' lens. That doesn't make much sense to me.

Second, there is actually another substantial reason why fMRI may indeed be unsuitable to study STN activity, specifically in the stop-signal paradigm: its limited time resolution. The sequence of subcortical processes on each specific trial type in the stop-signal task is purportedly as follows: at baseline, the basal ganglia exert inhibition on the motor system. During motor initiation, this inhibition is lifted via direct pathway innervation. This is when the three trial types start diverging. When actions then have to be rapidly cancelled (SS and FS), cortical regions signal to STN via the hyperdirect pathway that inhibition has to be rapidly reinstated (see Chen, Starr et al., Neuron 2020 for direct evidence for such a monosynaptic hyperdirect pathway, the speed of which directly predicts SSRT). Hence, inhibition is reinstated (too late in the case of FS trials, but early enough in SS trials, see recordings from the BG in Schmidt, Berke et al., Nature Neuroscience 2013; and Diesburg, Wessel et al., eLife 2021). 

Hence, according to this prevailing model, all three trial types involve a sequence of STN activation (initial inhibition), STN deactivation (disinhibition during GO), and STN reactivation (reinstantiation of inhibition during the response via the hyperdirect pathway on SS/FS trials, reinstantiation of inhibition via the indirect pathway after the response on GO trials). What distinguishes the trial types during this period is chiefly the relative timing of the inhibitory process (earliest on SS trials, slightly later on FS trials, latest on GO trials). However, these temporal differences play out on a level of hundreds of milliseconds, and in all three cases, processing concludes well under a second overall. To fMRI, given its limited time resolution, these activations are bound to look quite similar. 

Lastly, further building on this logic, it's not surprising that FS trials yield increased activity compared to SS and GO trials. That's because FS trials are errors, which are known to activate the STN (Cavanagh et al., JoCN 2014; Siegert et al. Cortex 2014) and afford additional inhibition of the motor system after their occurrence (Guan et al., JNeuro 2022). Again, fMRI will likely conflate this activity with the abovementioned sequence, resulting in a summation of activity and the highest level of BOLD for FS trials. 

In sum, I believe this study has a lot of merit in demonstrating that fMRI is ill-suited to study the subcortex during the SST, but I cannot agree that it warrants any reappreciation of the subcortex's role in stopping, which are not chiefly based on fMRI evidence. 

We would like to thank reviewer 1 for their insightful and helpful comments. We have responded point-by-point below and will give an overview of how we reframed the paper here.  

We agree that there is good evidence from other sources for the presence of the canonical stopping network (indirect and hyperdirect) during action cancellation, and that this should be reflected more in the paper. However, we do not believe that a lack of evidence for this network during the SST makes fMRI ill-suited for studying this task, or other tasks that have neural processes occurring in quick succession. What we believe the activation patterns of fMRI reflect during this task, is the large of amount of activation caused by failed stops. That is, that the role of the STN in error processing may be more pronounced that its role in action cancellation. Due to the replicability of fMRI results, especially at higher field strengths, we believe the activation profile of failed stop trials reflects a paramount role for the STN in error processing. Therefore, while we agree we do not provide evidence against the role of the STN in action cancellation, we do provide evidence that our outlook on subcortical activation during different trial types of this task should be revisited. We have reframed the article to reflect this, and discuss points such as fMRI reliability, validity and the complex overlapping of cognitive processes in the SST in the discussion. Please see all changes to the article indicated by red text.

A few other points: 

- As I said before, this team's previous work has done a lot to convince me that 3T fMRI is unsuitable to study the STN. As such, it would have been nice to see a combination of the subsamples of the study that DID use imaging protocols and field strengths suitable to actually study this node. This is especially true since the second 3T sample (and arguably, the Isherwood_7T sample) does not afford a lot of trials per subject, to begin with.

Unfortunately, this study already comprises of the only 7T open access datasets available for the SST. Therefore, unless we combined only the deHollander_7T and Miletic_7T subsamples there is no additional analysis we can do for this right now. While looking at just the sub samples that were 7T and had >300 trials would be interesting, based on the new framing of the paper we do not believe it adds to the study, as the sub samples still lack the temporal resolution seemingly required for looking at the processes in the SST.

- What was the GLM analysis time-locked to on SS and FS trials? The stop-signal or the GO-signal? 

SS and FS trials were time-locked to the GO signal as this is standard practice. The main reason for this is that we use contrasts to interpret differences in activation patterns between conditions. By time-locking the FS and SS trials to the stop signal, we are contrasting events at different time points, and therefore different stages of processing, which introduces its own sources of error. We agree with the reviewer, however, that a separate analysis with time-locking on the stop-signal has its own merit, and now include results in the supplementary material where the FS and SS trials are time-locked to the stop signal as well.

- Why was SSRT calculated using the outdated mean method? 

We originally calculated SSRT using the mean method as this was how it was reported in the oldest of the aggregated studies. We have now re-calculated the SSRTs using the integration method with go omission replacement and thank the reviewer for pointing this out. Please see response to comment 3.

- The authors chose 3.1 as a z-score to "ensure conservatism", but since they are essentially trying to prove the null hypothesis that there is no increased STN activity on SS trials, I would suggest erring on the side of a more lenient threshold to avoid type-2 error. 

We have used minimum FDR-corrected thresholds for each contrast now, instead of using a blanket conservative threshold of 3.1 over all contrasts. The new thresholds for each contrast are shown in text. Please see below (page 12):

“The thresholds for each contrast are as follows: 3.01 for FS > GO, 2.26 for FS > SS and 3.1 for SS > GO.”

- The authors state that "The results presented here add to a growing literature exposing inconsistencies in our understanding of the networks underlying successful response inhibition". It would be helpful if the authors cited these studies and what those inconsistencies are. 

We thank reviewer 1 for their detailed and thorough evaluation of our paper. Overall, we agree that there is substantial direct and indirect evidence for the involvement of the cortico-basal-ganglia pathways in response inhibition. We have taken the vast constructive criticism on board and agree with the reviewer that the paper should be reframed. We would like to thank the reviewer for the thoroughness of their helpful comments aiding the revising of the paper.

(1) I would suggest reframing the study, abstract, discussion, and title to reflect the fact that the study shows that fMRI is unsuitable to study subcortical activity in the SST, rather than the fact that we need to question the subcortical model of inhibition, given the reasons in my public review.

We agree with the reviewer that the article should be reframed and not taken as direct evidence against the large sum of literature pointing towards the involvement of the cortico-basal-ganglia pathway in response inhibition. We have significantly rewritten the article in light of this.

(2) I suggest combining the datasets that provide the best imaging parameters and then analyzing the subcortical ROIs with a more lenient threshold and with regressors time-locked to the stop-signals (if that's not already the case). This would make the claim of a null finding much more impactful. Some sort of power analysis and/or Bayes factor analysis of evidence for the null would also be appreciated. 

Instead of using a blanket conservative threshold of 3.1, we instead used only FDR-corrected thresholds. The threshold level is therefore different for each contrast and noted in the figures. We have also added supplementary figures including the group-level SPMs and ROI analyses when the FS and SS trials were time-locked to the stop signal instead of the GO signal (Supplementary Figs 4 & 5). But as mentioned above, due to the difference in time points when contrasting, we believe that time-locking to the GO signal for all trial types makes more sense for the main analysis.

We have now also computed BFs on the first level ROI beta estimates for all contrasts using the BayesFactor package as implemented in R. We add the following section to the methods and updated the results section accordingly (page 8):

“In addition to the frequentist analysis we also opted to compute Bayes Factors (BFs) for each contrast per ROI per hemisphere. To do this, we extracted the beta weights for each individual trial type from our first level model. We then compared the beta weights from each trial type to one another using the ‘BayesFactor’ package as implement in R (Morey & Rouder, 2015). We compared the full model comprising of trial type, dataset and subject as predictors to the null model comprising of only the dataset and subject as predictor. The datasets and subjects were modeled as random factors. We divided the resultant BFs from the full model by the null model to provide evidence for or against a significant difference in beta weights for each trial type. To interpret the BFs, we used a modified version of Jeffreys’ scale (Jeffreys, 1939; Lee & Wagenmakers, 2014).”

(3) I suggest calculating SSRT using the integration method with the replacement of Go omissions, as per the most recent recommendation (Verbruggen et al., eLife 2019).

We agree we should have used a more optimal method for SSRT estimation. We have replaced our original estimations with that of the integration method with go omissions replacement, as suggested and adapted the results in table 3.

We have also replaced text in the methods sections to reflect this (page 5):

“For each participant, the SSRT was calculated using the mean method, estimated by subtracting the mean SSD from median go RT (Aron & Poldrack, 2006; Logan & Cowan, 1984).”

Now reads:

“For each participant, the SSRT was calculated using the integration method with replacement of go omissions (Verbruggen et al., 2019), estimated by integrating the RT distribution and calculating the point at which the integral equals p(respond|signal). The completion time of the stop process aligns with the nth RT, where n equals the number of RTs in the RT distribution of go trials multiplied by the probability of responding to a signal.”

Reviewer #2:

This work aggregates data across 5 openly available stopping studies (3 at 7 tesla and 2 at 3 tesla) to evaluate activity patterns across the common contrasts of Failed Stop (FS) > Go, FS > stop success (SS), and SS > Go. Previous work has implicated a set of regions that tend to be positively active in one or more of these contrasts, including the bilateral inferior frontal gyrus, preSMA, and multiple basal ganglia structures. However, the authors argue that upon closer examination, many previous papers have not found subcortical structures to be more active on SS than FS trials, bringing into question whether they play an essential role in (successful) inhibition. In order to evaluate this with more data and power, the authors aggregate across five datasets and find many areas that are *more* active for FS than SS, specifically bilateral preSMA, caudate, GPE, thalamus, and VTA, and unilateral M1, GPi, putamen, SN, and STN. They argue that this brings into question the role of these areas in inhibition, based upon the assumption that areas involved in inhibition should be more active on successful stop than failed stop trials, not the opposite as they observed. 

As an empirical result, I believe that the results are robust, but this work does not attempt a new theoretical synthesis of the neuro-cognitive mechanisms of stopping. Specifically, if these many areas are more active on failed stop than successful stop trials, and (at least some of) these areas are situated in pathways that are traditionally assumed to instantiate response inhibition like the hyperdirect pathway, then what function are these areas/pathways involved in? I believe that this work would make a larger impact if the author endeavored to synthesize these results into some kind of theoretical framework for how stopping is instantiated in the brain, even if that framework may be preliminary. 

I also have one main concern about the analysis. The authors use the mean method for computing SSRT, but this has been shown to be more susceptible to distortion from RT slowing (Verbruggen, Chambers & Logan, 2013 Psych Sci), and goes against the consensus recommendation of using the integration with replacement method (Verbruggen et al., 2019). Therefore, I would strongly recommend replacing all mean SSRT estimates with estimates using the integration with replacement method. 

I found the paper clearly written and empirically strong. As I mentioned in the public review, I believe that the main shortcoming is the lack of theoretical synthesis. I would encourage the authors to attempt to synthesize these results into some form of theoretical explanation. I would also encourage replacing the mean method with the integration with replacement method for computing SSRT. I also have the following specific comments and suggestions (in the approximate order in which they appear in the manuscript) that I hope can improve the manuscript: 

We would like to thank reviewer 2 for their insightful and interesting comments. We have adapted our paper to reflect these comments. Please see direct responses to your comments below. We agree with the reviewer that some type of theoretical synthesis would help with the interpretability of the article. We have substantially reworked the discussion and included theoretical considerations behind the newer narrative. Please see all changes to the article indicated by red text.

(1) The authors say "performance on successful stop trials is quantified by the stop signal reaction time". I don't think this is technically accurate. SSRT is a measure of the average latency of the stop process for all trials, not just for the trials in which subjects successfully stop. 

Thank you for pointing this technically incorrect statement. We have replaced the above sentence with the following (page 1):

“Inhibition performance in the SST as a whole is quantified by the stop signal reaction time (SSRT), which estimates the speed of the latent stopping process (Verbruggen et al., 2019).”

(2) The authors say "few studies have detected differences in the BOLD response between FS and SS trials", but then do not cite any papers that detected differences until several sentences later (de Hollander et al., 2017; Isherwood et al., 2023; Miletic et al., 2020). If these are the only ones, and they only show greater FS than SS, then I think this point could be made more clearly and directly. 

We have moved the citations to the correct place in the text to be clearer. We have also rephrased this part of the introduction to make the points more direct (page 2).

“In the subcortex, functional evidence is relatively inconsistent. Some studies have found an increase in BOLD response in the STN in SS > GO contrasts (Aron & Poldrack, 2006; Coxon et al., 2016; Gaillard et al., 2020; Yoon et al., 2019), but others have failed to replicate this (Bloemendaal et al., 2016; Boehler et al., 2010; Chang et al., 2020; B. Xu et al., 2015). Moreover, some studies have actually found higher STN, SN and thalamic activation in failed stop trials, not successful ones (de Hollander et al., 2017; Isherwood et al., 2023; Miletić et al., 2020).”

(3) Unless I overlooked it, I don't believe that the author specified the criterion that any given subject is excluded based upon. Given some studies have significant exclusions (e.g., Poldrack_3T), I think being clear about how many subjects violated each criterion would be useful. 

This is indeed interesting and important information to include. We have added the number of participants who were excluded for each criterion. Please see added text below (page 4):

“Based on these criteria, no subjects were excluded from the Aron_3T dataset. 24 subjects were excluded from the Poldrack_3T dataset (3 based on criterion 1, 9 on criterion 2, 11 on criterion 3, and 8 on criterion 4). Three subjects were excluded from the deHollander_7T dataset (2 based on criterion 1 and 1 on criterion 2). Five subjects were excluded from the Isherwood_7T dataset (2 based on criterion 1, 1 on criterion 2, and 2 on criterion 4). Two subjects were excluded from the Miletic_7T dataset (1 based on criterion 2 and 1 on criterion 4). Note that some participants in the Poldrack_3T study failed to meet multiple inclusion criteria.”

(4) The Method section included very exhaustive descriptions of the neuroimaging processing pipeline, which was appreciated. However, it seems that much of what is presented is not actually used in any of the analyses. For example, it seems that "functional data preprocessing" section may be fMRIPrep boilerplate, which again is fine, but I think it would help to clarify that much of the preprocessing was not used in any part of the analysis pipeline for any results. For example, at first blush, I thought the authors were using global signal regression, but after a more careful examination, I believe that they are only computing global signals but never using them. Similarly with tCompCor seemingly being computed but not used. If possible, I would recommend that the authors share code that instantiates their behavioral and neuroimaging analysis pipeline so that any confusion about what was actually done could be programmatically verified. At a minimum, I would recommend more clearly distinguishing the pipeline steps that actually went into any presented analyses.

We thank the reviewer for finding this inconsistency. The methods section indeed uses the fMRIprep boilerplate text, which we included so to be as accurate as possible when describing the preprocessing steps taken. While we believe leaving the exact boilerplate text that fMRIprep gives us is the most accurate method to show our preprocessing, we have adapted some of the text to clarify which computations were not used in the subsequent analysis. As a side-note, for future reference, we’d like to add that the fmriprep authors expressly recommend users to report the boilerplate completely and unaltered, and as such, we believe this may become a recurring issue (page 7).

“While many regressors were computed in the preprocessing of the fMRI data, not all were used in the subsequent analysis. The exact regressors used for the analysis can be found above. For example, tCompCor and global signals were calculated in our generic preprocessing pipeline but not part of the analysis. The code used for preprocessing and analysis can be found in the data and code availability statement.”

(5) What does it mean for the Poldrack_3T to have N/A for SSD range? Please clarify. 

Thank you for pointing out this omission. We had not yet found the possible SSD range for this study. We have replaced this value with the correct value (0 – 1000 ms).

(6) The SSD range of 0-2000ms for deHollander_7T and Miletic_7T seems very high. Was this limit ever reached or even approached? SSD distributions could be a useful addition to the supplement. 

Thank you for also bringing this mistake to light. We had accidentally placed the max trial duration in these fields instead of the max allowable SSD value. We have replaced the correct value (0 – 900 ms).

(7) The author says "In addition, median go RTs did not correlate with mean SSRTs within datasets (Aron_3T: r = .411, p = .10, BF = 1.41; Poldrack_3T: r = .011, p = .91, BF = .23; deHollander_7T: r = -.30, p = .09, BF = 1.30; Isherwood_7T: r = .13, p = .65, BF = .57; Miletic_7T: r = .37, p = .19, BF = 1.02), indicating independence between the stop and go processes, an important assumption of the horse-race model (Logan & Cowan, 1984)." However, the independent race model assumes context independence (the finishing time of the go process is not affected by the presence of the stop process) and stochastic independence (the duration of the go and stop processes are independent on a given trial). This analysis does not seem to evaluate either of these forms of independence, as it correlates RT and SSRT across subjects, so it was unclear how this analysis evaluated either of the types of independence that are assumed by the independent race model. Please clarify or remove. 

Thank you for this comment. We realize that this analysis indeed does not evaluate either context or stochastic independence and therefore we have removed this from the manuscript.

(8) The RTs in Isherwood_7T are considerably slower than the other studies, even though the go stimulus+response is the same (very simple) stimulus-response mapping from arrows to button presses. Is there any difference in procedure or stimuli that might explain this difference? It is the only study with a visual stop signal, but to my knowledge, there is no work suggesting visual stop signals encourage more proactive slowing. If possible, I think a brief discussion of the unusually slow RTs in Isherwood_7T would be useful. 

We have included the following text in the manuscript to reflect this observed difference in RT between the Isherwood_7T dataset and the other datasets (page 9).

“Longer RTs were found in the Isherwood_7T dataset in comparison to the four other datasets. The only difference in procedure in the Isherwood_7T dataset is the use of a visual stop signal as opposed to an auditory stop signal. This RT difference is consistent with previous research, where auditory stop signals and visual go stimuli have been associated with faster RTs compared to unimodal visual presentation (Carrillo-de-la-Peña et al., 2019; Weber et al., 2024). The mean SSRTs and probability of stopping are within normal range, indicating that participants understood the task and responded in the expected manner.”

(9) When the authors included both 3T and 7T data, I thought they were preparing to evaluate the effect of magnet strength on stop networks, but they didn't do this analysis. Is this because the authors believe there is insufficient power? It seems that this could be an interesting exploratory analysis that could improve the paper.

We thank the reviewer for this interesting comment. As our dataset sample contains only two 3T and three 7T datasets we indeed believe there is insufficient power to warrant such an analysis. In addition, we wanted the focus of this paper to be how fMRI examines the SST in general, and not differences between acquisition methods. With a greater number of datasets with different imaging parameters (especially TE or resolution) in addition to field strength, we agree such an analysis would be interesting, although beyond the scope of this article.

(10) The authors evaluate smoothing and it seems that the conclusion that they want to come to is that with a larger smoothing kernel, the results in the stop networks bleed into surrounding areas, producing false positive activity. However, in the absence of a ground truth of the true contributions of these areas, it seems that an alternative interpretation of the results is that the denser maps when using a larger smoothing kernel could be closer to "true" activation, with the maps using a smaller smoothing kernel missing some true activity. It seems worth entertaining these two possible interpretations for the smoothing results unless there is clear reason to conclude that the smoothed results are producing false positive activity. 

We agree with the view of the reviewer on the interpretation of the smoothing results. We indeed cannot rule this out as a possible interpretation of the results, due to a lack of ground truth. We have added text to the article to reflect this view and discuss the types of errors we can expect for both smaller and larger smoothing kernels (page 15).

“In the absence of a ground truth, we are not able to fully justify the use of either larger or smaller kernels to analyse such data. On the one hand, aberrantly large smoothing kernels could lead to false positives in activation profiles, due to bleeding of observed activation into surrounding tissues. On the other side, too little smoothing could lead to false negatives, missing some true activity in surrounding regions. While we cannot concretely validate either choice, it should be noted that there is lower spatial uncertainty in the subcortex compared to the cortex, due to the lower anatomical variability. False positives from smoothing spatially unmatched signal, are more likely than false negatives. It may be more prudent for studies to use a range of smoothing kernels, to assess the robustness of their fMRI activation profiles.”

wow. so if the grantType is authorization code flow type, this parseFromUrl() function actually automatically does an entire extra step which is the POST to get the token.

according to the next paragraph, at least in this example case of okta, we don't need manual access to the random secret generated by frontend code.

code is not assets

but a liability

Reviewer #2 (Public Review):

Summary:

This study takes advantage of multiple methodological advances to perform layer-specific staining of cortical neurons and tracking of their axons to identify the pattern of their projections. This publication offers a mesoscale view of the projection patterns of neurons in the whisker primary and secondary somatosensory cortex. The authors report that, consistent with the literature, the pattern of projection is highly different across cortical layers and subtype, with targets being located around the whole brain. This was tested across 6 different mouse types that expressed a marker in layer 2/3, layer 4, layer 5 (3 sub-types) and layer 6.<br /> Looking more closely at the projections from primary somatosensory cortex into the primary motor cortex, they found that there was a significant spatial clustering of projections from topographically separated neurons across the primary somatosensory cortex. This was true for neurons with cell bodies located across all tested layers/types.

Strengths:

This study successfully looks at the relevant scale to study projection patterns, which is the whole brain. This is achieved thanks to an ambitious combination of mouse lines, immuno-histochemistry, imaging and image processing, which results in a standardized histological pipeline that processes the whole-brain projection patterns of layer-selected neurons of the primary and secondary somatosensory cortex.<br /> This standardization means that comparisons between cell-types projection patterns are possible and that both the large-scale structure of the pattern and the minute details of the intra-areas pattern are available.<br /> This reference dataset and the corresponding analysis code are made available to the research community.

Weaknesses:

One major question raised by this dataset is the risk of missing axons during the post-processing step. Indeed, it appears that the control and training efforts have focused on the risk of false positives (see Figure 1 supplementary panels). And indeed, the risk of overlooking existing axons in the raw fluorescence data id discussed in the article.

Based on the data reported in the article, this is more than a risk. In particular, Figure 2 shows an example Rbp4-L5 mouse where axonal spread seems massive in Hippocampus, while there is no mention of this area in the processed projection data for this mouse line.

Similarily, the Ntsr1-L6CT example shows a striking level of fluorescence in Striatum, that does not reflect in the amount of axons that are detected by the algorithms in the next figures.<br /> These apparent discrepancies may be due to non axonal-specific fluorescence in the samples. In any case, further analysis of such anatomical areas would be useful to consolidate the valuable dataset provided by the article.

https://www.youtube.com/watch?v=KbzqB09ZyJQ

Résumé de la vidéo [00:00:00][^1^][1] - [00:25:15][^2^][2]:

Cette vidéo présente une conférence de Didier Fassin sur la faculté de punir, explorant les pratiques punitives au-delà de leur forme légale et l'impact de la peine d'emprisonnement. Fassin discute des théories de la justice rétributive et utilitariste, et analyse l'extension de la peine, notamment en termes de profondeur de l'affliction et d'élargissement du cercle des affligés.

Points forts: + [00:00:29][^3^][3] La critique de la définition traditionnelle de la peine * Remise en question de la définition par les philosophes et juristes * Focus sur le châtiment pour comprendre les pratiques punitives * Importance de la réalité des pratiques au-delà de la loi + [00:01:54][^4^][4] L'extension de la peine * La peine affecte plus profondément et au-delà de l'intention initiale * Analyse de l'emprisonnement et son impact sur les proches des détenus * Référence aux recherches en sociologie et anthropologie + [00:03:38][^5^][5] L'influence de Cesare Beccaria sur la prison et la peine d'emprisonnement * Discussion sur l'œuvre de Beccaria et son impact sur la réforme pénale * Rejet de la justice rétributive et plaidoyer pour l'utilitarisme * L'importance de la prévention des crimes et de la proportionnalité des peines + [00:21:19][^6^][6] L'histoire de la peine d'emprisonnement en France * Introduction de l'emprisonnement dans le code pénal de 1791 * Évolution des peines et principes de la réforme pénale * Critique de l'adoucissement des peines et de la punition généralisée Résumé de la vidéo [00:25:17][^1^][1] - [00:48:46][^2^][2]:

Cette partie de la vidéo explore l'évolution de la peine d'emprisonnement dans l'histoire française, depuis son introduction dans le code pénal en 1781 jusqu'à son utilisation contemporaine. Elle examine les changements dans la gestion des prisons, les conditions de détention et l'impact sur les détenus et le personnel pénitentiaire.

Points forts: + [00:25:17][^3^][3] Introduction de l'emprisonnement punitif * Remplacement des peines corporelles * Emprisonnement comme sanction ordinaire * Extension progressive de l'empire carcéral + [00:29:00][^4^][4] Privatisation et conditions des prisons * Développement des manufactures carcérales * Main-d'œuvre captive pour les industriels * Dénonciation des abus par des intellectuels + [00:35:00][^5^][5] Perception de la prison par le personnel * Stratégies de défense face à la détresse des détenus * Indifférence cognitive et justification de l'agressivité * Sensibilité de certains membres du personnel + [00:41:00][^6^][6] Confinement et privation de liberté * Confinement dans le confinement * Impact de la surpopulation carcérale * Privation de la vie affective et sexuelle + [00:45:00][^7^][7] Frustrations et privation de dignité * Toutepuissance du personnel et épreuve de l'estime de soi * Fouilles corporelles et atteinte à la dignité * Difficultés liées à la cohabitation forcée Résumé de la vidéo [00:48:48][^1^][1] - [01:03:27][^2^][2]:

Cette partie de la vidéo aborde la faculté de punir et les diverses privations subies par les détenus, allant au-delà de la simple perte de liberté. Elle met en lumière les conditions de vie difficiles en prison, l'impact de l'incarcération sur les proches des détenus et les conséquences sociales plus larges de la politique pénitentiaire.

Points forts: + [00:48:48][^3^][3] Les conditions de détention * Les décisions du tribunal administratif et leur impact * Les restrictions sur les activités quotidiennes comme les douches * La pression exercée par les surveillants + [00:50:07][^4^][4] La privation de sens de la peine * L'absence de prise de conscience du délit commis * Le manque d'opportunités pour la réinsertion sociale et la réforme morale * La description de la prison comme un lieu qui dévalorise la personne + [00:52:17][^5^][5] Le suicide en milieu carcéral * Le taux élevé de suicide en prison en France * Les facteurs contribuant aux suicides, comme le choc de l'incarcération * L'impact des conditions carcérales sur la santé mentale des détenus + [00:55:23][^6^][6] Les répercussions sur les proches des détenus * L'effet de l'incarcération sur les familles et les communautés * Les difficultés rencontrées par les visiteurs pour accéder à la prison * La notion de "châtiment vicariant" affectant les proches des condamnés

Onderliggende gegevens? Python code voor de plot? Misschien wel aardig om ook het 10e en 90e percentiel te geven

This work has been published in GigaByte Journal under a CC-BY 4.0 license (https://doi.org/10.46471/gigabyte.120), and has published the reviews under the same license. This is part of a thematic series presenting Data Releases from the Hong Kong Biodiversity Genomics consortium (https://doi.org/10.46471/GIGABYTE_SERIES_0006). These are as follows.

Reviewer 1. Anton Sonnenberg

Is the language of sufficient quality? Yes.

Are all data available and do they match the descriptions in the paper? Yes.

Is the data acquisition clear, complete and methodologically sound? Yes.

Is there sufficient detail in the methods and data-processing steps to allow reproduction? Yes.

Figure 1E could be improved by eliminating in the pie-chart the non-repeat sequences or bar-plot the repeats. That will visualize better the frequencies of each type of repeats.

Reviewer 2. Riccardo Iacovelli

Is the language of sufficient quality? No.

There are several typos spread across the text, and some sentences are written in an unclear manner. I provide some suggestions in the attachment.

Are all data available and do they match the descriptions in the paper?

Yes, but some of the data shown is rather unclear and/or not supported by sufficient explanation. For example, what is actually Fig. 1C showing? Because the reference in the text (which contains a typo, line 197) refers to something else. What is the second set of stats in Fig. 1B? This other organism is not mentioned at all anywhere in the manuscript.

Are the data and metadata consistent with relevant minimum information or reporting standards?

No. NCBI TaxID of the sequenced species object of this work is missing.

Is there sufficient detail in the methods and data-processing steps to allow reproduction?

No. In my opinion, some of the procedures described for the processing of the sample and library prep for sequencing are reported in an unclear way. For example, lines 100-103: no details on RNAse A treatment; how do you define chloroform:IAA (24:1) washes? how much supernatant is added to how much H1 buffer to have the final volume of 6 ml? Another example, lines 180-175: what parameters did you use for EvidenceModeler to generate the final consensus genes model? The weight given to each particular prediction set is important.

Is there sufficient data validation and statistical analyses of data quality?

No/ While sufficient data validation and statistical analyses have been carried out with respect to DNA sequencing and genome assembly, nothing is reported about DNA extraction and quality. The authors mention several times throughout the text that DNA preps are checked via NanoDrop, Qubit, gel electrophoresis, etc. But none of this is shown in the main body or in the supplementary information. Without this information, it is difficult to assess directly the efficacy of DNA extraction and preparation methods. I recommend including this type of data.

Additional Comments:

In this article, the authors report the first whole genome assembly of Dacryopinax spathularia, an edible mushroom-forming fungus that is used in the food industry to produce natural preservatives. In general, I find the data of sufficiently high quality for release, and I do agree with the authors in that it will prove useful to gain further insights into the ecology of the fungus, and to better understand the genetic basis of its ability to decay wood and produce valuable compounds. This can ultimately lead to discoveries with applications in biotech and other industries.

Nevertheless, during the review process I noticed several shortcomings with respect to unclear language, insufficient description of the experimental procedures and/or results presented, and missing data altogether. These are all discussed within the checklist available in the ReView portal. For minor comments line-by-line, see below:

1: Dacrymycetaceae should be italicized (throughout the whole manuscript). This follows the convention established by The International Code of Nomenclature for algae, fungi, and plants (https://www.iaptglobal.org/icn). Although not binding, this allows easy recognition of taxonomic ranks when reading an article. 49: other fungus -> other fungi 56: photodynamic injury -> UV damage/radiation (photodynamic is used with respect to light-activated therapies etc.) 60: in food industry as natural preservatives in soft drinks -> in food industry to produce natural preservatives for soft drinks 68: cultivated in industry as food additives -> cultivated in industry to produce food additives 69: isolated fungal extract -> the isolated fungal extract 71: What do you mean by Pacific? It’s unclear 71-72: the genomic resource -> genomic data/ genome sequence 72: I would remove “with translational values”, it is very vague and does not add anything to the statement 78: genomic resource -> genomic data/ genome sequence 78-81: this could be rephrased in a smoother manner: e.g. something like “the genomic data will be useful to gain a better understanding of the fungus’ ecology as well as the genetic basis of its wood-decaying ability and…” 85: fruit bodies -> fruiting bodies 88-89: Grown hyphae from >2 week-old was transferred  Fungal hyphae from 2-week old colonies were transferred 90-91: validated with the DNA barcode of Translation  assigned by DNA barcoding using the sequence of Translation… 95: ~ -> Approximately (sentences are not usually started with symbols or numbers) 101-3: Procedure is not clear enough (see other comments through ReView portal) 124: for further cleanup the library -> to further clean up the library / for further cleanup of the library 132: as line 95 152: as lines 95, 132 181-5: Insufficient description of methods, see comments through ReView portal 197: Figure and 1C; Table 2 -> Figure 1C and Table 2 200: average protein length of 451 bp -> average protein-coding gene length / average protein length of ~150 amino acids 211: via the fermentation process with applications in the food industry -> via the fermentation process with potential applications in the food industry

As a fungal biologist myself interested in fungal genomics and biotechnology, I would like to thank the authors for carrying out this work and the editor for the opportunity to review it. I am looking forward to reading the revised version of the manuscript.

Riccardo Iacovelli, PhD GRIP, Chemical and Pharmaceutical Biology department University of Groningen, Groningen - The Netherlands

Reviewer #1 (Public Review):

I thank the authors for addressing almost all my comments on the previous version of this manuscript, which studies the representation by gender and name origin of authors from Nature and Springer Nature articles in Nature News.

The representation of author identities is an important step towards equality in science, and the authors found that women are underrepresented in news quotes and mentions with respect to the proportion of women authors.

The research is rigorously conducted. It presents relevant questions and compelling answers. The documentation of the data and methods is thoroughly done, and the authors provide the code and data for reproduction.

Author response:

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

We would like to first thank the Editor as well as the three reviewers for their enthusiasm and conducting another careful evaluation of our manuscript. We appreciate their thoughtful and constructive comments and suggestions. Some concerns regarding experimental design, data analysis, and over-interpretation of our findings still remains unresolved after the initial revision. Here we endeavored to address these remaining concerns through further refinement of our writing, and inclusion of these concerns in the discussion session. We hope our response can better explain the rationale of our experimental design and data interpretation. In addition, we also acknowledge the limitations of our present study, so that it will benefit future investigations into this topic. Our detail responses are provided below.

Reviewer #1 (Public Review):

This study examines whether the human brain uses a hexagonal grid-like representation to navigate in a non-spatial space constructed by competence and trustworthiness. To test this, the authors asked human participants to learn the levels of competence and trustworthiness for six faces by associating them with specific lengths of bar graphs that indicate their levels in each trait. After learning, participants were asked to extrapolate the location from the partially observed morphing bar graphs. Using fMRI, the authors identified brain areas where activity is modulated by the angles of morphing trajectories in six-fold symmetry. The strength of this paper lies in the question it attempts to address. Specifically, the question of whether and how the human brain uses grid-like representations not only for spatial navigation but also for navigating abstract concepts, such as social space, and guiding everyday decision-making. This question is of emerging importance.

I acknowledge the authors' efforts to address the comments received. However, my concerns persist:

Thanks very much again for the re-evaluation and comments. Please find our revision plans to each comment below.

(1) The authors contend that shorter reaction times correlated with increased distances between individuals in social space imply that participants construct and utilize two-dimensional representations. This method is adapted from a previous study by Park et al. Yet, there is a fundamental distinction between the two studies. In the prior work, participants learned relationships between adjacent individuals, receiving feedback on their decisions, akin to learning spatial locations during navigation. This setup leads to two different predictions: If participants rely on memory to infer relationships, recalling more pairs would be necessary for distant individuals than for closer ones. Conversely, if participants can directly gauge distances using a cognitive map, they would estimate distances between far individuals as quickly as for closer ones. Consequently, as the authors suggest, reaction times ought to decrease with increasing decision value, which, in this context, corresponds to distances. However, the current study allowed participants to compare all possible pairs without restricting learning experiences, rendering the application of the same methodology for testing two-dimensional representations inappropriate. In this study, the results could be interpreted as participants not forming and utilizing two-dimensional representations.

We apologize for not being clear enough about our task design, we have made relevant changes in the methodology section in the manuscript to make it clearer. The reviewer’s concern is that participants learned about all the pairs in the comparison task which makes the distance effect invalid. We would like to clarify that during all the memory test tasks (the comparison task, the collect task and the recall task outside and inside scanner), participants never received feedback on whether their responses were correct or not. Therefore, the comparison task in our study is similar to the previous study by Park et al. (2021). Participants do not have access to correct responses for all possible pairs of comparison prior to or during this task, they would need to make inference based on memory retrieval.

(2) The confounding of visual features with the value of social decision-making complicates the interpretation of this study's results. It remains unclear whether the observed grid-like effects are due to visual features or are genuinely indicative of value-based decision-making, as argued by the authors. Contrary to the authors' argument, this issue was not present in the previous study (Constantinescu et al.). In that study, participants associated specific stimuli with the identities of hidden items, but these stimuli were not linked to decision-making values (i.e., no image was considered superior to another). The current study's paradigm is more akin to that of Bao et al., which the authors mention in the context of RSA analysis. Indeed, Bao et al. controlled the length of the bars specifically to address the problem highlighted here. Regrettably, in the current paradigm, this conflation remains inseparable.

We’d like to thank the reviewer for facilitating the discussion on the question of ‘social space’ vs. ‘sensory space’. The task in scanner did not require value-based decision making. It is akin to both the Bao et al. (2019) study and Constantinescu et al. (2016) study in a sense that all three tasks are trying to ask participants to imagine moving along a trajectory in an abstract, non-physical space and the trajectory is grounded in sensory cue. Participants were trained to associate the sensory cue with abstract (social/nonsocial) concepts. We think that the paradigm is a relatively faithful replication of the study by Constantinescu et al. Nonetheless, we agreed that a design similar to Bao et al. (2019) which controls for sensory confounds would be more ideal to address this concern, or adopting a value-based decision-making task in the scanner similar to that by Park et al. (2021), and we have included this limitation in the discussion section.

(3) While the authors have responded to comments in the public review, my concerns noted in the Recommendation section remain unaddressed. As indicated in my recommendations, there are aspects of the authors' methodology and results that I find difficult to comprehend. Resolving these issues is imperative to facilitate an appropriate review in subsequent stages.

Considering that the issues raised in the previous comments remain unresolved, I have retained my earlier comments below for review.

We apologize for not addressing the recommendations properly, please find detailed our response and plans for revision.

I have some comments. I hope that these can help.

(1) While the explanation of Fig.4A-C is lacking in both the main text and figure legend, I am not sure if I understand this finding correctly. Did the authors find the effects of hexagonal modulation in the medial temporal gyrus and lingual gyrus correlate with the individual differences in the extent to which their reaction times were associated with the distances between faces when choosing a better collaborator? If so, I am not sure what argument the authors try to draw from these findings. Do the authors argue that these brain areas show hexagonal modulation, which was not supported in the previous analysis (Fig.3)? What is the level of correlation between these behavioral measures and the grid consistency effects in the vmPFC and EC, where the authors found actual grid-like activity? How do the authors interpret this finding? More importantly, how does this finding associate with other findings and the argument of the study?

We apologize for not being clear enough in the manuscript and we will improve the clarity in our revision. This exploratory analysis reported in Figure 4 aims to use whole-brain analysis to examine: 1) if there is any correlation between the strength of grid-like representation of social value map and behavioral indicators of map-like representation; and 2) if there are any correlation between the strength of grid-like representation of this social value map and participants’ social trait.

To be more specific, for the behavioral indicator, we used the distance effect in the reaction time of the comparison task outside the scanner. We interpreted stronger distance effect as a behavioral index of having better internal map-like representation. We interpreted stronger grid consistency effect as a neural index of better representation of the 2D social space. Therefore, we’d like to see if there exists correlation between behavioral and neural indices of map-like representation.

To achieve this goal, behavioral indicators are entered as covariates in second-level analysis of the GLM testing grid consistency effect (GLM2). Figure3 showed results from GLM2 without the covariates. Figure4 showed results of clusters whose neural indices of map-like representation covaried with that from behavior and survived multiple-comparison correction. Indeed, in these regions, the grid consistency effect was not significant at group level (so not shown in Figure 3). We tried to interpret this finding in our discussion (line 374-289 for temporal lobe correlation, line 395-404 for precuneus correlation).

Finally, we would like to point out that including the covariates in GLM2 did not change results in Figure3, the clusters in Figure3 still survives correction. Meanwhile, these clusters in Figure 3 did not show correlation with behavioral indicators of map-like representation.

Author response image 1.

(2) There are no behavioral results provided. How accurately did participants perform each of the tasks? How are the effects of grid consistency associated with the level of accuracy in the map test?

Why did participants perform the recall task again outside the scanner?

We will endeavor to improve signposting the corresponding figures in the main text. For the behavioral results, we reported the stats in section “Participants construct social value map after associative learning of avatars and corresponding characteristics” in the main text, and the plots are shown in Figure 1. Particularly, figure 1F showed accuracy of tasks in training, as well as the recall task in the scanner. For the correlation, we did not find significant correlation between behavioural accuracy and grid consistency effect. We will make it clearer in the result section.

(3) The methods did not explain how the grid orientation was estimated and what the regressors were in GLM2. I don't think equations 2 and 3 are quite right.

For the grid orientation estimation method, we provided detailed description in the Supplementary methods 2.2.2. We will add links to this section in the main text.

Equation 2 and 3 describes how the parametric regressors entered into GLM2 were formed and provided prerequisites on calculation of grid orientations. Equation 2 was the results of directly applying the angle addition and subtraction theorems so they should be correct. We will try to make the rationale clearer in the supplementary text.

(4) With the increase in navigation distances, more grid cells would activate. Therefore, in theory, the activity in the entorhinal cortex should increase with the Euclidean distances, which has not been found here. I wonder if there was enough variability in the Euclidean distances that can be captured by neural correlates. This would require including the distributions of Euclidean distances according to their trajectory angles. Regarding how Fig.1E is generated, I don't understand what this heat map indicates. Additionally, it needs to be confirmed if the grid effects remain while controlling for the Euclidean distances of navigation trajectories.

We did not specifically control for the trajectory length, we only controlled for the distribution of trajectory to be uniform. We have included a figure of the distribution of Euclidean distances in Figure S9 and the distribution of trajectory direction in Figure S8.

Author response image 2.

As for Figure 1E, we aim to reproduce the findings from Figure 1F in Constantinescu et al. (2016) where they showed that participants progressively refined the locations of the outcomes through training. We divided the space into 15×15 subregions and computed the amount of time spent in each subregion and plotted Figure 1E. Brighter color in Figure 1E indicate greater amount of time spent in the corresponding subregion. Note that all these timing indices were computed as a percentage of the total time spent in the explore task in a given session. If participants were well-acquainted with the space and avatars, they would spend more time at the avatar (brighter color in avatar locations) in the review session compared to the learning session.

As for the effect of distances on grid-like representation, we did not include the distance as a parametric modulator in grid consistency effect GLM (GLM2) due to insufficient trials in each bin (6-8 trials). But there is side evidence that could potentially rule out this confound. In the distance representation analysis, we did not find distance representation in any of the clusters that have significant grid-like representation (regions in Figure 2).

Reviewer #2 (Public Review):

Summary:

In this work, Liang et al. investigate whether an abstract social space is neurally represented by a grid-like code. They trained participants to 'navigate' around a two-dimensional space of social agents characterized by the traits warmth and competence, then measured neural activity as participants imagined navigating through this space. The primary neural analysis consisted of three procedures: 1) identifying brain regions exhibiting the hexagonal modulation characteristic of a grid-like code, 2) estimating the orientation of each region's grid, and 3) testing whether the strength of the univariate neural signal increases when a participant is navigating in a direction aligned with the grid, compared to a direction that is misaligned with the grid. From these analyses, the authors find the clearest evidence of a grid-like code in the prefrontal cortex and weaker evidence in the entorhinal cortex.

Strengths:

The work demonstrates the existence of a grid-like neural code for a socially-relevant task, providing evidence that such coding schemes may be relevant for a variety of two-dimensional task spaces.

Weaknesses:

In the revised manuscript, the authors soften their claims about finding a grid code in the entorhinal cortex and provide additional caveats about limitations in their findings. It seems that the authors and reviewers are in agreement about the following weaknesses, which were part of my original review: Claims about a grid code in the entorhinal cortex are not well-supported by the analyses presented. The whole-brain analysis does not suggest that the entorhinal cortex exhibits hexagonal modulation; the strength of the entorhinal BOLD signal does not track the putative alignment of the grid code there; multivariate analyses do not reveal any evidence of a grid-like representational geometry.

In the authors' response to reviews, they provide additional clarification about their exploratory analyses examining whether behavior (i.e., reaction times) and individual difference measures (i.e., social anxiety and avoidance) can be predicted by the hexagonal modulation strength in some region X, conditional on region X having a similar estimated grid alignment with some other region Y. My guess is that readers would find it useful if some of this language were included in the main text, especially with regard to an explanation regarding the rationale for these exploratory studies.

Thank you very much again for your careful re-evaluation and suggestions. We have tried to improve our writing and incorporate the suggestions in the new revision.

Reviewer #3 (Public Review):

Liang and colleagues set out to test whether the human brain uses distance and grid-like codes in social knowledge using a design where participants had to navigate in a two-dimensional social space based on competence and warmth during an fMRI scan. They showed that participants were able to navigate the social space and found distance-based codes as well as grid-like codes in various brain regions, and the grid-like code correlated with behavior (reaction times).

On the whole, the experiment is designed appropriately for testing for distant-based and grid-like codes, and is relatively well powered for this type of study, with a large amount of behavioral training per participant. They revealed that a number of brain regions correlated positively or negatively with distance in the social space, and found grid-like codes in the frontal polar cortex and posterior medial entorhinal cortex, the latter in line with prior findings on grid-like activity in entorhinal cortex. The current paper seems quite similar conceptually and in design to previous work, most notably Park et al., 2021, Nature Neuroscience.

(1) The authors claim that this study provides evidence that humans use a spatial / grid code for abstract knowledge like social knowledge.

This data does specifically not add anything new to this argument. As with almost all studies that test for a grid code in a similar "conceptual" space (not only the current study), the problem is that, when the space is not a uniform, square/circular space, and 2-dimensional then there is no reason the code will be perfectly grid like, i.e., show six-fold symmetry. In real world scenarios of social space (as well as navigation, semantic concepts), it must be higher dimensional - or at least more than two dimensional. It is unclear if this generalizes to larger spaces where not all part of the space is relevant. Modelling work from Tim Behrens' lab (e.g., Whittington et al., 2020) and Bradley Love's lab (e.g., Mok & Love, 2019) have shown/argued this to be the case. In experimental work, like in mazes from the Mosers' labs (e.g., Derdikman et al., 2009), or trapezoid environments from the O'Keefe lab (Krupic et al., 2015), there are distortions in mEC cells, and would not pass as grid cells in terms of the six-fold symmetry criterion.

The authors briefly discuss the limitations of this at the very end but do not really say how this speaks to the goal of their study and the claim that social space or knowledge is organized as a grid code and if it is in fact used in the brain in their study and beyond. This issue deserves to be discussed in more depth, possibly referring to prior work that addressed this, and raise the issue for future work to address the problem - or if the authors think it is a problem at all.

Thanks very much again for your careful re-evaluation and comments. We have tried to incorporate some of the suggested papers into our discussion. In summary, we agree that there is more to six-fold symmetric code that can be utilized to represent “conceptual space”. We think that the next step for a stronger claim would be to find the representation of more spontaneous non-spatial maps.

References

Bao, X., Gjorgieva, E., Shanahan, L. K., Howard, J. D., Kahnt, T., & Gottfried, J. A. (2019). Grid-like Neural Representations Support Olfactory Navigation of a Two-Dimensional Odor Space. Neuron, 102(5), 1066-1075 e1065. https://doi.org/10.1016/j.neuron.2019.03.034

Constantinescu, A. O., O'Reilly, J. X., & Behrens, T. E. J. (2016). Organizing conceptual knowledge in humans with a gridlike code. Science, 352(6292), 1464-1468. https://doi.org/10.1126/science.aaf0941

Park, S. A., Miller, D. S., & Boorman, E. D. (2021). Inferences on a multidimensional social hierarchy use a grid-like code. Nat Neurosci, 24(9), 1292-1301. https://doi.org/10.1038/s41593-02100916-3

Reviewer #3 (Public Review):

Liang and colleagues set out to test whether the human brain uses distance and grid-like codes in social knowledge using a design where participants had to navigate in a two-dimensional social space based on competence and warmth during an fMRI scan. They showed that participants were able to navigate the social space and found distance-based codes as well as grid-like codes in various brain regions, and the grid-like code correlated with behavior (reaction times).

On the whole, the experiment is designed appropriately for testing for distant-based and grid-like codes, and is relatively well powered for this type of study, with a large amount of behavioral training per participant. They revealed that a number of brain regions correlated positively or negatively with distance in the social space, and found grid-like codes in the frontal polar cortex and posterior medial entorhinal cortex, the latter in line with prior findings on grid-like activity in entorhinal cortex. The current paper seems quite similar conceptually and in design to previous work, most notably Park et al., 2021, Nature Neuroscience.

(1) The authors claim that this study provides evidence that humans use a spatial / grid code for abstract knowledge like social knowledge.

This data does specifically not add anything new to this argument. As with almost all studies that test for a grid code in a similar "conceptual" space (not only the current study), the problem is that, when the space is not a uniform, square/circular space, and 2-dimensional then there is no reason the code will be perfectly grid like, i.e., show six-fold symmetry. In real world scenarios of social space (as well as navigation, semantic concepts), it must be higher dimensional - or at least more than two dimensional. It is unclear if this generalizes to larger spaces where not all part of the space is relevant. Modelling work from Tim Behrens' lab (e.g., Whittington et al., 2020) and Bradley Love's lab (e.g., Mok & Love, 2019) have shown/argued this to be the case. In experimental work, like in mazes from the Mosers' labs (e.g., Derdikman et al., 2009), or trapezoid environments from the O'Keefe lab (Krupic et al., 2015), there are distortions in mEC cells, and would not pass as grid cells in terms of the six-fold symmetry criterion.

After revision, the authors now discuss some of this and the limitations and notes that future work is required to address the problem.