I don't understand this, because we could still call react-redux's useDispatch to get the store's dispatcher, couldn't we?

yes! definitely! switch case statements would be a good use case. makes code much more readable as well

Webhook?

good that ur main function is short and u make use of helper functions. make ur code easier to read

Example code isn't cheap or quick - no matter how you represent it, this code sets the tone for canonical project use. If it's not properly written then (1) the library should be simple enough to make the canonical usage obvious, so you've messed up, and (2) you should spend more time using your library to understand how to make it both idiomatic and intuitive.

parameters formal and actual

extract a procedure

Esto es equivalente a la zona y por lo tanto se debe codificar como factor.

Smart, I like that reddit explicitly states it will not tolerate the use of its service as a promoter for malware. However, I have seen some sketchy posts on reddit with some questionable links so I don't know how effective it is at moderating this term.

this resonates a lot, also matches what I read in the book <philosophy of software design>, a package / module should be deep, so that it offers something that can really help

optimizing packaging size will improve cold start performance. - use aws sdk v3 - bundle and minify code - avoid top-level import

I was wondering whether this should be done in the module defining and exporting the component, or in the code consuming it.

Given that React.memo could be thought of as a replacement of PureComponent for function components, I think it would be appropriate to have the module export the wrapped version of the component.

This work has been published in GigaByte Journal under a CC-BY 4.0 license (https://doi.org/10.46471/gigabyte.64), and has published the reviews under the same license. These are as follows.

Reviewer 1. Peter Mulhair

Is the language of sufficient quality?

This manuscript is clear and concise. However, there are some issues with consistency in species names used throughout the manuscript. First, on line 99 Eubasilissa regina should be italicised. Secondly, I would recommend after the initial use of the full names of the species (Plodia interpunctella and Eubasilissa regina) that these be referred to as P. interpunctella and E. regina in the rest of the text. There is inconsistent use of full species names, shortened species names and genus name alone which may cause confusion. Please read through and correct these inconsistencies throughout the manuscript text.

Are the data and metadata consistent with relevant minimum information or reporting standards? See GigaDB checklists for examples http://gigadb.org/site/guide

No. Missing items from the metadata checklist include (1) Coding gene annotations (GFF), Coding gene nucleotide sequences and Coding gene translated sequences (fasta) and (2) Full (not summary) BUSCO results output files (text).

Is the data acquisition clear, complete and methodologically sound?

Yes. Is there a specific reason why fifth instar larvae were used for RNA sequencing of silk glands of P. interpunctella? If this stage is biologically important than it may be worth stating why this specific stage is used.

Is there sufficient detail in the methods and data-processing steps to allow reproduction?

Yes. However, the code used for Heavy fibroin gene annotation could be made publicly available to enable reproducibility of this analysis (using other species for example or to annotate other repeat rich genes). This could be uploaded to the rest of the relevant code at https://github.com/AshlynPowell/silk-gene-visualization

Is there sufficient information for others to reuse this dataset or integrate it with other data?

Yes. One point worth making is that on Line 161 you state that "The assembly for E. regina is the most contiguous Trichoptera genome assembly to date.". However, there are currently 3 chromosome level assemblies available for Trichoptera on NCBI. I would recommend removing this statement, or changing it by also pointing to these other genomes available.

Other comments:

This work was carried out to a very high quality and I am particularly happy to see more high quality genomic and transcriptomic data for these groups of insects. I also think that annotation of the Heavy fibroin genes is of particular importance and relevance to researchers interested in silk evolution and evolution and annotation of repeat rich proteins.

Recommendation: Minor revision

Reviewer 2. Reuben W Nowell

Are all data available and do they match the descriptions in the paper?

No. I wasn't able to access the data with the FTP link provided.

Additional comments:

A very nice piece of work, I have only a few minor comments:

• Line 140: "with the k-mer length set to 1" - do you mean 21?
• Line 164: great that you provide a link to the GenomeScope html but I recommend to add these kmer plots as additional supplemental figures, they are extremely useful. Just a screenshot of the GenomeScope plot would be fine.
• Line 164: in relation to the kmer distributions, in fact both plots look a little bit multimodal to me... especially the Eubasilissa, with peaks at 1n (20x), 2n (40x) and 4n (~80x) coverage. This might indicate tetraploidy, which might explain the large increase in genome span and gene number for this species too. You could run OrthoFinder and look at the distribution of OG membership size, for diploid assemblies it peaks at 2, but you might find a peak at 2 and 4 for Eubasilissa if it is tetraploid.
• Line 167: how many contaminant contigs were identified, and where did they come from? - Line 168: the coverage for both species is roughly the same, but the species with the much larger genome is the more contiguous one - any ideas why this is the case?
• Line 184: maybe this is a silly question, but how do you know they are full-length? Based on the B. mori BAC sequence?
• Line 192: a unit for molecular weight, Da?
• Line 224: would be useful to know how many genes are in the Insecta core BUSCO db (i.e., where the 95% comes from).
• Line 233: is there a possibility that RepetModeler has also classified the repeat-rich fibroin genes as 'repeats', and so these are masked in the assemblies?
• Line 243: this is a huge difference in gene number! Why? Is the E. regina assembly actually a diploid assembly? Or ploidy > 2? [See above comment on kmer plots].
• Line 265: "insects have generally been neglected with respect to genome sequencing efforts" - quite a bold statement and I'm not sure I agree, there has been a huge focus on lepidopteran genomics and much of the early sequencing from initiatives such as Darwin Tree of Life have been on insects (also i5k).
• Line 457: Table 2: any idea why the P. interpunctella HiFi assembly is ~60 Mb shorter than the two Illumina assemblies?
• Line 475: Figures 2 and 3: these are nice figures but I don't quite follow what the two coloured panels on the left are showing, specifically, why are there two panels? A bit more clarification in the legend needed perhaps.
• Line 476: N and C capitalised

Recommendation: Minor revision

Reviewer 3. Martin Pippel

Is there sufficient information for others to reuse this dataset or integrate it with other data?

Yes. (partly) : To make the study fully reproducible the authors need to upload the PacBio HiFi data (e.g. to NCBI). Otherwise the genome assemblies cannot be reproduced with the available raw data in GenBank.

Any additional comments:

The manuscript entitled “Long-read HiFi sequencing correctly assembles repetitive heavy fibroin silk genes in new moth and caddisfly genomes” from Kawahara et al. describes the de novo assembly and gene annotation of two silk-producing insect species Plodia interpunctella and Eubasilissa regina. The manuscript is well structured and written. Sequencing data, assemblies and genome annotations are publicly available and can be reused by the scientific community. Both contig assemblies show a very high contiguity and good BUSCO scores. Indeed, several from the 118 P. interpunctella and 53 E. regina contigs show telomere repeat sequence at both ends indicating that those represent full chromosomes. Furthermore, the authors showed that even long repetitive genes such as silk fibroin genes were gapless assembled. I consider the manuscript as a valuable contribution for the scientific community and do only have some minor comments and suggestions:

line 129: - which CCS version was used? line 140: - k-mer length was set to 1? Not 21? line 148: - Typo: obd10 reference endopterygota. - In order to make the Busco scores better comparable to other recent Lepidoptera assemblies it would be better to provide the BUSCO scores for P. interpunctella based on the lepidoptera lineage line 158: CCS data should be added to GenBank as well. Usually the raw data (subreads.bam) is lossy converted into fastq files from NCBI, which makes it impossible to reproduce the consensus step with pbCCS or even the assembly. line 159: Both read coverages are quite high and the heterozygosity rates are with 0.7 (Eubasilissa) and 0.36 (Plodia) high as well. I was wondering if the alternate assemblies were also of a decent quality and if those are published as well? line 265: As of today, there are at least 3 other HiFi assemblies available: (GCA_917563855.2, GCA_929108145.1, GCA_917880885.1) line 457: Table 2 states that E.regina was assembled into 53 contigs. However the assembly available at NCBI GCA_022840565.1 has 123 contigs!?

Definition of "gas" on the blockchain

If you want to reproduce the exact plot you need to run the following code:

           CASchools$D <- CASchools$STR < 20                                   # Create the dummy variable as defined above

    mean.score.for.D.1 <- mean( CASchools$score[ CASchools$D == TRUE  ] )      # Compute the average score when D=1 (low  STR)
    mean.score.for.D.0 <- mean( CASchools$score[ CASchools$D == FALSE ] )      # Compute the average score when D=0 (high STR)



    plot( CASchools$score ~ CASchools$D,                                       # Plot the data

                 pch = 19,                       
                 cex = 0.5,                       
                 col = "Steelblue",                    
                xlab = expression(D[i]),                
                ylab = "Test Score",
                main = "Dummy Regression")

    points( y = mean.score.for.D.0, x = 0,   col="red", pch = 19)               # Add the average for each group
    points( y = mean.score.for.D.1, x = 1,   col="red", pch = 19)

Author Response:

Reviewer #1 (Public Review):

The authors show that the unmitigated generation interval of the original variant of SARS-CoV-2 is longer than originally thought. They argue that in the absence of interventions that limit transmission late in the course of infection, the fraction of transmission events that occur before symptom onset would be considerably lower, and the fraction of transmission events occurring 10 days or more after infection of the index case would be substantially higher.

These findings improve our ability to accurately estimate the basic reproductive number (R0), to evaluate quarantine and isolation policies, and to model counterfactual intervention-free scenarios. Many applied analyses rely on accurate generation interval estimates. To head off confusion, it would be helpful if the authors could provide more comprehensive guidance about which applied analyses should be informed by the unmitigated generation interval, or the observed generation interval. (E.g. the unmitigated interval is useful for quarantine and isolation policies, but would we ever want to use the unmitigated interval to estimate R?).

The unmitigated generation-interval should be used for estimation of the R0 of the initial epidemic phase, but not for the R(t) of the current epidemics. Estimation of R(t) must account for changes in generation-interval distributions caused by the invasion of new variants and changes in behavior. When analyzing policies of quarantine, isolation or contact tracing, the unmitigated interval should also be adopted to account for late transmissions.

We added few sentences at the end of our introduction to clarify this point:

“The estimated unmitigated generation-interval distribution could be adopted for answering questions about quarantine and isolation policy, as well as for estimating the original R0 at the initial spread in China. However, estimation of instantaneous R(t) should account for changes in generation-interval distributions, reflecting mitigation effects and the current variant.”

The analysis estimates a longer generation interval after accounting for three main sources of bias or error that are common in other analyses: 1. Recently infected individuals are intrinsically overrepresented in data on a growing epidemic. Thus, shorter incubation periods and forward serial intervals are more likely to be observed, even in the absence of interventions. This analysis adjusts for these dynamical biases. 2. Interventions or behavioral changes can prevent transmission late in the course of infection. This can shorten the generation and serial intervals over the course of an epidemic. This analysis focuses specifically on transmission pairs observed very early, before the adoption of interventions. 3. The incubation period and generation interval should be correlated - infectors that progress relatively quickly to symptoms should also become infectious sooner (symptom onset occurs near the peak of viral titers). Most existing analyses assume these intervals are uncorrelated, but this analysis accounts for their correlation.

Overall, the conclusions seem reasonable and well-supported. The observation that the generation interval decreases over the course of an epidemic is also consistent with existing studies that show the serial interval has similarly decreased over time. But given the implications of the findings, I hope the authors can address a few questions about potential additional sources of bias:

1. It is somewhat reassuring that the generation interval decreases relatively smoothly as the cutoff date increases (Fig. S6), but it would be helpful if the authors address the potential impact of ascertainment biases. One of the main reasons that the authors estimate a shorter generation interval is that they define January 17th, early in the outbreak before interventions and behavioral changes had taken place, as the cutoff point for the infector's date of symptom onset. This cutoff eliminates biases from interventions, but it also severely limits the size of the transmission-pair dataset (Fig. S3), and focusing on this very early subset of cases may increase the influence of ascertainment bias. Prior to January 17th, should we expect observed transmission pairs to involve more severe cases on average? And is the unmitigated generation interval correlated with case severity?

We thank the reviewer for identifying a source of possible bias that we overlooked. Following the comment we performed a new sensitivity analysis for the inclusion of the severe cases, summarized in Appendix 1—figure 11.

Severity of the cases was reported only in Ali et al.’s data, for some of the individuals. In these cases, individuals are divided into one of three conditions: mild, severe (non-fatal) and death. As non-mild cases represent a small fraction of the dataset, we combine them into one category, which we denote as severe.

Severe cases (including deaths) were overrepresented in the period prior to January 17, with 8 out of 77 cases, compared to 18 out of 745 in the period of January 18-31. The effect of inclusion of severe cases was analyzed by comparing the means of the estimated generation-interval distribution, separately for the two periods in question, using the inference framework with 30 bootstrapping runs. For the earlier period, the estimated means were compared between the dataset with or without the severe cases. For the later period, we also consider the “enriched” dataset, in which severe cases are oversampled for each bootstrap such that the proportion of severe cases matches that during the earlier period (10%). In both cases we see that the effect on the estimated mean generation interval is small.

1. The analysis assumes the incubation period follows a fixed distribution, whose parameterization comes from a meta-analysis of previously estimated incubation periods. But p.5 discusses the idea that observed incubation periods are affected by the same dynamical biases as forward serial intervals, "For example, when the incidence of infection is increasing exponentially, individuals are more likely to have been infected recently. Therefore, a cohort of infectors that developed symptoms at the same time will have shorter incubation periods than their infectees on average, which will, in turn, affect the shape of the forward serial-interval distribution." Has the incubation period been adjusted for these dynamical biases, or should it be?

In our analysis we use the incubation period distribution from Xin et al. 2021 which already considers the backward bias caused by the expanding epidemic with the corrected growth rate of 0.1/d. Xin et al. showed in their meta-analysis that the mean incubation period reported by the various sources changed according to the dates used by the source. Incubation periods prior to the peak of the epidemic in China were lower than ones from after the peak, in a manner that coincided with the backward correction they performed (using a similar derivation to that suggested by Park et al. 2021). Accordingly, the distribution of incubation period they report is the intrinsic incubation period, after correction for the growth rate of the initial spread in China. We added two sentences in our methods section to clarify this point:

“In their meta-analysis, Xin et al. found an increase of the incubation period following the introduction of interventions in China, matching the theoretical framework shown above. Their inferred incubation period distribution includes a correction for the growth rate of the early spread, accordingly.”

Furthermore, we perform a sensitivity analysis for the shape of the incubation period distribution, and show that it has a minor effect on our conclusions (Appendix 1—figure 10).

1. It appears that correlation parameter estimates co-vary with estimates of the mean generation interval (Fig. S6; S13b). Are the authors confident that the correlation parameter is identifiable? How much would the median generation interval estimate in the main analysis change if the correlation parameter had been fixed to 0 (which isn't realistic) or to 0.5 (which might be plausible)?

As the reviewer pointed out, the correlation parameter estimates co-vary with estimates of the mean generation interval. We further analyzed this relation following the comment. The analysis is summarized in supplemental figures S19-20.

We first examine the relation between the mean generation interval and the correlation parameter based on the uncertainty estimates, consisting of 1000 bootstrap runs. Appendix 1—figure 12 shows a joint bivariate scatter plot of the parameters, together with contours of equal probability. As can be seen there is a connection between the parameters. The estimates centered around the maximum likelihood estimate with correlation parameter of 0.75 and mean generation interval of 9.7 days. The confidence interval for the correlation parameter of 0.45-0.95 corresponds to mean generation intervals in the range of 8-11 days, supporting the conclusion of this study.

Next, we reanalyzed the dataset while fixing the correlation parameter, as suggested by the reviewer. Appendix 1—figure 13 shows the estimated mean generation interval for fixed correlation parameters with values of 0, 0.25, 0.5, 0.75, 0.9. For each fixed correlation parameter 100 bootstrapping runs. As can be seen, the results reflect the same connection that can be seen in Appendix 1—figure 12, with probable values in the range of 8-11 days, for correlation parameters in the range of 0.5-0.9. Assuming no correlation would cause underestimation of the mean generation interval match previous literature (Hart, Maini, and Thompson 2021; Park et al. 2022).

Reviewer #2 (Public Review):

There have been several estimates of the generation time and serial interval published for SARS-CoV-2, but as the authors note, estimates can be subject to biases including shifted event timing depending on the phase of the epidemic, correlation in characteristics between infector and infectee, and impact of control measures on truncating potential infectiousness. This study, therefore, has several strengths. It first collates data on transmission events from the earliest phase of the COVID-19 pandemic, then makes adjustments for these potential biases to estimate the generation time in absence of control measures, and finally discusses implications for transmission.

Given many subsequent aspects of the COVID-19 pandemic have been defined relative to earlier phases (e.g. relative transmissibility of variants, relative duration of infectiousness), understanding the baseline characteristics of the infection is crucial. I thought this paper makes a useful contribution to this understanding, generating adjusted estimates for infectiousness (which is longer than previous estimates) and corresponding values for the reproduction number (which is remarkably similar to earlier estimates, presumably because of the different sources of bias in the growth rate and generation time distribution somehow end up canceling each other out).

However, there are some weaknesses at present. The study correctly flags several potential sources of bias in estimates, but in making adjustments uses estimates from the literature that themselves could suffer from these biases, e.g. the distribution of incubation period from a 2021 meta-analysis. Although the authors conduct some sensitivity analysis it would be worth including some more explicit consideration of whether they would expect any underlying bias to propagate through their calculations. The authors also conduct some sensitivity analysis around the underlying data (e.g. ordering of transmission pairs), but again it would be useful to know whether there could be systematic biases in these early data. Specifically, the paper references Tsang et al (2020), which highlighted variability in early case definitions - is it possible that early generation times are estimated to be longer because intermediate cases in the transmission chain were more likely to go undetected than later in the epidemic?

We recognize the potential biases in the transmission pairs data. We therefore developed an extensive framework of sensitivity analyses for identifying biases that could substantially affect the results. In the results section and figure 5, we show that the main study result, that the unmitigated generation-interval distribution is longer than previously estimated, is robust to reasonable amounts of ascertainment bias. We discuss this point at length and have added several supplemental figures to support this claim.

As reviewer #3 mentioned, we conducted a sensitivity analysis for the inclusion of the longest serial intervals, to investigate possible effects of missing links in the longest transmission pairs. We also discuss why we think it’s not necessary to explicitly model the short intervals that may be unobserved due to missing links.

“Second, we considered the possibility that long serial intervals may be caused by omission of intermediate infections in multiple chains of transmission, which in turn would lead to overestimation of the mean serial and generation intervals. Thus, we refit our model after removing long serial intervals from the data (by varying the maximum serial interval between 14 and 24 days). We also considered “splitting” these intervals into smaller intervals, but decided this was unnecessarily complex, since several choices would need to be made, and the effects would likely be small compared to the effect of the choice of maximum, since the distribution of the resulting split intervals would not differ sharply from that of the remaining observed intervals in most cases.”

We added to the discussion text regarding the effect of possible bias in the dataset, explicitly specifying the ascertainment bias.

“Our analysis relies on datasets of transmission pairs gathered from previously published studies and thus has several limitations that are difficult to correct for. Transmission pairs data can be prone to incorrect identification of transmission pairs, including the direction of transmission. In particular, presymptomatic transmission can cause infectors to report symptoms after their infectees, making it difficult to identify who infected whom. Data from the early outbreak might also be sensitive to ascertainment and reporting biases which could lead to missing links in transmission pairs, causing serial intervals to appear longer (For example, people who transmit asymptomatically might not be identified). Moreover, when multiple potential infectors are present, an individual who developed symptoms close to when the infectee became infected is more likely to be identified as the infector. These biases might increase the estimated correlation of the incubation period and the period of infectiousness. We have tried to account for these biases by using a bootstrapping approach, in which some data points are omitted in each bootstrap sample. The relatively narrow ranges of uncertainty suggest that the results are not very sensitive to specific transmission pairs data points being included in the analysis. We also performed a sensitivity analysis to address several potential biases such as the duration of the unmitigated transmission period, the inclusion of long serial intervals in the dataset, and the incorrect ordering of transmission pairs (see Methods). The sensitivity analysis shows that although these biases could decrease the inferred mean generation interval, our main conclusions about the long unmitigated generation intervals (high median length and substantial residual transmission after 14 days) remained robust (Figure 5).”

It would also be helpful to have some clarifications about methodology, particularly in how the main results about generation time are subsequently analyzed. For example, estimates such as the conversion of generation time to R0 and VOC scalings are described very briefly, so it is currently unclear exactly how these calculations are being performed.

Following the reviewer comments we made edits to the Methods section in order to make it more readable and clearer. We added subheadings for the various sections. Moreover, we added a section explaining the derivation of the basic reproduction number and clarified the section regarding the VOCs extrapolations.

We made some edits to the methods section in order to make it more accessible and clear, for example, we added subheadings for the various sections, added a section explaining the derivation of the basic reproduction number, and clarified the section regarding the VOCs extrapolations.

Reviewer #3 (Public Review):

Sender & Bar-On et al. perform robust analyses of early SARS-CoV-2 line list data from China to estimate the intrinsic generation interval in the absence of interventions. This is an important topic, as most SARS-CoV-2 data are from periods when transmission-reducing interventions are in place, which will lead to underestimation of the potential infectious period.

The authors highlight two shortcomings in previous approaches. First, the distribution of 'observed' serial intervals (the time between symptom onset in the infector and symptom onset in the infectee) depends not only on the timeline of each infector's infection, but also the epidemic growth rate, which weights the proportion of observed short vs. long serial intervals. The authors argue that by accounting for this weighting, more accurate estimates of the intrinsic generation interval - the metric on which isolation policies are based - can be obtained. Second, the authors find that the original SARS-CoV-2 generation interval distribution has both a higher mean and longer tail than previous estimates when using only data prior to the introduction of interventions. Finally, the authors use publicly available data on viral load trajectories to extrapolate their estimates to other SARS-CoV-2 variants, finding that alpha, delta, and omicron may have shorter generation intervals than original SARS-CoV-2. These findings are important, as case isolation policies are based on assumptions for how long individuals remain infectious. More broadly, these methods will be important for future work to correctly estimate generation intervals in other outbreaks.

The conclusions are well supported by the data, and a suite of sensitivity analyses give confidence that the findings are robust to deviations from many of the key assumptions. The code is well documented and publicly available, and thus the findings are easily reproducible. Key strengths of the paper include the clarity and rigor of the modeling methods, and the exhaustive consideration of potential biases and corresponding sensitivity analyses - it is very difficult to think of potential biases that the authors have not already considered! I think this is a well-written and well-executed study. The work is likely to be impactful for reconsidering SARS-CoV-2 isolation policies and revisiting generation interval estimates from other data sources. I also expect this to be a key reference and method for future studies estimating the generation interval.

I have some minor comments on potential weaknesses and interpretation:

1. Uncertainty in early generation interval estimates. One of the conclusions is that the estimated mean generation interval is longer than the observed mean serial interval. However, this conclusion does not seem justified given that the observed mean serial interval (9.1 days) is well within the 95% CI of 8.3-11.2 days for the mean generation interval. The confidence intervals for the serial interval in figure 2 are also wide for pre-Jan 17th (though presumably these would be reduced if all pre-Jan 17th serial intervals were combined). Further, only 77 of the ~1000 transmission pairs are actually from pre-January 17th. The actual sample size used for these estimates is much smaller than suggested by Figure S1 and thus this should be made clear. Therefore, although the intuition for why observed serial intervals may differ from the generation interval is correct, I do not think that the data alone demonstrate this. A related issue is on ascertainment bias - could the early serial interval data be biased longer because ascertainment is initially poor and thus more intermediate infectors are missed? The authors consider removing particularly long serial intervals to try and account for this, but that does not deal with e.g. chains of multiple short serial intervals being incorrectly recorded as a single long serial interval (but still within 16 days).

We agree with the reviewer that due the large uncertainty we cannot deduce that the mean generation interval is longer than the mean serial interval. We changed the phrasing to emphasize this statement is supported by mathematical theory.

“We note that our estimated mean generation-interval is longer than the observed mean serial-interval (9.1 days) of the period in question. This is supported by the theory (Park et al. 2021) of the dynamical effects of the epidemic -- in contrast to the common assumption that the mean generation and serial intervals are identical. During the exponential growth phase, the mean incubation period of the infectors is expected to be shorter than the mean incubation period of the infectee - this effect causes the mean forward serial interval to become longer than the mean forward generation interval of the cohorts that developed symptoms during the study period. However, these cohorts of infectors with short incubation periods will also have short forward generation (and therefore serial) intervals due to their correlations. When the latter effect is stronger, the mean forward serial interval becomes shorter than the mean intrinsic generation interval, as these findings suggest.“

Following the comment, we added to Figure S1 the filtering according to date, to reflect the true sample size we use for the main analysis (We renamed it: Appendix 1—figure 1).

We recognize the potential biases in the transmission pairs data. We therefore developed an extensive framework of sensitivity analyses for identifying biases that could substantially affect the results. In the results section and figure 5, we show that the main study result, that the unmitigated generation-interval distribution is longer than previously estimated, is robust to reasonable amounts of ascertainment bias. We discuss this point at length and have added several supplemental figures to support this claim.

As reviewer #3 mentioned, we conducted a sensitivity analysis for the inclusion of the longest serial intervals, to investigate possible effects of missing links in the longest transmission pairs. We also discuss why we think it’s not necessary to explicitly model the short intervals that may be unobserved due to missing links.

“Second, we considered the possibility that long serial intervals may be caused by omission of intermediate infections in multiple chains of transmission, which in turn would lead to overestimation of the mean serial and generation intervals. Thus, we refit our model after removing long serial intervals from the data (by varying the maximum serial interval between 14 and 24 days). We also considered “splitting” these intervals into smaller intervals, but decided this was unnecessarily complex, since several choices would need to be made, and the effects would likely be small compared to the effect of the choice of maximum, since the distribution of the resulting split intervals would not differ sharply from that of the remaining observed intervals in most cases.”

We added to the discussion text regarding the effect of possible bias in the dataset, explicitly specifying the ascertainment bias.

“Our analysis relies on datasets of transmission pairs gathered from previously published studies and thus has several limitations that are difficult to correct for. Transmission pairs data can be prone to incorrect identification of transmission pairs, including the direction of transmission. In particular, presymptomatic transmission can cause infectors to report symptoms after their infectees, making it difficult to identify who infected whom. Data from the early outbreak might also be sensitive to ascertainment and reporting biases which could lead to missing links in transmission pairs, causing serial intervals to appear longer (For example, people who transmit asymptomatically might not be identified). Moreover, when multiple potential infectors are present, an individual who developed symptoms close to when the infectee became infected is more likely to be identified as the infector. These biases might increase the estimated correlation of the incubation period and the period of infectiousness. We have tried to account for these biases by using a bootstrapping approach, in which some data points are omitted in each bootstrap sample. The relatively narrow ranges of uncertainty suggest that the results are not very sensitive to specific transmission pairs data points being included in the analysis. We also performed a sensitivity analysis to address several potential biases such as the duration of the unmitigated transmission period, the inclusion of long serial intervals in the dataset, and the incorrect ordering of transmission pairs (see Methods). The sensitivity analysis shows that although these biases could decrease the inferred mean generation interval, our main conclusions about the long unmitigated generation intervals (high median length and substantial residual transmission after 14 days) remained robust (Figure 5).”

1. Frailty of using viral loads to extrapolate generation intervals. The authors take the observation that variants of concern demonstrate faster viral clearance on average to estimate shorter generation intervals for alpha, delta, and omicron. The authors rightly point out in the discussion that using viral load as a proxy for infectiousness has many limitations. I would emphasize even further that it is very difficult to extrapolate from viral load data in this way, as infectiousness appears to vary far more between variants than can be explained by duration positive or peak viral load. Other factors are potentially at play, such as compartmentalization in the respiratory tract, aerosolization, receptor binding, immunity, etc. Further, there is considerable individual-level variation in viral trajectories and thus the use of a population-mean model overlooks a key component of SARS-CoV-2 infection dynamics. An important reference, which came out recently and thus makes sense to have been missed from the initial submission, is Puhach et al. Nature Medicine 2022 https://doi.org/10.1038/s41591-022-01816-0.

We agree with the reviewer about the frailty of using viral loads to extrapolate generation intervals. We therefore expanded our discussion of the limitation of using viral load data for inferring infectiousness including many of the points mentioned by the reviewer. We use viral load data in the most minimal way to try to enable some discussion of new VOC, and try to emphasize the needed caution.

Viral load trajectories data have potential for informing estimates of the infectiousness profile. However the relationship between viral load, culture positivity, symptom onset, and infectivity is complex and not well characterized. Due to this limitation we tried to use viral loads in a more limited way, extrapolating our results to variants of concerns (which lack unmitigated transmission data). Following the comment, we added a detailed discussion of the limitations of using viral loads as a proxy for infectiousness, including the variation of viral loads across individuals. We also added supplementary figures (Figure 6—figure supplements 1-2) to show the possible effect of an individual's viral loads in relation to the infectiousness and for comparison with new viral load and culture results (Chu et al. 2022; Killingley et al. 2022). As the viral load trajectories data for the different VOC is given only as a function of time from the onset of symptoms, it is not possible to directly link it to the fraction of transmission post 14 days from infection. We made changes to Figure 6 to clarify the possible connection of viral load with the TOST (time from symptoms onset to transmission) distribution and the resulting extrapolation to the unmitigated generation-interval distributions.

“SARS-CoV-2 viral load trajectories serve an important role in understanding the dynamics of the disease and modeling its infectiousness (Quilty et al. 2021; Cleary et al. 2021). Indeed, the general shapes of the mean viral load trajectories and culture positivity, based on longitudinal studies, are comparable with our estimated unmitigated infectiousness profile (Figure 6—figure supplements 1-2, comparison with (Chu et al. 2022; Killingley et al. 2022; Kissler et al. 2021)). However, the nature of the relationship between viral load, culture positivity, symptom onset, and real-world infectivity is complex and not well characterized. Therefore, the ability to infer infectiousness from viral load data is very limited, especially near the tail of infectiousness, several days following symptom onset and peak viral loads. Viral load models are usually made to fit the measurements during an initial exponential clearance phase and in many cases miss a later slow decay (Kissler et al. 2021). Furthermore, there is considerable individual-level variation in viral trajectories that isn’t accounted for in population-mean models (Kissler et al. 2021; Singanayagam et al. 2021). Other factors limiting the ability to compare generation-interval estimates with viral loads models are the variability of the incubation periods and its relation to the timing of the peak of the viral loads, and the great uncertainty and apparent non-linearity of the relation between viral loads and culture positivity (Jaafar et al. 2021; Jones et al. 2021). Due to these caveats and in order to avoid over interpretation of viral load data, we restrict our extrapolation of new VOCs’ infectiousness to a single parameter characterizing the viral duration of clearance.”

We also edited another paragraph in the discussion:

“Our extrapolations are necessarily crude given the complex relationship between viral load, symptomaticity, and infectiousness discussed above. Moreover, compartmentalization in the respiratory tract, aerosolization, receptor binding affinity, and immune history can also play important roles in determining the infectiousness profiles of SARS-CoV-2 variants (Puhach et al. ). ”

1. Lack of validation with other datasets This study hinges on data from a single setting in a short window of time. Although the data are from multiple publications, the fact that so many reported the same transmission pair data demonstrates that these are overlapping datasets. As the authors note, there are potential biases e.g., ascertainment rates and behavioral changes which will impact the generation interval estimates. Thus, generalizability to other settings is limited.

We agree with the reviewer that the dataset used in our study is limited, and consists of overlapping transmission pairs. We perform some analysis of the possible bias caused by inclusion of each dataset, as can be seen in Appendix 1—figure 4.

The best validation would have been a comparison with another independent dataset from the early spread of the epidemic, but no such dataset exists. We added a sentence to the discussion to emphasize this point.

“Due to the nature of early spread of a new unknown disease it is nearly impossible to find two completely unrelated datasets from the period prior to mitigation, limiting the ability of further validation of the current results.”

1. The impact of epidemic dynamics on infector vs. infectee serial intervals. It took me a long time to get my head around the assertion that the forward serial interval distribution will be longer during epidemic growth due to the overrepresentation of short incubation periods among infectors relative to infectees. A supplementary figure, similar to the way Figure 1 is laid out, to illustrate this concept may go a long way to aid the reader's understanding.

We added an explanation to the paragraph in order to make it clearer:

“A cohort of individuals that develop symptoms on a given day is a sample of all individuals who have been previously infected. When the incidence of infection is increasing, recently infected individuals represent a bigger fraction of this population and thus are over-represented in this cohort. Therefore, we are more likely to encounter infected individuals with a short incubation period in this cohort compared to an unbiased sample. The forward serial-interval is calculated for a cohort of infectors who developed symptoms at the same time and therefore is sensitive to this bias. These dynamical biases are demonstrated using epidemic simulations by Park et al."

1. Simulations to illustrate concepts and power Given the assertion that observed serial intervals will depend on epidemic growth rates, reporting, and timing of interventions, I think a simple simulation to illustrate some of these ideas would be very helpful. For example, a simple agent-based model with simulated infectivity profiles and incubation periods using the estimated bivariate distribution would be extremely helpful in illustrating how serial intervals and estimates of the generation interval can differ from the true intrinsic generation interval (I coded such a simulation to help me understand this paper in a couple of hours with <100 lines of R code, so I do not think this would be much work). This would also be very helpful for illustrating statistical power re. comment 1.

The current paper is based on a strong theoretical foundation provided by previous works, specifically Park et al. 2021, which used simulations similar to the reviewer’s suggestions to demonstrate the dynamical biases. We now mention these simulations somewhere in the introduction section:

“These dynamical biases are demonstrated using epidemic simulations by Park et al."

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what? so almost half of MathQA has wrong answers??

Author Response

Reviewer #1 (Public Review):

The largest point of improvement that I expect will unfold over this project's development lifecycle will be its documentation.”

This is indeed one of the biggest source code issues. In the next version, we plan to improve the source code documentation, add more examples and also some small HOWTOs for the RasPi setup.

Reviewer #2 (Public Review):

The Design section then introduces the actor model, the C++ library SObjectivizer used to implement it, and the binary message protocol used for transmission of data across nodes. As currently written, however, this section seems overly technical and hard to grasp for readers who might be interested in experimental neuroscience, but who lack the expertise to understand all mentioned functional constructs and required expertise in the C++ language. Several concepts are mentioned only in passing and without introductory references for the non-expert reader. The level of detail also seems to distract from conveying a more meaningful understanding of the remaining trade-offs involved between network communication, latency, synchronization, and bandwidth.

We wanted to briefly describe why the actor model was used and how it addresses the problem of multithreading programming. We think most of the concepts should be understandable even without prior C++ knowledge. This is also why these concepts are only described briefly. For a more in-depth look e.g. the SObjectizer has a detailed documentation.

The essence of the actor-model could probably be captured more succinctly, and more time spent discussing some of these critical decisions underlying LabNet's design principles. For example, although each Raspberry Pi device runs a LabNet server, the current implementation allows only one client connection per node. This might be surprising for some readers as it excludes a large number of possible network topologies, and the reason presented for the design decision as currently detailed is hard to understand without further clarification.

We have removed some unnecessary details about the actor model. In the beginning of the Design section we now describe more in depth why LabNet was designed as a distributed system and why this results in only one connection per node. The hardware low cost made also us prefer simplicity over more complex hardware topologies.

The main method for evaluating the performance of LabNet is a series of performance tests in the Raspberry Pi comparing clients written in C++, C# and Python, followed by a series of benchmarks comparing LabNet against other established hardware control platforms. While these are undoubtfully useful, especially the latter, the use of benchmarking methods as described in the paper should be carefully revisited, as there are a number of possible confounding factors.

For example, in the performance tests comparing clients written in C++, C# and Python, the Python implementation is running synchronously and directly on top of the low-level interface with system sockets, while the C++ and C# versions use complex, concurrent frameworks designed for resilience and scalability. This difference alone could easily skew the Python results in the simplistic benchmarks presented in the paper, which can leave the reader skeptical about all the comparisons with Python in Figure 3. Similarly, the complex nature of available frameworks also raises questions about the comparison between C# and C++. I don't think it is fair to say that Figure 3 is really comparing languages, as much as specific frameworks. In general, comparing the performance of languages themselves for any task, especially compiled languages, is a very difficult topic that I would generally avoid, especially when targeting a more general, non-technical audience.

This is true; comparisons between different languages are always difficult. This is now explicitly addressed in the text. However, since the implementations in C++, C# and Python were so close in all tests, this is more a demonstration then a comparison: the language and framework at the client side is not really important, at least for the simple cases considered here

The second set of benchmarks comparing LabNet to other established hardware control platforms is much more interesting, but it doesn't currently seem to allow a fair assessment of the different systems. Specifically, from the authors' description of the benchmarking procedure, it doesn't seem like the same task was used to generate the different latency numbers presented, and the values seem to have been mostly extracted from each of the platform's published results. This unfortunately reduces the value of the benchmarks in the sense that it is unclear what conditions are really being compared. For example, while the numbers for pyControl and Bpod seem to be reporting the activation of simple digital input and output lines, the latency presented for Autopilot uses as reference the start of a sound waveform on a stereo headphone jack. Audio DSP requires specialized hardware in the Pi which is likely to intrinsically introduce higher latency versus simply toggling a digital line, so it is not clear whether these scenarios are really comparable. Similarly, the numbers for Whisker and Bpod being presented without any variance make it hard to interpret the results.

We also saw this as a problem. Therefore, all tests were resigned and repeated. Now all platforms were subjected to the same test (with the exception of Whisker, where we did not have suitable hardware available). In this way we now have comparable measurements for all platforms.

One of the stated aims of LabNet was to provide a system where implementing new functionality extensions would be as simple as possible. This is another aspect of experimental neuroscience that is under active discussion and where more contributions are very much needed. Surprisingly, this topic receives very little attention in the paper itself. It is not clear whether the actor model is by itself supposed to make the implementation of new functionality easier, but if this is the case, this is not obvious from the way the design and evaluation sections are currently written, especially given the choice of language being C++.

One of the reasons behind the choice of Python for other hardware platforms such as pyControl and Autopilot is the growing familiarity and prevalence of Python within the neuroscience research community, which might assist researchers in implementing new functionality. Other open-hardware projects in neuroscience allowing for community extensions in C++ such as Open-Ephys have informally expressed the difficulty of the C++ language as a point of friction. I feel that the aim of "ease of extensibility" should merit much more discussion in any future revision of the paper.

Indeed, they only mention in passing that user extensibility is in the conclusion where it is stated that it is not currently possible to modify LabNet without directly modifying and recompiling the entire code base. A software plug-in system is suggested, and indeed this would be extremely beneficial in achieving the second stated aim.

With the simplicity of implementing new functionality, we rather meant the simplicity to adapt the LabNet source code to new requirements. For which the modularization and the use of the actor model is responsible. This is now explained more explicitly in the text. And yes, a plug-in system is on our roadmap but not a part of LabNet yet.

Finally, a set of example experimental applications would have been extremely useful to ground the design of LabNet in practical terms, in addition to the example listings. Even in diagrammatic form, describing how specific experiments have been powered by LabNet would give readers a better sense of the kind of designs that might be currently more appropriate for this platform. For example, video is being increasingly used in behavioral experiments, and Raspberry Pi drivers are available for several camera models, but this important aspect is not mentioned at all in the discussion, so readers interested in video would not know from reading this paper whether LabNet would be appropriate for their goals.

The section "Example" actually shows how a simple experiment can be realized with LabNet. Listings 1-3 are also responsible for this.

LabNet does not support video acquisition in the current version. Even though this video transmission would be quite easy to implement. Nevertheless, we have not needed this in our experiments so far.

As the manuscript currently stands, I don't feel the authors have achieved their second stated aim, and I am unfortunately not fully convinced that the experimental results are adequate to demonstrate the achievement of the first aim. I fully agree, however, that a robust, high-performance and flexible hardware layer for combining neuroscience instruments is desperately needed, and so I do expect that a more thorough treatment of the methods developed in LabNet will in the future have a very positive impact on the field.

Latency measurements are indeed very important, also because in this way a comparison with other tools can be achieved. With the test redesign and an own implementation for each tool the comparability is now a given. Of course, LabNet cannot beat Bpod. After all, Bpod is running on a microcontroller and LabNet has to send all commands via Ethernet. But the results are still very good. The stress test also demonstrates the scalability of LabNet. Above all, LabNet offers the possibility to control many systems at the same time, which cannot be done with other tools, or only in a complicated way.

Path Parameter heading to appear after the code sample block

Code Sample to appear above Request Parameters heading. Refer - https://betasite.razorpay.com/docs/razorpay/invoices-api-revamp/api/orders#create-an-order

Alternative code:

               X <- runif(50, min = -5, max = 5)                                         # simulate the data 
               u <- rnorm(50, sd = 1)  
               Y <- X^2 + 2*X + u                                                        # the true relation, which is the true population regression equation

      mod_simple <- lm( Y ~ X )                                                          # estimate a simple but incorrect regression model

   mod_quadratic <- lm( Y ~ X + I(X^2) )                                                 # estimate the correct quadratic regression model

      prediction <- predict( mod_quadratic  , data.frame( X = sort(X) ) )                # predict (Y.hat) using the correct quadratic model



par(mfrow=c(1,3))

        plot( Y ~ X, col = "steelblue", pch = 20, xlab = "X", ylab = "Y")                # plot the results
      abline( mod_simple, col = "red")                                                   #   red line = incorrect linear regression (this violates the first OLS assumption)
       lines( sort(X), prediction )                                                      # black line = correct quadratic regression

        plot( resid(mod_quadratic) ~ X , col = "steelblue", pch = 20, main=c("Quadratic regression","Residuals plotted against X"), ylim=c(-10,15) )
        plot( resid(mod_simple)    ~ X , col = "steelblue", pch = 20, main=c("Simple regression"   ,"Residuals plotted against X"), ylim=c(-10,15) )

Because the compiler is broken into a three-phrase design, the community can engage more an the engineers and work on their respective end without communication clashes

There are 3 parts to a compiler: * Frontend * Optimizer * Backend

Source code as an input

Machine Code as an output

Explicitly obfuscating critical external access information - hitting a database, making a system call, pulling data from another URL - is an anti pattern that hurts the end user.

As a programmer, I need to constantly develop a threat model of the systems I'm combining in my program. Will this database invocation trigger an exception? What about this memory allocation? Can I safely send this packet across the network without disruption?

We need to model not only the actions themselves in our heads, but also two other things: the exceptional behavior that could come from our code and the performance implications of a particular action. If I don't know, then I can't program effectively.

The case can be made that performance doesn't matter until it's profiled, but some operations can be ludicrously inefficient - and those need to be explicitly noted.

i don't really understand this: in z-code thre are tasks that other competitive softwares would need to restart all over again while z-code can do it without restarting...

this model is what actually z-code is and what makes it special

can do the same but much faster

downright frightening.

the ability for a coin to "be held pegged to the USD" based solely on code is frightening, to say the least--this "technique" looks like it could be used on this large set of actual reserve holding coins to topple them to near zero rates also.

after "free as in oil" i dont think we'll ever feel the same about writing the phrase "free as in beer"ever again.

i'm using this as a sort of "first test for hypothes.is commenting." #peggedtowha

Fetch QR Codes

Fetch QR Codes

The type of the QR code

QR code

The letter "c" is caps in some places and not in some places. It is good to keep it consistent.

The table should be placed after the sample. Please check and replace across the doc.

WiFi QR code format

WordPress tip to start loading some CSS and JS files earlier.

Sample code to add to .htaccess: H2PushResource /wp-content/themes/phpied2/style.css H2PushResource /wp-includes/css/dist/block-library/style.min.css?ver=5.4.1 H2PushResource /wp-includes/js/wp-emoji-release.min.js?ver=5.4.1

Author Response

Reviewer 1

Strengths:

This manuscript combines experimental, exploratory, and observational methods to investigate the big question in innovation literature--why do some animals innovate over others, and how information about innovations spread. By combining a variety of methods, the manuscript tackles this question in a number of ways, and finds support for previous work showing that animals can learn about foods via social olfactory inspection (i.e., muzzle to muzzle contact), and also presents data intended to investigate the role of dispersing animals in innovation and information spread.

Using data from a previously-published experiment, the manuscript illustrates how investigators can numerous interesting questions while limiting the disturbances to wild animals. The manuscript's attempt at using exploratory analysis is also exciting, as exploratory analyses provide a useful tool for behavior research-indeed, Tinbergen insisted that behavior must first be described.

Weaknesses:

The manuscript's introduction is a bit unclear as to how the fact that dispersing males may be an important source of information ties to innovations in response to disruptions due to climate change, humans, or new predators, if at all. An introduction regarding the role of dispersed animals in introducing novel behaviors and social transmission would better prepare readers for the questions presented in the manuscript. As it stands now, the manuscript only provides one sentence discussing the theoretical relevance of investigating the role of dispersing animals in innovations.

We have added some information about this to the introduction (lines 66 – 69 and 121-123) and maintain our discussion of it in the discussion.

Additionally, while the manuscript attempts to use exploratory analysis, it does not provide enough theoretical background as to why certain questions were asked while the data were explored. While the discussion provides some background as to the role of dispersing males in innovation, the introduction provides little background, and thus does not properly frame the issue. It is unclear how dispersing males became of interest and why readers should be interested in them. As the manuscript reads now, it may be that dispersing males became interesting only as a result of the exploratory analysis-except that the predictions explicitly mentions dispersing males. Thus, manuscript at present makes it difficult to know if the questions surrounding immigrant males resulted from the exploratory analysis, or was a question the analyses were intended to answer from the beginning. If this question only came out after first reviewing the results, then this needs to be made clear in the introduction. I see no issue with reporting observations that were the result of investigations into earlier results, but it needs to be reported in a way that can be replicated in future research-I need to know the decision process that took place during the data exploration.

We hope this is clearer from our new research aims (lines 125-173)

The manuscript never clearly defines what counts as an immigrant male; presumably, in this species, all adult males in the group should be immigrants, as females are the philopatric sex. Sometimes, the manuscript uses "recently" to modify immigrant males, but doesn't define exactly what counts as recent, except to say that the males that innovated were in their respective groups for fewer than 3 months, but never explains why three months should be an important distinction in adult male tenure.

We realise how we wrote about this previously was not clear and perhaps misleading. We noticed that the males that innovated had been in the group for less than three months. We do not know if this is necessary for them to innovate or not. We also added to the discussion a description of the male in AK19 who had been in the group for four months and did no innovate – as he had many other traits which we would expect to exclude him from criteria for innovation (e.g. very old, post-prime, and inactive – died within months of the experiment).

Due to the above weaknesses, the provided predictions are a bit murky. It is not clear how variation between groups in accordance with who innovated, or initiated eating a novel food, or demographics is related to the central issue. The manuscript does contribute to the literature by looking at changing rates of muzzle contact over exposure to a novel food source, and provides a good extension of previous findings; that, if muzzle contacts help animals learn about new foods, then rates of muzzle contacts involving novel foods should decrease as animals become familiar with the food. However, this point isn't explicit in the manuscript.

This is now addressed in the new aims paragraph (lines 125-173)

Finally, it is also unclear as to why changing rates of muzzle contact AND whether certain individual level variables like knowledge, sex, age, and/or rank might influence muzzle contacts during opportunities to innovate.

We are not sure exactly what the reviewer means here, but hope that the substantial revisions we have made now address their concern.

As for the methods, the manuscript doesn't provide enough details as to why certain decisions were made. For example, no reason is given as to why only the first four sessions after an animal ate were considered, why the first three months of tenure (but not four, as seen on one group that didn't innovate) was considered to be a critical time for which immigrant males may innovate, why (including the theoretical reasons) the structure of models for one analysis was changed (dropping one variable, adding interactions), or even how the beginning and ending of a trial was decided, despite reporting that durations varied widely,-from 5 minutes to two hours.

Please see: above about the male with 4 month tenure; and top of document for description of our updated models.

The discussion contains results that are never elsewhere presented in the manuscript- (2a) Individual variation in uptake of a novel food according to who ate first).

It was just an error in the sub-title in the discussion – this is now amended. But all the other corresponding details were already there, in the list of research aims in the introduction and in the results as well.

Finally, the largest issue with the manuscript is that its results are not as convincing as the conclusions made. An issue with all the analyses is that some grouping variables in some analyses but not others despite the fact that all of the analyses contain multiple groups (necessitating group as a grouping variable) and multiple observations of the same individuals (i.e., immigrant males tested in multiple groups, necessitating animal identity as a random effect), and not accounting for individual exposure to the experiment when considering whether animals ate the food in the allotted period (an important consideration given the massive differences in trial times), making these results difficult to interpret in their current forms. As for the results regarding muzzle contact, the analyses has a number of issues that make it difficult to determine if the claims are supported. These issues include not explaining why rank calculated a year before the experiments took place was valid or if rank was calculated among all group members or within age and sex classes, not explaining how rank was normalized, and not conducting any kind of formal model comparisons before deciding the best model.

Mostly addressed at top of this document. Regarding rank calculations: rank was not calculated a year before the experiments, it was calculated using a year’s worth of data up to the beginning of the experiments – and ranks were calculated among all group members - we have made this clearer in the methods. We also explained our method of normalisation, and noted that it was an error to include non-normalised rank in one of the models – this has now been rectified

As for the results regarding immigrant males and innovation, little is done to help the fact that these results are from very few observations and no direct analyses. It is possible that something that occurs relatively often but in small sample sizes, like dispersing animals, could have immense power in influencing foraging traditions, and observation is a necessary step in understanding behavior. However, the manuscript doesn't consider any alternative hypotheses as to why it found what it found. No other possible difference between the groups was considered (for example, the groups that rapidly innovated appear to be quite smaller than the groups that did), making the claim that immigrant males were what allowed groups to innovate unconvincing. This is particularly true given that some groups in this study population have experimental histories (though this goes unmentioned in the current manuscript), which likely influenced neophobia-especially given work by the same research group showing that these animals are more curious compared to their unhabituated counterparts.

We have added more discussion of alternative hypotheses to the discussion (line numbers mentioned above).

Regarding the comment about rapid innovation in smaller groups – we are not sure what the reviewer means here – all groups except BD were similar sized. The second largest group, NH, had one of the quickest innovations and a smaller group (KB) innovated only at the third exposure. Unless the reviewer instead refers to the spread of the innovation here? This is also not quite what we see in the data – BD is the largest group and one of the fastest to spread, and KB is the smallest group and the slowest to spread. Regarding groups experimental histories, all the five studied groups have already been used in field experiments. The group (LT) with the least experimental history was the one having the greatest proportion of individuals eating the novel food at the first and over the four exposures (see Fig. 2) while one of the groups with the most experimental history (NH) was one having a smaller proportion of individuals eating the food across the experiment. This is discussed in the discussion (lines 370-380).

Reviewer 2

I have separated my issues with the manuscript into three sub-headings (Conceptual Clarity, Observational Detail and Analysis) below.

1) Conceptual clarity

There are a number of areas where it would greatly benefit the manuscript if the authors were to revisit the text and be more specific in their intentions. At present, the research questions are not always well-defined, making it difficult to determine what the data is intended to communicate. I am confident all of these issues could be fixed with relatively minor changes to the manuscript.

For example, Line 104: Question 1 is not really a question, the authors only state that they will "investigate innovation and extraction of eating the food", which could mean almost anything.

We re-wrote the research questions paragraph and results with this advice in mind – hope it is clearer now. We keep the innovation part just descriptive and hope this is less problematic now.

Question 2a (line 98) is also very vague in it's wording, and I'm left unclear as to what the authors were really interested in or why. This is not helped by Line 104 which refuses to make predictions about this research question because it is "exploratory". Empirical predictions are not simply placing a bet on what we think the results of the study will be, but rather laying out how the results could be for the benefit of the reader. For instance, if testing the effects of 10 different teaching methods on language acquisition-rate: Even if we have no a priori idea of which method will be most effective, we can nevertheless generate competing hypotheses and describe their corresponding predictions. This is a helpful way to justify and set expectations for the specific parameters that will be examined by the methods of the study. In fact, in the current paper, the authors in fact had some very clear a priori expectations going into this study that immigrant males would be vectors of behavioural transmission (clear that is from the rest of the introduction, and the parameters used in their analysis, which were not chosen at random).

We have now updated the whole research aims (lines 125-173).

The multiple references to 'long-lived' species in the abstract (line 16 and introduction (39, 56) is a bit confusing given the focus of this study. Although such categorisations are arbitrary by nature (a vervet is certainly long-lived compared to a dragonfly), I would not typically put vervet monkeys (or marmosets, line 62) in the same category as apes (references 8 and 9) or humans (line 62) in this regard.

When we use “long-lived” in the introduction, we explain that we mean animals with slow generational turnover for whom genetic adaptation is relatively slow – too slow to adapt to very rapid environmental change. Within the distinctions the reviewer makes here, we feel that vervets and marmosets are much more similar to apes than to dragonflies etc. in this respect… and we think making the comparisons that we do are valid in this context (though we do agree that for other reasons we would not find it appropriate). We have modified the sentence in the introduction (line 4042) and hope this is clearer now. The study in reference 9 is about crop-raiding, which is something vervets can learn to do within one generation too. In addition, reference 8 is used as it was one of the earlier and long-standing definitions of innovation which we are using here – we are not comparing vervets to apes directly, but we do not think a different definition of innovation is required.

This contributes a little towards the lack of overall conceptual focus for the manuscript: beginning in this fashion suggests the authors are building a "comparative evolutionary origins" story, hinting perhaps at the phylogenetic relevance of the work to understanding human behaviour, but the final paragraph of the study contextualises the findings only in terms of their relevance to feeding ecology and conservation efforts. I would recommend that the authors think carefully about their intended audience and tailor the text accordingly. This is not to say that readers interested in human evolution will not be interested in conservation efforts, but rather that each of these aspects should be represented in each stage of the manuscript (otherwise - conservationists may not read far into the Introduction, and cultural evolution fans will be left adrift in the Conclusion).

We agree that the line running through the whole paper needed to be clearer and have tried to improve this.

2) Observational detail

There are a number of areas of the manuscript which I found to be lacking in sufficient detail to accurately determine what occurred in these experimental sessions, making the data difficult to interpret overall. All of this additional information ought to be readily available from the methods used (the experiments were observed by 3-5 researchers with video cameras (line 341)) and is all of direct relevance to the research questions set out by the authors.

We added more details about the experiment in the method section.

While I appreciate that it will take quite a bit of work to extract this information, I am certain that it would greatly improve the robustness and explanatory power of this study to do so.

The data on who was first to innovate/demonstrate successful extraction of the food in each group (Question 1) and subsequent uptake (Question 2), as well as the actual mechanism by which that uptake occurred (the authors strongly imply social learning in their Discussion, but this is never directly examined) is difficult to interpret based on the information presented. Some key gaps in the story were:

We did not intend to claim that muzzle contact was the specific mechanism by which individuals learned to extract and eat peanuts – we rather use this experiment to evaluate the function of muzzle contact in the presence of a novel food.

We did not record observation networks in all groups during experiments and cannot obtain accurate ones from all our videos – we hope it is clearer in our text now. Our group’s previous study (Canteloup et al., 2021) already shows social transmission of the opening techniques using data of two of our groups (NH and KB).

• Which/how many individuals encountered the food and in what order? I.e., were migrants/innovators simply the first to notice the food?

No, and we have now added some info about other individuals approaching the box and inspecting the peanuts before innovation took place

• Did any individuals try and fail to extract the food before an "innovator" successfully demonstrated?
• How many tried and failed to extract the nuts before and after observing effective demonstrators?

We have added the number of individuals that inspected the peanuts (visually and with contact)

• Were individuals who observed others interact with the food more likely to approach and/or extract it themselves?
• Did group-members use the same methods of extraction as their 'innovators'?

Yes – this is the topic of Canteloup et al. 2021 – and these data are not presented again here. That study was on two of the groups presented here (KB and NH), and with up to 10 exposures in each of those groups and present a fine-grained analysis of peanuts opening techniques used by monkeys. We hope this is clearer now in the text where we refer to this paper.

• How many tried and succeeded without having directly observed another individual do so (i.e. 'reinvention' as per Tennie et al.)?

For this, and the above points: We did not record an observation network for the groups added in this study and are not able to answer this – it is not the focus of this study. For this reason, we do not make claims in this line in the present study, and are cautious with our social learning related language. Whilst we examine the role of muzzle contact in acquiring information about a novel food, we do not expect this behaviour to be a necessary prerequisite in being able to extract and eat this food – indeed many individuals who learned to eat did not perform muzzle contacts. This aspect of the study is about using this novel food situation to explore whether muzzle contact serves information acquisition – which our evidence suggests it does.

Moreover, the processing of this food is not complex and is similar to natural foods in their environment, and we do expect individuals to be capable of reinventing it easily (and this point with Tennie’s hypothesis is actually discussed in Canteloup et al. 2021 paper) – but the point here is that their natural tendency is to be neophobic to unknown food, and therefore they do not readily eat it until they see a conspecific doing so, after which they do. And we also used this opportunity, though in a very small sample size, to investigate which individuals would overcome that neophobia and be the first to eat successfully.

The connective tissue between the research questions set out by the authors is clearly social learning. In short: the thesis is that Migrants/Innovators bring a novel behaviour to the group, then there is 'uptake' (social learning), which may be influenced by demographic factors and muzzle-contact (biases + mechanisms). Given this focus (e.g. lines 224-264 of the Discussion), I would expect at least some of the details above to be addressed in order to provide robust support for these claims.

See above – the reason we talk about ‘uptake’ rather than social learning is that we really see this as a case of social disinhibition of neophobia, rather than more detailed social learning such as copying or imitation, as it would be in a tool-use setting, for example (though in Canteloup et al. 2021 paper, evidence is found that the specific methods to open peanuts are socially transmitted).

Question 2a (Lines 136-146): This data is hard to interpret without knowing how much of the group was present and visible during these exposures.

Please see response to reviewer 1 on this.

For example: 9% update in NH group does not sound impressive, but if only 10% of the total group were present while the rest were elsewhere, then this is 90% of all present individuals. Meanwhile if 100% of BD group were present and only experienced 31% uptake, then this is quite a striking difference between groups.

Experiments were done at sunrise at monkeys’ sleeping site in AK, LT, NH and KB where most of the group was present in the area; we added more precision on this point in the Method section (lines 615-619).

Of course, there is also an issue of how many individuals can physically engage with the novel food even if they want to - the presence of dominant individuals, steepness of hierarchy within that group, etc, will significantly influence this (and is all of interest with regards to the authors' research questions).

We discuss this with respect to the result showing that higher rank individuals were more likely to extract and eat the food at the first exposure and over all four exposures

Muzzle-contact behaviour: The authors use their data to implicate muzzle-contact in social learning, but this seems a leap from the data presented (some more on this in the Analysis section).

We hope our distinction between information acquisition and information use is clearer now.

For example: - What is the role of kinship in these events?

We did not analyse kinship here, but we see a lot of targeting towards adult males, and we do not have reliable kinship data for them. We also checked (see response to reviewer 3) the muzzle contacts initiated by knowledgeable adult females, and they are mostly towards adult males, not towards related juveniles (see new figure 4D and lines 497-500).

• Did they occur when the juvenile had free access to the food (i.e. not likely to be chased off by a feeding adult)?

We recorded muzzle contacts visible within 2m of the box, so individuals were not necessarily eating at the box at the time of engaging in muzzle contacts. However, the majority of muzzle contacts that we could record took place directly at the edge of the box – at the location where the food is accessed – so an individual would not likely be if they were not able to have access to the food. It is possible they could be there and not eating, but they would not have been chased off, otherwise they would not be able to engage in muzzle contacts there. But it is not entirely clear what the reviewer’s point is here.

• Did they primarily occur when adults had a mouthful of food? (i.e. could it simply be attempted pilfering/begging)

This is not typical of this species. Very few specific individuals remove food from others’ mouths, and they do it with their hands, usually beginning with grooming their face and cheekpouches, before prising their mouth open and removing food from the victim’s cheekpouches

• What proportion of PRESENT (not total) individuals were naïve and knowledgeable in each group for each trial (if 90% present were knowledgeable, then it is not surprising that they would be targeted more often)?

We agree somewhat with this statement, but given the multiple ways we show the effect of knowledge – both at the individual level and the group level (effect of exposure number i.e. overall group familiarity) – we feel we present enough evidence to establish the link between knowledge of the food and muzzle contacts. We find that the model showing the interaction between exposure number and number of monkeys eating on the overall rate of muzzle contacts actually addresses this issue, because we see that when many monkeys are eating during later exposures, when many were indeed knowledgeable, the rate of muzzle contacts is massively decreased. Moreover, if 90% of the individuals present are knowledgeable, then only 10% of the individuals present are naïve, and we show both that knowledgeable individuals are targeted, but also that naïve individuals are initiators.

• Did these events ever lead to food-sharing (In other words, how likely are they to simply be begging events)?

We do not observe food-sharing in vervets.

• Did muzzle-contact quantifiably LEAD to successful extraction of the food? If the authors wish to implicate muzzle-contact in social learning, it is not sufficient to show that naïve individuals were more likely to make muzzle-contact, they must also show that naïve individuals who made more muzzlecontact were more likely to learn the target behaviour.

We disagree here, because there is a distinction between information acquisition and information use - obtaining olfactory information about a novel resource that conspecifics are eating is not the same as learning a complex tool use behaviour for which detailed observation of a model is required. We are not claiming that that muzzle contact is THE mechanism by which the monkeys learn how to eat the food – but we do believe that the clear separation between naïve individuals initiating and knowledgeable individuals being target, and the decrease of the rate of this behaviour as groups’ familiarity with the food increases – is good evidence that this behaviour functions to acquire information about a novel food.

3) Analysis

There are a number of issues with the current analysis which I strongly recommend be addressed before publication. Some of these are likely to simply require additional details inserted to the manuscript, whereas others would require more substantial changes. I begin with two general points (A & B), before addressing specific sections of the manuscript.

A) My primary issue with each of the analyses in this manuscript is that the authors have fit complex statistical models for each of their analyses with no steps to ascertain whether these models are a good fit for the data. With a relatively small dataset and a very large number of fixed effects and interactions, there is a considerable risk of overfitting. This is likely to be especially problematic when predictor variables are likely to be intercorrelated (age, sex and rank in the case of this analysis).

We have now checked for overfitting in our models.

The most straightforward way to resolve this issue is to take a model-comparison approach. Fitting either a) a full suite of models (including a 'null' model) with each possible permutation of fixed effects and interactions (since the authors argue their analysis is exploratory) or b) a smaller set of models which the authors find plausible based on their a priori understanding of the study system. These models could then be compared using information criterion to determine which structure provides the best out-of-sample predictive fit for the data, and the outputs of this model interpreted. Alternatively, a model-averaging approach can be taken, where the effects of each individual predictor are averaged and weighted across all models in the set. Both of these approaches can be performed easily using the r package 'MuMIn'. There are also a number of tutorials that can be found online for understanding and carrying out these approaches.

Please see our answer at the beginning of the document, detailing how we have updated our models.

B) It does not seem that interobserver reliability testing was carried out on any of the data used in these analyses. This is a major oversight which should be addressed before publication (or indeed any re-analysis of the data).

We have added this now and mention it above already.

Line 444: Much more detail is needed here. What, precisely, was the outcome measure? Was collinearity of predictors assessed? (I would expect Age + Rank to be correlated, as well as Sex + Rank).

This is now addressed (please see details above) – we use VIFs to assess multicollinearity of predictors in our models and find they are all satisfactory (see R code).

Line 452. A few comments on this muzzle-contact analysis:

The comments below are a little confusing as some seem to refer to the muzzle-contact rate model (previously line number 452), and some seem to refer to the initiator/receiver model. We have tried to figure out which comments refer to which, and answer accordingly.

"We investigated muzzle contact behaviour in groups where large proportions of the groups started to extract and eat peanuts over the first four exposures"

What was the criteria for "a large proportion"?

All groups are now included in this analysis.

The text for this muzzle-contact analysis would indicate that this model was not fit with any random effects, which would be extremely concerning. However, having checked the R code which the authors provided, I see that Individual has been fit as a random effect. This should be mentioned in the manuscript. I would also strongly recommend fitting Group (it was an RE in the previous models, oddly) and potentially exposure number as well.

The model about muzzle contact rate never contained individual as a random effect because individuals are not relevant in this model – it is the number of muzzle contacts occurring during each exposure. However, the reviewer might refer here to the model that we forgot to provide the script for. Nonetheless, we have substantially revised this model, it now (Model 3) includes all groups, and has group as a random effect.

Following on from this, if the model was fit with individual as a random effect it becomes confusing that Figure 3 which represents this data seemingly does not control for repeated measures (it contains many more datapoints than the study's actual sample size of 164 individuals). This needs to be corrected for this figure to be meaningfully interpretable.

Figure 3 is not related to the model described in (original) line 452.

The numbers were referring to the number of muzzle contacts, and this was written in the figure caption. However, we no longer present these details on the new figure (see Fig 4).

Finally, would it make sense to somehow incorporate the number of individuals present for this analysis? Much like any other social or communicative behaviour, I would predict the frequency of occurrence to depend on how many opportunities (i.e. social partners) there are to engage in it.

We have included the number of monkeys eating in our muzzle contact rate model now (Model 3) as upon further thought, we found that this was the issue leading us to want to exclude exposures, and only include the groups where many monkeys were eating. We have resolved this now by including all groups and not dropping exposures, and rather we include an interaction between number of monkeys eating and exposure number. We feel this addresses our hypothesis here much more satisfactorily. We hope these updates also address the reviewers concerns adequately.

Line 460: "For BD and LT we excluded exposures 4 and 3, respectively, due to circumstances resulting in very small proportions of these groups present at these exposures"

What was the criterion for a satisfactory proportion? Why was this chosen

See above – this is now addressed.

Line 461: "We ran the same model including these outlier exposures and present these results in the supplementary material (SM3)."

The results of this supplemental analysis should be briefly stated. Do they support the original analysis or not?

We no longer present this like this. We revised the model examining muzzle contact rate substantially and actually included the number of individuals eating in the model rather than excluding groups where this number was low. The results of the new model show good support our hypothesis.

Line 465: "Due to very low numbers of infants ever being targets of muzzle contacts, we merged the infant and juvenile age categories for this analysis."

This strikes me as a rather large mistake. The research question being asked by the authors here is "How does age influence muzzle-contact behaviour?"

Then, when one age group (infants) is very unlikely to be a target of muzzle-contact, the authors have erased this finding by merging them with another age category (juveniles). This really does not make sense, and seriously confounds any interpretation of either age category.

Yes we agree with this issue, and no longer do that. Rather we remove the infant data from this model, which is now Model 6, because of the large amounts of error they introduced into the model due to the small sample size. We show the process in the R code, and we describe our reasons in the text (lines 713-719). Since we are now only comparing within age- and sex-categories (see below) we do not find this decision introduces any bias.

Lines 466-474: Why was rank removed for the second and third models? Why is Group no longer a random effect (as in the previous analysis)? The authors need to justify such steps to give the reader confidence in their approach.

This is now addressed and discussed in descriptions of our new models.

Furthermore - because of the way this model is designed, I do not think it can actually be used to infer that these groups are preferentially targeted, merely that adult female and adult males are LESS likely to target others than to be targeted themselves, which is a very different assertion.

Because the specific outcome measure was not described here, this only became apparent to me after inspecting Figure 3, where outcome measure is described as "Probability of (an individual) being a target rather than initiator" - so, it can tell us that adults are more often targeted rather than initiating, but does not tell us if they are targeted more frequently than juveniles (who may get targeted very often, but initiate so often that this ratio is offset).

We thank the reviewer for noticing this as we had indeed chosen an inappropriate model for what we were intending to measure – this has been addressed now with two additional models (Models 4 and 5; see details at the top of document). We nonetheless found the aspects of this model to still be highly interesting, so have re-framed it to focus on them.

Lines 467-473: "Our first simple model included individuals' knowledge of the novel food at the time of each muzzle contact (knowledgeable = previously succeeded to extract and eat peanuts; naïve = never previously succeeded to extract and eat peanuts) and age, sex and rank as fixed effects. Individual was included as a random effect. The second model was the same, but we removed rank and added interactions between: knowledge and age; and knowledge and sex. The third model was the same as the second, but we also added a three-way interaction between knowledge, age and sex."

This is a good example of some of the issues I describe above. What is the justification for each of these model-structures? The addition and subtraction of variables and interactions seems arbitrary to the reader.

For Model 6, we no longer include rank at all, because we had not hypothetical reason to (see lines 723-725). We now begin with the three-way interaction, and only remove this, because it is not significant, and the model had problems converging as well, due to its complexity. We show this in the R script. We retain only the two separate interactions, and we do not include group as a random effect in this model due to the complexity AND because we do not think there is a theoretical requirement for it to be included here (this is explained in lines 730-735- in the manuscript. We report the results of the 3-way interaction in the supplementary material – SM3 Table S2).

Reviewer 3

In this study, the authors introduce a novel food that requires handling time to five vervet monkey groups, some of which had previous experience with the food. Through the natural dispersal of males in the population, they show that dispersing individuals transmit behavioral innovations between groups and are often also innovators. They also examine muzzle contact initiations and targets within the groups as a way to determine who is seeking social information on the new food source and who is the target of information seeking. The authors show that knowledgeable adults are more often the target of muzzle contacts compared to young individuals and those that are not knowledgeable.

This is a very interesting study that provides some novel insights. The methods employed will be useful to others that are considering an experimental approach to their field research. The data set is good and analyzed appropriately and the conclusions are justified. However, there are several areas where the paper could be improved for readers in terms of its clarity.

1) It wasn't until the Discussion that it became clear to me that the actual physiological and personality traits of dispersers were being linked with innovation. From the Title, Abstract, and Introduction, it seemed as though the focus was on dispersing males bringing their experience with a novel food to a new group to pass it on. I think it needs to be made clear much earlier in the manuscript that the authors are investigating not only the transmission of behavioural adaptation but also how the traits of dispersers might may make them more likely to innovate.

We have now addressed this above.

2) Early in the paper on line 28, the authors state that continued initiation of muzzle contacts by adult females could have been an effort to seek social information. This is true but another interpretation is that females were imparting or giving social information. It seems important here and elsewhere (lines 322-323) to consider and report the target of these initiations. If these were directed at more knowledgeable individuals, it supports the idea that this was social information seeking. If muzzle contacts were directed to younger or unknowledgeable individuals, it would imply a form of teaching, which is possible but perhaps unlikely, so I think the authors need to be totally clear here.

We thank the reviewer for pointing this out We looked into our data and now present figure 4D, showing that almost all knowledgeable adult females’ muzzle contacts were targeted towards knowledgeable adult males and talk about it in the discussion (lines 499-500).

3) The argument made on lines 344-350 needs more fleshing out to be convincing or it should be deleted. The link between number of dispersers, social organization, and large geographic range seems a little muddled. There are many dispersing individuals in species that are not typically in large multi-male, multi-female social organizations. Indeed, in many species both sexes disperse. Think of pair living birds where both sexes disperse and geographic range can be enormous. There are also no data or references presented here to show that species in multi-male, multi-female social organizations do have larger geographic ranges than those that are not in these social organizations. It seems to me that, even if this is the case, niche is more important than social organization, for instance not being dependent on forests to constrain much of your range.

We have removed this section

Reviewer #2 (Public Review)

I have separated my issues with the manuscript into three sub-headings (Conceptual Clarity, Observational Detail and Analysis) below.

1) Conceptual clarity

There are a number of areas where it would greatly benefit the manuscript if the authors were to revisit the text and be more specific in their intentions. At present, the research questions are not always well-defined, making it difficult to determine what the data is intended to communicate. I am confident all of these issues could be fixed with relatively minor changes to the manuscript.

For example, Line 104: Question 1 is not really a question, the authors only state that they will "investigate innovation and extraction of eating the food", which could mean almost anything.

Question 2a (line 98) is also very vague in it's wording, and I'm left unclear as to what the authors were really interested in or why. This is not helped by Line 104 which refuses to make predictions about this research question because it is "exploratory". Empirical predictions are not simply placing a bet on what we think the results of the study will be, but rather laying out how the results could be for the benefit of the reader. For instance, if testing the effects of 10 different teaching methods on language acquisition-rate: Even if we have no a priori idea of which method will be most effective, we can nevertheless generate competing hypotheses and describe their corresponding predictions. This is a helpful way to justify and set expectations for the specific parameters that will be examined by the methods of the study. In fact, in the current paper, the authors in fact had some very clear a priori expectations going into this study that immigrant males would be vectors of behavioural transmission (clear that is from the rest of the introduction, and the parameters used in their analysis, which were not chosen at random).

The multiple references to 'long-lived' species in the abstract (line 16 and introduction (39, 56) is a bit confusing given the focus of this study. Although such categorisations are arbitrary by nature (a vervet is certainly long-lived compared to a dragonfly), I would not typically put vervet monkeys (or marmosets, line 62) in the same category as apes (references 8 and 9) or humans (line 62) in this regard. This contributes a little towards the lack of overall conceptual focus for the manuscript: beginning in this fashion suggests the authors are building a "comparative evolutionary origins" story, hinting perhaps at the phylogenetic relevance of the work to understanding human behaviour, but the final paragraph of the study contextualises the findings only in terms of their relevance to feeding ecology and conservation efforts. I would recommend that the authors think carefully about their intended audience and tailor the text accordingly. This is not to say that readers interested in human evolution will not be interested in conservation efforts, but rather that each of these aspects should be represented in each stage of the manuscript (otherwise - conservationists may not read far into the Introduction, and cultural evolution fans will be left adrift in the Conclusion).

2) Observational detail

There are a number of areas of the manuscript which I found to be lacking in sufficient detail to accurately determine what occurred in these experimental sessions, making the data difficult to interpret overall. All of this additional information ought to be readily available from the methods used (the experiments were observed by 3-5 researchers with video cameras (line 341)) and is all of direct relevance to the research questions set out by the authors.

While I appreciate that it will take quite a bit of work to extract this information, I am certain that it would greatly improve the robustness and explanatory power of this study to do so.

The data on who was first to innovate/demonstrate successful extraction of the food in each group (Question 1) and subsequent uptake (Question 2), as well as the actual mechanism by which that uptake occurred (the authors strongly imply social learning in their Discussion, but this is never directly examined) is difficult to interpret based on the information presented. Some key gaps in the story were:

- Which/how many individuals encountered the food and in what order? I.e., were migrants/innovators simply the first to notice the food?<br /> - Did any individuals try and fail to extract the food before an "innovator" successfully demonstrated?<br /> - How many tried and failed to extract the nuts before and after observing effective demonstrators?<br /> - Were individuals who observed others interact with the food more likely to approach and/or extract it themselves?<br /> - Did group-members use the same methods of extraction as their 'innovators'?<br /> - How many tried and succeeded without having directly observed another individual do so (i.e. 'reinvention' as per Tennie et al.)?

The connective tissue between the research questions set out by the authors is clearly social learning. In short: the thesis is that Migrants/Innovators bring a novel behaviour to the group, then there is 'uptake' (social learning), which may be influenced by demographic factors and muzzle-contact (biases + mechanisms). Given this focus (e.g. lines 224-264 of the Discussion), I would expect at least some of the details above to be addressed in order to provide robust support for these claims.

Question 2a (Lines 136-146): This data is hard to interpret without knowing how much of the group was present and visible during these exposures.

For example: 9% update in NH group does not sound impressive, but if only 10% of the total group were present while the rest were elsewhere, then this is 90% of all present individuals. Meanwhile if 100% of BD group were present and only experienced 31% uptake, then this is quite a striking difference between groups.

Of course, there is also an issue of how many individuals can physically engage with the novel food even if they want to - the presence of dominant individuals, steepness of hierarchy within that group, etc, will significantly influence this (and is all of interest with regards to the authors' research questions).

Muzzle-contact behaviour: The authors use their data to implicate muzzle-contact in social learning, but this seems a leap from the data presented (some more on this in the Analysis section).

For example:<br /> - What is the role of kinship in these events?<br /> - Did they occur when the juvenile had free access to the food (i.e. not likely to be chased off by a feeding adult)?<br /> - Did they primarily occur when adults had a mouthful of food? (i.e. could it simply be attempted pilfering/begging)<br /> - What proportion of PRESENT (not total) individuals were naïve and knowledgeable in each group for each trial (if 90% present were knowledgeable, then it is not surprising that they would be targeted more often)?<br /> - Did these events ever lead to food-sharing (In other words, how likely are they to simply be begging events)?<br /> - Did muzzle-contact quantifiably LEAD to successful extraction of the food? If the authors wish to implicate muzzle-contact in social learning, it is not sufficient to show that naïve individuals were more likely to make muzzle-contact, they must also show that naïve individuals who made more muzzle-contact were more likely to learn the target behaviour.

3) Analysis

There are a number of issues with the current analysis which I strongly recommend be addressed before publication. Some of these are likely to simply require additional details inserted to the manuscript, whereas others would require more substantial changes. I begin with two general points (A & B), before addressing specific sections of the manuscript.

A) My primary issue with each of the analyses in this manuscript is that the authors have fit complex statistical models for each of their analyses with no steps to ascertain whether these models are a good fit for the data. With a relatively small dataset and a very large number of fixed effects and interactions, there is a considerable risk of overfitting. This is likely to be especially problematic when predictor variables are likely to be intercorrelated (age, sex and rank in the case of this analysis).

The most straightforward way to resolve this issue is to take a model-comparison approach. Fitting either a) a full suite of models (including a 'null' model) with each possible permutation of fixed effects and interactions (since the authors argue their analysis is exploratory) or b) a smaller set of models which the authors find plausible based on their a priori understanding of the study system. These models could then be compared using information criterion to determine which structure provides the best out-of-sample predictive fit for the data, and the outputs of this model interpreted. Alternatively, a model-averaging approach can be taken, where the effects of each individual predictor are averaged and weighted across all models in the set. Both of these approaches can be performed easily using the r package 'MuMIn'. There are also a number of tutorials that can be found online for understanding and carrying out these approaches.

B) It does not seem that interobserver reliability testing was carried out on any of the data used in these analyses. This is a major oversight which should be addressed before publication (or indeed any re-analysis of the data).

Line 444: Much more detail is needed here. What, precisely, was the outcome measure? Was collinearity of predictors assessed? (I would expect Age + Rank to be correlated, as well as Sex + Rank).

Line 452. A few comments on this muzzle-contact analysis:

"We investigated muzzle contact behaviour in groups where large proportions of the<br /> groups started to extract and eat peanuts over the first four exposures"

What was the criteria for "a large proportion"?

The text for this muzzle-contact analysis would indicate that this model was not fit with any random effects, which would be extremely concerning. However, having checked the R code which the authors provided, I see that Individual has been fit as a random effect. This should be mentioned in the manuscript. I would also strongly recommend fitting Group (it was an RE in the previous models, oddly) and potentially exposure number as well.

Following on from this, if the model was fit with individual as a random effect it becomes confusing that Figure 3 which represents this data seemingly does not control for repeated measures (it contains many more datapoints than the study's actual sample size of 164 individuals). This needs to be corrected for this figure to be meaningfully interpretable.

Finally, would it make sense to somehow incorporate the number of individuals present for this analysis? Much like any other social or communicative behaviour, I would predict the frequency of occurrence to depend on how many opportunities (i.e. social partners) there are to engage in it.

Line 460: "For BD and LT we excluded exposures 4 and 3, respectively, due to circumstances resulting in very small proportions of these groups present at these exposures"

What was the criterion for a satisfactory proportion? Why was this chosen?

Line 461: "We ran the same model including these outlier exposures and present these results in the supplementary material (SM3)."

The results of this supplemental analysis should be briefly stated. Do they support the original analysis or not?

Line 465: "Due to very low numbers of infants ever being targets of muzzle contacts, we merged the infant and juvenile age categories for this analysis."

This strikes me as a rather large mistake. The research question being asked by the authors here is "How does age influence muzzle-contact behaviour?"<br /> Then, when one age group (infants) is very unlikely to be a target of muzzle-contact, the authors have erased this finding by merging them with another age category (juveniles). This really does not make sense, and seriously confounds any interpretation of either age category.

Lines 466-474: Why was rank removed for the second and third models? Why is Group no longer a random effect (as in the previous analysis)? The authors need to justify such steps to give the reader confidence in their approach.

Furthermore - because of the way this model is designed, I do not think it can actually be used to infer that these groups are preferentially targeted, merely that adult female and adult males are LESS likely to target others than to be targeted themselves, which is a very different assertion.

Because the specific outcome measure was not described here, this only became apparent to me after inspecting Figure 3, where outcome measure is described as "Probability of (an individual) being a target rather than initiator" - so, it can tell us that adults are more often targeted rather than initiating, but does not tell us if they are targeted more frequently than juveniles (who may get targeted very often, but initiate so often that this ratio is offset).

Lines 467-473: "Our first simple model included individuals' knowledge of the novel food at the time of each muzzle contact (knowledgeable = previously succeeded to extract and eat peanuts; naïve = never previously succeeded to extract and eat peanuts) and age, sex and rank as fixed effects. Individual was included as a random effect. The second model was the same, but we removed rank and added interactions between: knowledge and age; and knowledge and sex. The third model was the same as the second, but we also added a three-way interaction between knowledge, age and sex."

This is a good example of some of the issues I describe above. What is the justification for each of these model-structures? The addition and subtraction of variables and interactions seems arbitrary to the reader.

You can even annotate code !

You can even annotate code !

• pearl : language is the original code for hacking virtual reality

I shall always love you, StarPterano. NEVER DIE.

This approaches it backwards. Consider a TypeScript-free codebase where the type annotations live in the documentation—which isn't generated. Your "compiler" then is really just a program verifier. Given the JS program text and the availability of docs, it takes the fusion as input and runs the verifier on that. No source-to-source compilation or mangling. The code that runs is the code you write—not some intermediate file output by tsc.

https://twinery.org/

Twine is an open-source tool for telling interactive, nonlinear stories.

You don’t need to write any code to create a simple story with Twine, but you can extend your stories with variables, conditional logic, images, CSS, and JavaScript when you're ready.

Twine publishes directly to HTML, so you can post your work nearly anywhere. Anything you create with it is completely free to use any way you like, including for commercial purposes.

Heard referenced in Reclaim Hosting community call as a method for doing "clue boards".

Could twinery.org be used as a way to host/display one's linked zettelkasten or note card collection?

Actually, the two density plots should have the same height if the sample sizes are both equal to 25. But in the code above you set size=10, even though the legend says n=25.

Reviewer #2 (Public Review):

The manuscript by Oláh, Pedersen, and Rowan, "Ultrafast Simulation of Large-Scale Neocortical Microcircuitry with Biophysically Realistic Neurons", demonstrates an ANN architecture that accurately captures the dynamics of neurons while also providing a substantial reduction of computing time relative to the standard method using NEURON simulations. This is important work that, together with recent similar work by others, opens exciting opportunities for detailed and accurate simulations of neurons with much higher speed than has been possible so far. The authors demonstrated an important step forward in enabling accurate and high-speed simulations of neurons taking advantage of modern ANN architectures and computing hardware such as GPUs.

• They started by considering several different ANN architectures and training each architecture to capture the membrane voltage dynamics in a single-compartment NEURON model of a neuron described by Hodgkin-Huxley equations. One particular architecture, the "CNN-LSTM" was substantially more successful than others in training and testing, especially in reproducing the action potentials (APs), i.e., it captured well both the subthreshold membrane voltage and APs.

• They then showed that once trained on a neuron model, the CNN-LSTM ANN generalizes to the cases where ionic conductance is manipulated and can capture the ionic sodium and potassium currents, in addition to the membrane voltage, without the need to re-train the ANN.

• Furthermore, the ANN generalizes to the cases involving nonlinear synapses, such as NMDA synapses, in addition to the simpler AMPA synapses.

• The authors then applied the ANN simulations to a realistic multi-compartmental model of a pyramidal cell (PC) from Layer 5 (L5PC) in the mammalian cortex and showed good performance for this cell, as well as L2/3PC, L4PC, and L6PC.

• In the next step, between one and 5,000 L5 PCs were simulated, and it was shown that ANN simulations on a GPU are faster by a factor of over 10,000 than NEURON simulations on a single CPU. This is a drastic and impressive difference.

• Finally, the authors demonstrated that a network of 150 PCs mimicking the effects of Rett syndrome can be efficiently simulated using the ANN approach. They sampled a large parameter space using the ANN simulations on a single GPU within seconds, a task that would take again on the order of 10,000 times longer for regular CPU simulations without the ANN approach.

The study is interesting and extensive. Multiple lines of evidence, as enumerated above, show that the approach described here is promising. It definitely deserves the attention of fellow computational neuroscientists. I am convinced that many of them would like to try out the approach and the code that will be shared freely by the authors. The paper is mostly clear and easy to follow.

In my opinion, the weaknesses of this work are relatively minor. Generally, I would like to see more characterization of ANN generalization for tasks relevant to the everyday practice of neuronal modeling. For example, it is common to change not only the strength, but also the number of synapses, and it will be useful if the ANN approach seamlessly generalizes to that. Another point is that the authors could put their study more into the context of other research happening in this area and discuss the uniqueness of their contributions in that light. But, again, overall I find this study to be extensive and interesting, and I think it will generate a strong interest in the field.

Reviewer #3 (Public Review):

In this study, the authors' goal was to accelerate biologically-detailed neuronal network simulations, by leveraging the computational efficiency and amenability to parallelization of modern artificial neural network architectures (ANNs). The general idea is to train an ANN on time series generated by traditional neuronal simulations, then provide new inputs and determine whether the generalization capabilities of the ANN allow it to predict the time series that would be generated by the original model with the same inputs.

Starting with a simple, single-compartment neuron model, the authors trained five different ANNs to reproduce/approximate the behaviour of the model and found that only one of these ANNs, a recurrent model containing convolutional layers, long short-term memory layers, and fully connected layers, which they termed the CNN-LSTM network, was able to satisfactorily reproduce both the subthreshold activity and the spiking activity (91% of spikes predicted correctly).

The authors then added complexity to the model and found that it generalized well to changes in synaptic weight, non-linear synapses, and changes in input patterns. Partial retraining of the upper layers allowed generalization to other changes (steady-state activation of K channels).<br /> Moving from single-compartment to multi-compartment neurons, the CNN-LSTM network was still able to accurately reproduce sub-threshold fluctuations, although the accuracy of spike prediction declined to 67%.

Applying the technique to circuit models, the authors performed a parameter-space mapping in a model of Rett syndrome. In all cases beyond single point-neuron models, the CNN-LSTM network running on a GPU system outperformed the NEURON simulator running on a single CPU. In the case of simulating many identical neurons (but with different inputs), and when simulating the small circuit model of Rett syndrome, the performance gain was of several orders of magnitude.

Strengths:<br /> Although ANNs have been used extensively in approximating the dynamics of neural systems, this has typically been at a much higher level of abstraction and a much coarser anatomical scale. I am not aware of any previous demonstration of using ANNs as a practical tool to approximate the behaviour of individual biological neurons and networks of such neurons (as opposed to using spiking neural networks to perform machine learning tasks, where there is a large literature). This manuscript demonstrates convincingly that this approach is a promising one, and provides a practical starting point for further research on this technique. The comparisons at the single neuron level are particularly thorough and well done, and (i) demonstrate that the trained network displays good generalization, and (ii) provide good evidence that the network has really learned important features of the underlying system.

Weaknesses:<br /> The comparisons at the network level are less convincing than for single neurons.<br /> Although this is not stated clearly, it seems that the simulations with 50 and 5000 neurons were for identical neurons differing only in their inputs. Given the variability of neuronal properties even within a specific cell type and the increasing representation of this variability in computational neuroscience models, it would have been valuable to know what the performance impact of incorporating such variability would be, in both the training and exploitation phases.<br /> Furthermore, much less detailed comparisons between the NEURON simulation results and the ANN results are given for the network models. For the Rett syndrome model, no results from the NEURON simulations are shown, neither at the single neuron level nor at the level of parameter maps, which makes it impossible to determine whether the ANN model is adequately reproducing the correct behaviour.<br /> For very large-scale simulations, spike communication is often the rate-limiting factor in simulations, rather than solving the equations for neuronal dynamics. Cortical pyramidal neurons typically receive around 10000 synapses, a much higher number than appears to have been used here. It remains to be demonstrated whether the advantage in computational speed is still an important factor in systems with very high rates of synaptic events, in particular for models that are too large to fit on a single GPU.<br /> It could be argued that the playing field was tilted towards the ANN, since the NEURON simulator cannot benefit from GPU parallelization at the present time. Using a GPU-capable simulator such as GeNN as an additional point of comparison would give a clearer picture of the strengths and weaknesses of the ANN approach.<br /> The Discussion section does not adequately discuss the limitations of the current study, nor does it sufficiently address the potential weaknesses of the ANN approach, although some potential limitations are mentioned.

In summary, the authors have shown that ANNs are a promising tool for greatly increasing the scope of what can be modelled with generally available computing hardware, reducing the bottleneck of supercomputer availability. Clearly further studies are needed to explore the utility of the approach in a broader range of real-world scenarios, but by providing a good description of the successful CNN-LSTM model, and by providing their source code in a public repository, the authors have provided a strong basis for others to test this approach in their own projects.

This study is likely to have a substantial impact, stimulating further work in (i) understanding the performance-accuracy tradeoffs of this approach in comparison to other GPU-based simulation methods, and (ii) understanding the modelling domain for which this approach gives adequate accuracy (does it break down for networks on the edge of chaos, for example?). Should the method live up to its promise, it could greatly accelerate progress in computational neuroscience.

Reviewer #2 (Public Review):

The medically important mosquito genus Anopheles contains many species that are difficult or impossible to distinguish morphologically, even for trained entomologists. Building on prior work on amplicon sequencing, Boddé et al. present a novel set of tools for in silico identification of anopheline mosquitoes. Briefly, they decompose haplotypes generated with amplicon sequencing into kmers to facilitate the process of finding similar sequences; then, using the closest sequence or sequences ("nearest neighbors") to a target, they predict taxonomic identity by the frequency of the neighbor sequences in all groups present in a reference database. In the An. gambiae species complex, which is well-known for its historical and ongoing introgression between closely-related species, this approach cannot distinguish species. Therefore, they also apply a deep learning method, variational autoencoders, to predict species identity. The nearest neighbor method achieves high accuracy for species outside the gambiae complex, and the variational autoencoder method achieves high accuracy for species within the complex.

The main strength of this method (along with the associated methods in the paper on which this work builds) is its ability to speed up the identification of anopheline mosquitoes, therefore facilitating larger sample sizes for a wide breadth of questions in vector biology and beyond. This technique has the added advantage over many existing molecular identification protocols of being non-destructive. This high-throughput identification protocol that relies on a relatively straightforward amplicon sequencing procedure may be especially useful for the understudied species outside the well-resourced gambiae complex.

An additional and intriguing strength of this method is that, when a species label cannot be predicted, some basic taxonomic predictions may still be made in some cases. Indeed, even in the case of known species, the authors find possible cryptic variation within An. hyrcanus and An. nili, demonstrating how useful this new tool can be.

The main weakness of this method is that, as the authors note, accuracy is dependent on the quality and breadth of the reference database (which in turn relies on the expertise of entomologists). A substantial portion of the current reference database, NNv1, comes from one species complex, An. gambiae. This is reasonable given the complex's medical importance and long history of study; however, for that same reason, robust molecular and computational tools for identifying species in this complex already exist. The deep learning portion of this manuscript is a valuable development that can eventually be applied to other species complexes, but building up a sufficient database of specimens is non-trivial. For that reason, the nearest neighbor method may be the more immediately impactful portion of this paper; however, its usefulness will depend on good sampling and coverage outside the gambiae complex.

Another potential caveat of this method is its portability. It is not clear from either the manuscript or the code repository how easy it would be for other researchers to use this method, and whether they would need to regenerate the reference database themselves. The authors clearly have expansive and immediate plans for this workflow; however, as many researchers will read this manuscript with an eye towards using these methods themselves, clarifying this point would be valuable.

The authors present data suggesting that their method is highly accurate in most of the species or groups tested. While the usefulness of this method will depend on the reference database, two points ameliorate this potential concern: it is already accurate on a wide breadth of species, including the understudied ones outside the An. gambiae complex; additionally, even when a specific species identification cannot be made, the specimen may be able to be placed in a higher taxonomic group.

Overall, these new methods offer an additional avenue for identifying anopheline species; given their high-throughput nature, they will be most useful to researchers doing bulk collections or surveillance, especially where multiple morphologically similar species are common. These methods have the potential to speed up vector surveillance and the generation of many new insights into anopheline biology, genetics, and phylogeny.

copilot将先code后comment的模式变为先comment后code

The response sample code is not updated. Please use the one I am sharing below.

{ "entity": "collection", "count": 1, "items": [ { "id": "pay_JsSu2WouXWEBGu", "entity": "payment", "amount": 100, "currency": "INR", "status": "captured", "order_id": null, "invoice_id": null, "international": false, "method": "bank_transfer", "amount_refunded": 0, "refund_status": null, "captured": true, "description": "", "card_id": null, "bank": null, "wallet": null, "vpa": null, "email": "gaurav.kumar@example.com", "contact": "+919999999999", "customer_id": "cust_F4W8ju0t4WE0m0", "notes": [], "fee": 1, "tax": 0, "error_code": null, "error_description": null, "error_source": null, "error_step": null, "error_reason": null, "acquirer_data": {}, "created_at": 1657631198 } ] }

See also http://cr.yp.to/qhasm/literature.html

See: Oberon

See also the discussion (in the comments) about optimization-after-the-fact in http://akkartik.name/post/mu-2019-2

Pros

1. Easy to build microServices that perform.

2. Reduced dev and maintenance time

3. Better code / product ownership through small and nimble teams that own your services and apps

4. reduced code size

5. Easy and type safe configurations

• Within Indyweb ecosystem,
• would this be when a user uses Trailmarks to identify a potentially useful application
• and a bounty can then be offered to app developers
• to develop an Indyweb app
• to process the new function?

Definition of Intentional Programming * In computer programming, * Intentional Programming is a programming paradigm * developed by Charles Simonyi * that encodes in software source code the precise intention which programmers (or users) have in mind when conceiving their work. * By using the appropriate level of abstraction at which the programmer is thinking, * creating and maintaining computer programs become easier. * By separating the concerns for intentions and how they are being operated upon, * the software becomes more modular and allows for more reusable software code. * Can we see an example of this in action for clarification?

@2:10

They didn't publish the code. They published the algorithm. And they prided themselves on—the computer scientists at the time—of describing the algorithm, not GitHubbing the code. These days we don't—we GitHub the code. You want the algorithm? Here's the code.

This is not always reliable. There are some non-highly-mathematical things that you'd prefer to have the algorithm explained rather than slog through the code, which is probably adulterated with hacks for e.g. platform gotchas, etc.

There is a better way, though, which is to publish a high-level description of the workings as runnable code that you can simulate in a Web browser. Too many people have misconceptions about the stability of the Web browser as a platform for simulations, however. We need to work on this.

I would add: Some academic journals require you to submit a script as well, so that your research can be reproduced or at least tested. You will notice that in some of CIM modules you are obliged to submit your code as part of your assignment.

Coding and programming can be compared to "typing and writing". In other words, you need to code in order to program, just as you need to type in order to write.

ps. love the analogy!

perhaps explaining?

This might be a good type to introduce other contrast ideas such as (-0.5, 0.5) to have intercept represent the mean and slope the difference.

The prosecution representing the Crown wish to invoke Section 386 of the Criminal code to push for life sentencing without parole

The code sample should come after the endpoint info Check for all places Endpoint > Sample code > Request Parameter table

Add the one line above the code sample

This should come above the code sample.

remove The table should come before the code sample

So far, although there are many different splintered student groups under different names, they seem to echo the same general points and ideals.

很全的SPT

mRNA vaccines provides genetic code of pathogen's relevant antigen unlike other vaccines platforms when inoculated into body it exposes subject with pathogen. Once cells got the blueprint to construct the protein, immune response starts producing antibodies, body starts developing certain level of immunity against particular pathogen. This mRNA vaccine technique has been in use for years against other pathogens such as Zika, influenza.

PyTorch use broadcasting

Author Response

Reviewer #3 (Public Review):

In this work, the authors describe a novel method, based on deep learning, to analyze large numbers of yeast cells dividing in a controlled environment. The method builds on existing yeast cell trapping microfluidic devices that have been used for replicative lifespan assay. The authors demonstrate how an optimized microfluidic device can be coupled with deep learning methods to perform automatic cell division tracking and single cell trajectories quantification. The overall performance of the method is impressive: it allows to deal with large image datasets generated by timelapse microscopy several order of magnitudes faster than what manual annotation would require. The method has been carefully tested on several microscopy settings and datasets and compared with known results from the literature in a convincing manner. In addition, the authors show how the analysis pipeline can be enriched with semantic segmentation to quantify cellular physiology and gene expression during their lifespan, creating high quality, high throughput measurements of single cell trajectories. The software, its documentation and related datasets are available through public repository. Taken together, the author succeeded in setting up a method that can be a game changer for high throughput longitudinal analysis of yeast cells.

Overall, the method seems robust and powerful but some aspects need to be clarified and/or extended.

• The authors chose MATLAB to develop DetecDiv. This is a valid choice but as Python is becoming the standard for deep learning developments it is important to 1/ better justify the use of MATLAB and 2/ discuss how this can be "translated into" and/or linked with Python. This would facilitate adoption by other research teams.

Using MATLAB as a prototyping language was instrumental for us in establishing the proof of principle of the method reported here since we have a long-standing experience in MATLAB programming. Yet, we fully agree with the reviewer that Python may appear as a more legitimate choice, especially in the field of deep learning. For future work, we are considering moving our code to Python to make it more widely accessible and to more quickly benefit from the latest development in the field. We also envision that Python developers could transpose our methods for their own research interests.

Last, we note that MATLAB has bidirectional communication with a number of programming languages, including Python. Therefore, it is currently possible to use Python scripts to fully control the DetecDiv pipelines by calling its low levels functions at the command line. Obviously, it may be more cumbersome to use than native Python code and it restricts the possibility to use the graphical user interface that we have developed.

• A critical aspect of deep learning methods is their potential ability to be used on a different datasets and/or experimental setup (transfer learning). The authors explained that a "generalist" model, trained using several datasets perform comparably (or even better) than "specialist" models that are independently trained on a specific dataset. Yet, they do not discuss how accurate would an already trained generalist model perform on a novel dataset made with a different imaging setup and/or a different yeast strain?

We thank the reviewer for this comment, which is somewhat related to point #2 raised by reviewer #1, regarding the ability of a model to generalize its prediction to various contexts. In the revised version, we now provide clear evidence that the model designed for division counting and RLS analysis, which is trained on WT data only, can successfully predict the lifespan of mutants such as fob1delta and sir2delta (new Figure 2 - Figure supplement 5) and the onset of cell death during stress response assays (Figure 6 - Figure supplement 1).

However, changing the imaging conditions (e.g. magnification, illumination, etc) would quickly deteriorate the performance of the model, unless it has been exposed to these new conditions upon training. Hence, the purpose of the ‘generalist’ approach we use is to demonstrate that the models we use have the capacity to deal with various imaging conditions when appropriately trained.

We have added a sentence in the discussion to explain what determines the potential of a model to be successfully employed in different contexts.

function name starts with a lowercase

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

Learn more at Review Commons

Reply to the reviewers

1. General Statements

We would like to thank the reviewers for their insightful and useful comments about our manuscript. Based on these comments and as outlined in our revision plan, we plan to strengthen our findings by performing new experiments and quantitative analyses. This particularly applies to our nanoscale (dSTORM) imaging dataset which was discussed by multiple reviewers.

We also appreciate the reviewers’ overall positive evaluation of the significance of our labeling method for the axon initial segment studies. With regards to this, we would like to highlight that this manuscript particularly addresses the labeling of “difficult-to-label” neuronal proteins, such as large ion channels and transmembrane proteins. Although we and another group have recently reported click labeling of neurofilament light chain (PMID: 35031604) and AMPAR regulatory proteins (PMID: 34795271) in primary neurons, both of these proteins have a small size between ~30-68 kDa and compared to larger ion channels/transmembrane proteins are “easier” to express in primary neurons. The novelty in the current manuscript is that we successfully applied this method for the labeling of large and spatially restricted AIS components, such as NF186 and Nav1.6 (186 and 260 kDa, respectively). As some of the reviewers also pointed out, the size and complexity of these proteins makes labeling of the AIS rather challenging. We also used our approach to study the localization of epilepsy-causing Nav1.6 variants and could exclude the retention in the cytoplasm as a possible cause of their loss of function. Finally, we improved the efficiency of genetic code expansion in primary neurons by developing AAV-based viral vectors. Although AAVs are routinely used for gene delivery to neurons, AAVs for click-based labeling need to encode multiple components of the orthogonal translational machinery for genetic code expansion. By trying different promoters and gene combinations, we developed several variants that enable high efficiency of the genetic code expansion in neurons. On their own, these findings will facilitate further genetic code expansion and click chemistry studies, beyond the labeling of the axon initial segment.

2. Description of the planned revisions

Reviewer #2

• On lines 107 and 108, the sentence "The C-terminal HA-tag allowed us to detect the full-length NF-186 protein by immunostaining it with an anti-HA antibody" would have a better place just after lines 104-105 " [...] we modified the previously described plasmid (Zhang et al., 1998) by moving the hemagglutinin (HA) tag from the N terminus to the C terminus".

We will modify the text as the reviewer suggested.

• Fig.2b: the AnkG staining looks substantially longer than that showed in c. However, the results on AIS length show no significant changes in between the groups. This is visually misleading, the authors should choose a picture for the WT construct that is representative of the data.

We thank the reviewer for bringing this up. We will replace the panel in Fig.2b with a more representative image of NF186 WT construct in the revised version of the manuscript.

• Line 238: what is the rationale behind choosing these cells? For example, have they been used in other studies for similar purposes? If so, please provide the reference.

We initially probed neuroblastoma ND7/23 which are commonly used for the electrophysiological recordings of recombinant Nav1.6 (PMID: 30615093, 22623668, 25874799, 27375106). Although we were able to record Na+ currents in those cells, only a small portion of channels was detected on the cell surface by microscopy (Suppl. Fig. 5a). As we discuss in the manuscript (lines 237-240), we then switched to N1E-115-1 cells in which we obtained a higher level of expression of the recombinant NaV1.6 channels on the cell surface (Suppl. Fig. 5b). These cells have also been previously used for the electrophysiological studies of voltage-gated sodium channels, including Nav1.6 (PMID: 8822380, 24077057). We will modify the text and include these references in the revised manuscript.

• Figure 3c, the authors omitted the comparison with the WT construct this time, as opposed to the neurofascin experiments. What is the reason?

As shown by others (PMID: 31900387) and us in this manuscript, one of the main issues with the expression of the recombinant NF186 in neurons was that overexpression led to mislocalization of NF186 in neuronal soma and processes. This was particularly true for WT construct and certain amber mutants (e.g. K809TAG). Based on previous reports (PMID: 31900387), we then tested a weak human neuron-specific enolase promoter. This reduced expression level and improved localization of NF186. However, since we still observed some neurons with mislocalized NF186 WT even with the enolase promoter, we found it important to quantitively compare the AIS length of WT construct and amber mutants to surrounding untransfected cells. On the other hand, since we did not have overexpression and mislocalization problem with Nav1.6 WT construct (all observed neurons have signal localizing in the AIS), we measured only the AIS length of the amber mutants. However, to avoid any confusion, we will also measure the AIS size of the neurons expressing Nav1.6 WT construct and compare it to surrounding cells and amber mutants. For this, we will need to perform new experiments and acquire new images. We will include the data in the revised manuscript.

• Fig. 4: why did the authors chose these cells for electrophysiology experiments and not neurons? Explain the rationale in the text or, alternatively, cite similar studies using the same tool.

Due to the branched neuronal processes which cause the space clamp problem in voltage clamp experiments with neurons, round and none-branching cells are frequently used to examine the biophysical properties of ion channels, including Nav1.6. By far, most of studies investigating the biophysical properties of NaV1.6 channels were performed in neuroblastoma cells e.g. ND7/23 and N1E-115-1 cells (PMID: 25874799; 25242737). We tested these two types of cells and found that N1E-115-1 cells supported higher expression level of the recombinant NaV1.6 channels on the cell surface than the ND7/23 cells (Suppl. Fig 5). Hence, N1E-115-1 were more suitable to get robust and reliable recordings (as we also discuss above in the response to reviewer’s comment). We will clarify this in the revised manuscript.

• Fig.4, biophysical properties: did the authors find differences in passive properties? Measures of resting potential, membrane resistance and cell capacitance should be reported.

Passive properties such as resting membrane potential and membrane resistance are important functional features in neurons measured in current clamp experiments, but not applicable for ND7/23 and N1E-115-1 cells used in our voltage clamp experiments. To measure the Na+ current mediated by WT or mutant NaV1.6 channels expressed in N1E-115-1 cells, the endogenous Na+ channels were blocked by tetrodotoxin and the endogenous K+ channels were blocked by tetraethylammonium chloride, CsCl and CsF in extracellular and intracellular solutions. Under these conditions, resting potential and membrane resistance are not relevant for experiments. Cell capacitance reflects the size of the cell surface area, which can affect the number of channels expressed on the cell surface. To eliminate the effect of different cell sizes, Na+ current densities normalized by cell capacitances were used in our experiments. We will report on these values in the revised manuscript.

• Fig 4, STORM images. The periodic distribution of the dots should be enhanced with some sort of arrows or lines, for the non-specialist audience.

Based on the comments from multiple reviewers, we plan to obtain additional dSTORM images of the neurons expressing recombinant Nav1.6 WT or amber mutants. We also intend to improve the visualization of these results by updating/modifying existing figures and including quantitative data.

• Line 374: rat or mouse primary neurons?

We are here referring to both, rat and mouse neurons. The images shown in Fig. 06 and Suppl. Fig. 08 were obtained from rat cortical neurons expressing Nav1.6 or fluorescent reporter. However, we were also able to successfully transduce mouse neurons with AAV92A carrying orthogonal translational machinery (data not shown). We will clarify this in the revised manuscript.

**Referees cross-commenting**

I fully agree with the following remarks from Reviewers #3, #4 and #5. This is a point that I have raised in my report too. The authors need better images to show the periodicity we visualization, and a quantification would be of great benefit to support the claim with numbers (and how these compare to similar studies in the literature):

R3: 2. For the dSTORM analysis of the tagged Nav1.6 protein, I also cannot tell there is periodic organization from the image directly. Some analysis is needed there. R4: 2."As there was no obvious difference in the nanoscale organization of the NaV1.6WT 317 -HA or NaV1.6TAG 318 -HA channels (Fig. 4. e-g), these experiments confirmed that the NaV1.6 overexpression, TCO*A319 Lys incorporation, and click labeling did not affect the nanoscale periodic organization of the sodium channels in the AIS." It is clearly noticeable that for WT, the spot density is more compared to the other two mutants. Why is that so? Using cluster analysis, one can quantify spot density and discuss nanoscale organization quantitatively. The author should quantify the periodicity and compare it among different variants and with previous reports. R5: 3. The authors claim that there was no obvious difference in the nanoscale organization of the NaV1.6WT 317 -HA or NaV1.6TAG 318 -HA channels (Fig. 4. e-g), but it is hard to conclude this without any quantification and statistical analysis. Sodium channels have been shown to be associated with the membrane-associated periodic skeleton structures in neurons and average autocorrelation analysis has been developed to quantify the degree of periodicity of such structural organizations (Han et al. PNAS 114(32)E6678-E6685, 2017). The authors should use this approach to quantify and compare the average autocorrelation amplitudes.

As we outlined in our responses to the individual reviewers’ comments below, we will address these questions by performing new experiments and quantifications.

I also agree with these comments from Reviewers #3 and #5:

R3: 4. It is unclear, for all the presented data, whether all the cells are collected from a single biological replicate or from multiple replicates. At least 2-3 replicates are needed to see the reproducibility in terms of labeling efficiency, and other related conclusions. R5: 1. The authors should indicate how many replicates were performed and how many cells were analyzed for each experiment.

We thank the reviewers for bringing this up. By mistake, we omitted this important information. We will include it in the revised manuscript, but we would like to highlight here that each experiment was repeated at least 3 times.

Reviewer #3

1. There is some patch-like background from the 488 channel from the click reaction, some of which have very as strong signal as the staining on the neurons. What is the potential cause for this? With immunostaining on HA, the background doesn't affect too much on the image data interpretation. However, the major goal of this method development is to use it in live-cell without immunostaining. Without another reference, the high background might cause issues in data interpretation. Can the author also suggest way to avoid or lower this in the discussion?

We thank the reviewer for bringing this up. We have occasionally observed patch-like background in what appears to be the cell debris. Such dead cells do not have an intact cell membrane and therefore can absorb cell-impermeable ATTO488-tetrazine dye during click labeling. This kind of background is also present in the control neurons transfected with the WT Nav1.6, which suggests that it originates from the UAA and tetrazine-dye accumulations. Additionally, since these patches are not visible with the immunostaining, they do not contain our protein of interest, which further confirms that they contain only dye and UAA accumulations. Depending on the neuron prep/quality before and after transfections, the presence of these patches is more or less obvious. However, despite the background we did not have problems identifying AIS during live cell imaging. Especially when overall neuronal health is optimal after transfections, AIS can easily be distinguished from patches that are positioned outside of labeled neurons. We will investigate this further and discuss it in the revised manuscript.

1. For the dSTORM analysis of the tagged Nav1.6 protein, I also cannot tell there is periodic organization from the image directly. Some analysis is needed there.

We will address this in the revised manuscript by performing additional experiments and quantifications. We also wrote a detailed answer below, in the response to the other reviewers.

1. The authors use the AIS length as a parameter to evaluate the function of the clickable mutant of NF186, and using patch clamp for functional validation of the clickable mutant of Nav1.6. In both cases, the comparison is done between the mutant and the WT construct, but both in transfected cell and exogenously expressed. It's also worth comparing with untransfected cells as the true native situation.

We agree with the reviewer that it is important to compare transfected cells with untransfected cells. As the reviewer points out, we have already performed some of these comparisons. When it comes to the NF186, we used the AIS length as a parameter to estimate if the expression of clickable mutant affected the AIS structure. As we show in the Fig. 02, we co-immunostained neurons transfected with NF186-HA WT or TAG constructs. We used HA antibody to detect neurons expressing NF186, while the ankG was used as a marker of the AIS length. To check if the AIS length of transfected cells is affected, we compared the length of transfected cells (expressing NF186, HA+) to surrounding untransfected cells (HA-). When it comes to the Nav1.6, we also compared the AIS length of cells expressing Nav1.6 (HA+) to surrounding untransfected cells (HA-). Similarly to the experiments with NF186, this allowed us to check if the expression of the recombinant Nav1.6 affect the AIS structure. What is missing is the comparison with untransfected conditions (i.e. neurons that are simply stained with ankG). We assume that is what the reviewer is referring to? We will also include these data in the revised manuscript. Furthermore, since we introduced a labeling modification in NaV1.6, we wanted to check if such modification would affect its function. To do so, as routinely done in the field (PMID: 25874799), we rendered the WT and TAG channels TTX-resistant and recorded only recombinant Na+ currents in neuroblastoma cells in the presence of TTX. Perhaps we misunderstand the reviewer’s comment, but in this regard measurements of untransfected cells are not relevant since they would not allow us to compare WT and TAG mutants.

1. It is unclear, for all the presented data, whether all the cells are collected from a single biological replicate or from multiple replicates. At least 2-3 replicates are needed to see the reproducibility in terms of labeling efficiency, and other related conclusions.

We thank the reviewer for the observation. By mistake, we omitted this important information. We will include in the revised version of the manuscript. We would like to highlight here that each experiment was repeated at least 3 times.

Reviewer #4

1."Confocal microscopy revealed that the hNSE promoter lowered the WT and clickable NF186-HA expression levels and consequently improved the localization of these proteins." Is the lower expression level a measure of localization improvement? How does the author conclude that the localization has improved?

Previous report (PMID: 31900387) suggested that the overexpression of the recombinant WT NF186 can affect its trafficking, leading to the NF186 mislocalization. We observed the same in our experiments with CMV NF186 (in particular for NF186 WT). Hence, based on the PMID: 31900387 we probed weak neuron specific enolase promoter. Since the WT was the most problematic in terms of the ectopic expression, we checked if AIS localization was improved with enolase promoter for this construct. To this aim, we counted number of neurons that with mislocalized signal or with the signal in the AIS for both, CMV and enolase promoter. We could observe that number of neurons with mislocalized signal was lower for enolase promoter. Since there were more neurons with the AIS-specific signal when NF186 was expressed from enolase promoter compared to CMV, we concluded that enolase promoter lowered expression and improved localization of the NF186. Therefore, we used enolase promoter for click labeling of NF186 amber mutants. We will include the results of this analysis in the revised version of the manuscript.

2."As there was no obvious difference in the nanoscale organization of the NaV1.6WT 317 -HA or NaV1.6TAG 318 -HA channels (Fig. 4. e-g), these experiments confirmed that the NaV1.6 overexpression, TCO*A319 Lys incorporation, and click labeling did not affect the nanoscale periodic organization of the sodium channels in the AIS." It is clearly noticeable that for WT, the spot density is more compared to the other two mutants. Why is that so? Using cluster analysis, one can quantify spot density and discuss nanoscale organization quantitatively. The author should quantify the periodicity and compare it among different variants and with previous reports.

We thank the reviewer for these suggestions. We will address these remarks by performing additional new experiments and quantifications. The difference in the level of the expression of the recombinant Nav1.6 might explain differences in the spot density for WT vs. TAG clickable mutants. However, as the reviewer suggested quantitative analysis is needed to address these concerns. We also intend to quantify the periodicity and compare it among different variants and with previous reports. It is just important to note that in the current version of the manuscript we looked at the nanoscale organization of the subset of Nav1.6 channels. The reason being that we used anti-HA antibody which will only detect our recombinant protein which got incorporated into the AIS and not the endogenous Nav1.6.

Minor comments

1."Although NF186K809TAG 158 -HA (Supplementary Fig. 4) showed bright click labeling, we excluded it from the analysis due to its frequent ectopic expression along the distal axon." How frequently is this bright click labeling observed for this mutation? Is it not observed for other mutations at all? The authors should state this point clearly with some statistics.

We are not sure what is the exact question from the reviewer. If we understand it correctly, the reviewer is asking us to quantify how frequent was the ectopic expression of this amber mutant compared to other mutants? And not the click labeling (as written in their original comment), since click labeling was observed for all the mutants independently of their ectopic expression?

2."Immunostaining with anti-HA antibody revealed that the expression of NaV1.6WT 239 -HA on the membrane of the N1E-115-1 cells was higher than on the ND7/23 cells (Supplementary Fig. 5a-c). However, click labeling of both NaV1.6K1425TAG 240 -HA and NaV1.6K1546TAG 241 -HA with ATTO488-tz was not successful (Supplementary fig. 5d) indicating insufficient expression of the clickable constructs." Is this due to insufficient expression level or accessibility? The author should make this statement clear.

We thank the reviewer for bringing this up. We will clarify this in the revised version of the manuscript. We believe that the click labeling of the K1546TAG mutant in N1E-115-1 cells is absent due to the insufficient expression of the channels on the membrane, since this mutant was successfully labeled in the primary neurons that represent more native environment and where Nav1.6 form high-density clusters. K1425TAG mutant is not labeled due to the insufficient expression on the membrane in N1E-115-1 cells as well. However, since this mutant is also poorly labeled in primary neurons, we can speculate that K1425TAG position might be less accessible for the tetrazine-dye compared to K1546TAG. To further support our claim that due to the insufficient expression click labeling is low/absent in neuronal cells, we can use NF186 as an additional example. When NF186 was expressed from strong CMV promoter, we observed click labeling for all the mutants in ND7/23 cells (Suppl. Fig.01). However, when CMV was replaced with neuron specific enolase promoter, the expression was of NF186 was substantially lower in ND7/23 cells and click labeling was absent (data not shown). We will clarify this in the revised manuscript.

1. Authors should clearly state the drift correction procedure of 3D STORM data. What are the localization precision and photon count for 3D STORM experiments?

We processed 3D dSTORM data in NIS-elements AR software. We used the automatic drift correction from the NIS-elements software that is based on the autocorrelation. We will provide further and updated information in the revised manuscript, including the localization precision and photon count for the new dSTORM images.

1. "Click labeling of NaV1.6 channels in living primary neurons" What kind of primary neurons have been used for click labeling of NaV1.6 channels? Is there any specific reason why authors have chosen cortical neurons for labeling NF186? Does this labeling strategy depend on primary neuron type?

For the establishment and click labeling of Nav1.6 we used primary rat cortical neurons (Fig. 03, Fig. 06). The same neuronal type has been used for click labeling of NF186 (Fig. 02). We established labeling of the AIS components in cortical neurons because we use those routinely in the laboratory. However, this labeling strategy does not depend on the neuronal type. As we show in Fig. 05, to study localization of the loss-of-function pathogenic Nav1.6 variants we used mouse hippocampal neurons. The reason for this is that in previous study the same neuronal type was used to characterize these two mutations (lines 361-362). This demonstrates nicely that method can be easily transferred to any neuronal type. Furthermore, we were also able to label Nav1.6 and NF186 in mouse cortical neurons (data are not shown in the manuscript). We will clarify this in the revised manuscript.

Reviewer #5

1.Throughout the manuscript, only one representative image containing one AIG is shown for each condition without statistics and quantifications, so the conclusions are not sufficiently convincing. For example, in Fig. 1b, c, e; Fig. 2b,c,d,e; Fig. 3b,c,d,e ; Fig. 5c; and Supplementary Fig.1-6, the authors should quantify the average fluorescence intensities both for HA immunostaining and ATTO488-tz labeling in different conditions, as well as the labeling ratios (fluorescence intensity ratios between ATTO488 and AF647/AF555) . Without statistics and quantifications, it is unclear whether there is any significant difference between the constructs with different TAG positions, or between different transfection methods (e.g., lipofectamine 2000 vs 3000).

We agree with the reviewer that the quantitative analysis is important and we will provide more quantitative data in the revised manuscript. At the same time, we are a bit confused by this comment which seems to refer to missing quantifications in one of the schemes (Fig. 1) and overlooks existing quantifications (e.g. quantitative analysis of the data set from Fig. 5c is shown in Fig. 5d). However, as suggested by the reviewer and to strengthen our data, in addition to the quantifications already provided in the manuscript (e.g. Fig. 2d: AIS length of NF186TAG constructs; Fig. 3f: AIS length of Nav1.6 TAG constructs; Fig. 5d: click-labeling intensity of LOF mutants), we intend to quantify the differences between labeling ratios of different mutants and transfection methods. When it comes to the different transfection methods, some data is already provided in the manuscript (e.g. we counted number of transfected versus transduced neurons) but we intend to clarify and expand on this in the revised manuscript.

1. The only quantification done was for the average AIS length, but the statistical tests should be performed between different conditions and the corresponding P values should be provided. It seems that the transfected neurons generally have a longer AIS length than the transfected neurons (Fig. 2d and 3f). Could the authors provide an explanation for this?

We are a bit confused by the first part of this comment. We measured the AIS lengths of NF186 WT or NF186 TAG as well as Nav1.6 TAG and compared it to the AIS lengths of surrounding untransfected cells (Fig. 2d and Fig.03f). In addition, we compared the AIS lengths of the NF186 WT and TAG to each other, and Nav1.6 TAG to each other. To analyze the differences, we performed statistical tests and provided the corresponding p values in the figure legends (Fig. 02 and 03). Further details on the statistical analysis are provided in supplementary tables (Suppl. table 01 and 02). Regarding the 2nd question, we have also noticed that the AIS lengths of transfected neurons appear longer than those of untransfected cells. This seems to be more pronounced in the case of NF186 which is expressed at the higher level compared to the Nav1.6. The appearance of slightly longer AIS is most likely the consequence of the fact that recombinant constructs are overexpressed in the neurons that express endogenous NF186 and Nav1.6. However, this difference in the AIS length is not significant to the controls. We will discuss this further in the revised manuscript.

1. The authors claim that there was no obvious difference in the nanoscale organization of the NaV1.6WT 317 -HA or NaV1.6TAG 318 -HA channels (Fig. 4. e-g), but it is hard to conclude this without any quantification and statistical analysis. Sodium channels have been shown to be associated with the membrane-associated periodic skeleton structures in neurons and average autocorrelation analysis has been developed to quantify the degree of periodicity of such structural organizations (Han et al. PNAS 114(32)E6678-E6685, 2017). The authors should use this approach to quantify and compare the average autocorrelation amplitudes.

We are thankful to the reviewer for suggestions on how to quantify the periodicity of recombinant sodium channels and how to more accurately compare WT and TAG mutants at the nanoscale level. We will perform additional experiments and analysis in order to address the concerns of this and other reviewers.

1. The authors should also obtain dSTORM images for the click labeled neurons to demonstrate if the click labeling method would provide sufficient labeling efficiency for dSTORM, compared to immunostaining (HA and Ankyrin G immunostaining).

We would like to thank the reviewer for this suggestion. We have already shown in our previous work that STED can be performed with click labeled neurons (PMID: 35031604). When it comes to this manuscript and AIS labeling, we have already obtained preliminary dSTORM images of click-labeled NF186. Since the expression of Nav1.6 is lower compared to NF186, the labeling is also less bright and dSTORM is a bit more challenging. To try to overcome this issue, in addition to dSTORM of click-labeled Nav1.6, we are planning to try click-PAINT (PMID: 27804198). Click-PAINT has been used for super-resolution imaging of less abundant targets in cells and could possibly allow super-resolution imaging of Nav1.6. We will report on these new experiments in the revised version of the manuscript.

1. It seems that the click labeling has a off-target/background labeling in the soma of the neuron (see Fig. 3c,d. Could the authors quantify and determine the sources of such off-target labeling?

We thank the reviewer for pointing this out. We will clarify this in the revised manuscript, but by looking at the other examples from our dataset it appears to us that this background is present in WT constructs as well. In the current version of the manuscript, this is not clear since the WT image that is shown in the Fig. 03b is a single plane confocal image. Therefore, we will replace it in the revised manuscript with a z-stack in which the presence of the background is more obvious (due to the maximum intensity projection). In addition, we will conduct additional control experiments to clarify this.

Minor comments:

1. The authors should indicate how many replicates were performed and how many cells were analyzed for each experiment.

We thank the reviewer for bringing this up. By mistake, we omitted this important information. We will include this information in the revised manuscript, but we would like to highlight here that each experiment was repeated at least 3 times.

1. The display range (i.e., intensity scale bar) was indicated only for a small portion of the fluorescence images. It is better to be consistent and show the display range for all images presented.

We will include intensity scale bars in all the images in the revised version of the manuscript.

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

Not applicable.

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

Reviewer #3, comment #5. One application presented in this manuscript is to evaluate the effect of epilepsy-causing mutations of Nav1.6. By comparing the intensity of ATTO488, the result suggests that there is no significant impact of these mutations on membrane tracking. I am wondering if the author should study the membrane tracking by also looking at the diffusion in live-cell with the labeling method. The comparison of the intensity only can be achieved by just immunostaining. It doesn't really demonstrate the benefit of live-cell labeling and imaging with the presented method.

Generally speaking, one of the advantages of click labeling is its compatibility with live cell labeling. As the reviewer also points out, this is especially useful for live-cell imaging but is not limited to it. In addition, click labeling allows selective labeling of membrane population of Nav1.6 in living neurons. We took advantage of this and used cell-impermeable dyes to label unnatural amino acids incorporated into extracellular part of Nav1.6 (Scheme 03a). On the contrary, HA tag that allows immunodetection of recombinant Nav1.6 is added to the intracellular C terminus. Hence, by anti-HA immunostaining total (intra- and extracellular) epilepsy-causing Nav1.6 channel population will be detected. That is why in this case live-cell click labeling was advantageous compared to the conventional immunostaining. We will clarify this in the revised manuscript. In addition, we would like to note that when we started the experiments with the epilepsy-causing mutations, we wanted to a) check if they are present on the membrane and b) depending on the outcome of those experiments follow the trafficking of these LOF Nav1.6 mutants. Since patch clamp recordings of pathogenic Nav1.6 showed loss of Na+ currents, we at first assumed that they are not properly expressed on the membrane. However, our click labeling showed that the pathogenic channels were detected at the AIS membrane despite the loss of Na+ currents. This was also somewhat surprising to us and we would love to investigate this further. We also appreciate the reviewer’s suggestion in this regard and we hope to be able to use all the advantages of our labeling approach in our follow-up studies. However, keeping in mind time and resources limitations, live-cell trafficking study might be beyond the scope of this revision.

bring responsiveness to post-code software processes

方法论 #文档先行

Author Response

Reviewer #1 (Public Review):

In their manuscript "CompoundRay: An open-source tool for high-speed and high-fidelity rendering of compound eyes", the authors describe their software package to simulate vision in 3D environments as perceived through a compound eye of arbitrary geometry. The software uses hardware accelerated ray casting using NVIDIA Optix to generate simulations at very high framerates of ~5000 FPS on recent NVIDIA graphics hardware. The software is released under the permissive MIT license, publicly available at https://github.com/ManganLab/eye-renderer, and well documented. CompoundRay can be extraordinarily useful for computational neuroscience experiments exploring insect vision and robotics with insect like vision devices.

The manuscript describes the target of the work: realistic simulating vision as perceived by compound eyes in arthropods and thoroughly reviews the state of the art. The software CompoundRay is then presented to address the shortcomings of existing solutions which are either oversimplifying the geometry of compound eyes (e.g. assuming shared focal points), using an unrealistic rendering model (e.g. local geometry projection) or being slower than real-time.

The manuscript then details implementation choices and the conceptual design and components of the software. The effect of compound eye geometries is discussed using some examples. The speed of the simulator depending on SNR is assessed and shown for three physiological compound eye geometries.

I find the described open source compound eye vision simulation software extraordinarily useful and important. The manuscript reviews the state of the art well. The figures are well made and easy to understand. The description of the method and software, in my opinion, needs work to make it more succinct and easier to understand (details below). In general, I found relevant concepts and ideas buried in overly complicated meandering descriptions, and important details missing. Some editorial work could help a lot here.

Thank you for the very positive feedback.

Major:

1) The transfer of the scene seen by an arbitrary geometry compound eye into a display image lacks information and discussion about the focal center/ choice of projection. I believe that only the orientation of ommatidia is used to generate this projection which leads to the overlap/ non-coverage in Fig. 5c. Correct? It would be great if, for such scenarios, a semi-orthogonal+cylindrical projection could be added? Also, please explain better.

For clarification, CompoundRay allows for a number of projection modes from any 3D sampling surface to visualised 2D projections. This has now been made clearer with an updated Methods section “From single ommatidia to full compound eye” (lines 171-188), and also a more clarified explanation of the display pipeline within the “CompoundRay Software Pipeline” section (lines 245-247).

We note that Fig 5 is simply intended as an example of the extreme differences in information that can be provided by nodel (the current state of the art) and non-nodal imagers (as in biological systems). A user could indeed produce custom projections (as now noted in the future work section of the Discussion), such as semi-orthgonal+cylindrical projections by modifying the projection shaders but we do not feel that this adds substantially to the desired message of Fig 5 as currently all view images are generated using the same projection method allowing them to be compared. Further to this, a semi-orthogonal+cylindrical projection would only serve to display these types of eyes and not be of significant use outside of this category of design. Rather, the utility of CompoundRay for research is now demonstrated by the inclusion of an entirely new example experiment (lines 394-467) (Fig 10) which compares artificial and realistic compound eye models in a visual tracking task.

In additional we note that specific references to the “orientation-wise spherical mapping” of images have been added to appropriate image captions (Fig 5 & 6).

Finally, we have attempted to be more explicit about about the way that 2D projection systems work within CompoundRay (182-185)

2) It is clear that CompoundRay is fast and addresses complex compound eyegeometries. It remains unclear, why global illumination models are discussed while the implementation uses ray casting to sample textures without illumination which is equivalent to projection rendering which runs fast on much simpler hardware. If the argument is speed and simplicity of writing the code, that's great, write it so. If it is an intrinsic advantage of the ray-casting method, then comparison with the 'many-cameras' approach sketched below should be done:

In your model, each ommatidium is an independent pin-hole camera. Instead of sampling this camera by ray-casting, you could use projection rendering to generate a small image per ommatidium-camera, then average over the intensities with an appropriate foveation function (Gaussian in your scenario, but could be other kernels). The resolution of the per-camera image defines the number of samples for anti-aliasing, randomizing will be harder than with ray-casting ;). What else is better when using ray-casting? Fewer samples? Hardware support? Possible to increase recursion depth and do more global things than local illumination and shadows? Easier to parallelize on specific hardware and with specific software libraries? Don't you think it would make sense to explain the entire procedure like that? That would make the choice to use ray-casting much easier to understand for naive readers like me.

Thanks for this feedback, and can see that it was misleading to include this in our previous Methods section. We have now reduced and moved discussion of global illumination models to the future work section at the end of the Discussion. We have also added a clarification to the end of this document that summarises this point as it was raised by multiple reviewers (see Changes Relating to Colour and Light Sampling)

3) CompoundRay, as far as I understand, currently renders RGB images at 8-bitprecision. This may not be sufficient to simulate the vision of arthropod eyes that are sensitive to other wavelengths and at variable sensitivity.

Thanks for pointing out this easy-to-miss implementation detail. Indeed, you are correct that the native output is at 8-bit level as is standard to match display equipment. However, we note that the underlying on-GPU implementation operates at a 32-bit depth, so exposing this to the higher-level Python API should be possible, which could then be used as you suggest. We view adding enhanced lighting properties including shadows, illumination and higher bit depths so as to better support increased-bandwidth visual sensor simulation as future updates which we have now outlined in the Discussion (line 549-553).

Reviewer #2 (Public Review):

In this paper, the authors describe a new software tool which simulates the spatial geometry of insect compound eyes. This new tool improves on existing tools by taking advantage of recent advances in computer graphics hardware which supports high performance real-time ray tracing to enable simulation of insect eyes with greater fidelity than previously. For example, this tool allows the simulation of eyes in which the optical axes of the ommatidia do not converge to a single point and takes advantage of ray tracing as a rendering modality to directly sample the scene with simulated light rays. The paper states these aims clearly and convincingly demonstrates that the software meets these aims. I think the availability of a high-quality, open-source software tool to simulate the geometry of compound eyes will be generally useful to researchers studying vision and visual behavior in insects and roboticists working on bio-inspired visual systems, and I am optimistic that the describe tool could fill that role well.

Thankyou for the positive feedback.

As far as weaknesses of the paper, the most major issue for me is that I could not find any example of why the additional modeling fidelity or speed is useful in understanding a biological phenomenon. While the work is technically impressive, I think such a demonstration would increase its impact substantially.

An example experiment has been added as requested.

I can identify a few more, relatively minor, weaknesses: the software tool is not particularly easy to install but I think this is due primarily to the usage of advanced graphics hardware and software libraries and hence not something the authors can easily correct. In fact, the authors provide substantial documentation to help with installation.

Indeed, we have tried to ease installation as much as possible by provided detailed documentation. This has been updated since initial submission and proven sufficient for multiple users. We have looked into dockerising the code but as correctly identified by the reviewer there are significant challenges due to proprietory hardware and their drivers.

Another weakness of the tool, which the authors might like to address in the paper, is that there are some aspects of insect vision and optics which are not directly addressed. For example, the wavelength and polarization properties of light rays are hardly addressed despite extensive research into the sensation of these properties. Furthermore, the optical model employed here is purely ray based and would not allow investigating the wave nature of light which is important for propagation from the corneal surface to the photoreceptors in many species.

Indeed, it is correct that the current implementation does not allow such advanced light modellign features but as our initial aim was to allow arbitrary surface shapes this was considered beyond the scope of this work. However, we have added a short description of extensions that the method would allow without significant architectural changes which include many of those listed by the reviewer. As the renderer simulates light as it reaches the lens surface, it is hoped that further works will be able to use this natural boundary between the eye surface and it’s internals to build further computational models that use the data generated in CompoundRay as a starting point to then simulate inside-eye light transport.

This is why you put script tags at the bottom of an html document.

Feedback and stigmergy are two key motivations for contributing to online communities.

Evaluation Summary:

This is an important paper querying odor responses in the olfactory bulb at low concentrations. Classical studies have revealed a 'combinatorial code' for odorant recognition, with individual odorants represented by combinations of broadly tuned and low-affinity olfactory receptors. Here, the authors perform a large-scale analysis of odor responses across glomeruli and surprisingly observe that odorant receptors instead generally display remarkably narrow tuning profiles.

(This preprint has been reviewed by eLife. We include the public reviews from the reviewers here; the authors also receive private feedback with suggested changes to the manuscript. Reviewer #1 and Reviewer #2 agreed to share their name with the authors.)

这也许是个可行的idea

I think this phrase describing the Colonel will be important throughout the novel. I do we write code to trace this collocation "wicked Colonel"?

I think that "superstition" is a keyword in The Moonstone. How do I write code to track each sentence/phrase in which "superstition" appears?

See also: wikis[1] vs anti-wikis

1. https://www.colbyrussell.com/2020/05/13/psa-wikis.html

This directly contradicts the earlier claim that irreducible complexity is the culprit behind the size of the node_modules directory.

35 MB → "a couple hundred kilobytes"? Clear evidence of not just reducibility but a case of actual reduction...

DOI: 10.1016/j.celrep.2022.111043

Resource: (IMSR Cat# CRL_207,RRID:IMSR_CRL:207)

Curator: @Naa003

SciCrunch record: RRID:IMSR_CRL:207

What is this?

I don't think this is a consecrated expression. If I'm right, it is clunky and should be replaced by The code designed to produce graphs from the Zotero [...] could then be used similarly on other Zotero libraries.

This sentence is convoluted and should be rewritten.

This should be a footnote.

This doesn't mean much

...allows users to combine live code and visualization in one notebook)... ?

...simple syntax and readability.

Capital letters at the beginning of each item, stay consistant (First, Second, Third, Fourth OR We, We, We, We OR reverse the orders to have no first-person plural and start with The, The, The, The).

...see both the result of one's and other's code at the same time...

The following lines present my participation to this event and the code designed

code review

there is definite need for more data to support a more thurough model

split up the table and also the code samples

bullet these. For the last point use the code format for the statuses.

Change the word "Request #1" in the code sample to "Curl"

Reviewer #2 (Public Review):

The authors wish to investigate how various allocentric representations, such as those observed in the brain's navigational system, can emerge from the interaction between action and sensory inputs. They use a predictive architecture, in which visual inputs are predicted from actions, to explain the emergence of multiple allocentric representations (HD cells, place cells, boundary vector cells). The major strength of the paper is the demonstration of the network's ability to develop spatial representations of multiple virtual environments and the demonstration that such representations can be used as a foundation to quickly represent new environments and to support further reinforcement learning tasks. However, the analysis is not yet sufficient to support a number of claims made in the paper about critical pieces of the findings. Further, two critical aspects of the model, namely the correction step, and the RNN-3 memory store, are not adequately described, rely on decisions that are not adequately justified, and their properties/significance are not adequately investigated. Thus, while the authors did demonstrate the emergence of spatial representation and the utility of their model, their presentation did not adequately support their conclusions. With significant revisions to the text and additional experiments/analysis, this work will have a significant impact on the field, and their model will be of further use to the community.

My major concern is that two critical aspects of the model, namely the correction step, and the RNN-3 Memory store, are not adequately described, rely on decisions that are not adequately justified, and their properties/significance are not adequately investigated, as discussed below.

Correction step

- In the results, the correction step is minimally described. However, the method is fairly involved. For example, lines 81-82 state that "visual information being communicated only by the activation of slots in the memory stores (Fig 1B)". Similar descriptions are given in lines 102-103 and 125-126. However, the nature of these predictions is not stated in the results or well-diagrammed in Figure 1B. It might help to specify, for example in the figure legend, that further details about this step are provided in Supplementary figure 1. As this is a crucial piece of the model, I recommend that at least a few more sentences be given to this step in the results, which outlines the high-level details of the correction step.

- In the methods, the description of the correction step is inadequate, it's given simply as G(x,x). While this may be appropriate for a machine learning conference proceeding, it's not appropriate for a general journal. The authors should include equations that specify G (as well as F), which could be included in the section "Sigmoid-LSTM and Sigmoid-Vanilla". Further, the authors might want to justify the need for an entirely new RNN cell, rather than another input to the existing RNN. In lines 318-319: "each x~ can be thought of as the result of a weighted reactivation of the RNN memory embeddings by the current visual input." It might be useful to explain the correction code as: "the expected RNN activation given the current visual input's activation of the memory cells".

- Lines 125-126 state that: "RNN-3 received no self-motion inputs, thus being dependent on temporal coherence, and corrections from mispredictions as its sole input". It's unclear why the corrections to this RNN are generated from "mispredictions", and not just visual "corrections", like in the other RNNs. Further, nothing in the implementation of the correction step enforces that it gives "corrections", only that it learns to incorporate information from the current visual input, via the memory store, to the action of the RNNs. They're just occasional information that the network learns to use to update the RNN state as best as possible. While this is presented as a correction, it's unclear what this RNN actually does. Does it learn to simply replace the existing x with what it should be from the memory store (i.e. a correction)? Or does it combine information from x^hat and x^tilde in some complicated way? To understand this, I recommend the authors could compare x^, x~, and x. During the correction step.

- Finally, the authors state that (Line numbers missing), "to correct for the accumulation of integration errors, the RNNs must incorporate positional and directional information from upstream visual inputs as well. This correction step should not be performed at every time step, or the integration of velocities would be unnecessary; in our experiments, it was performed at random timesteps with probability Pcorrection = 0.1." This entails a claim that for Pcorrection=0, errors will accumulate, while for Pcorrection=1, the integration of velocities will be "unnecessary". While this makes intuitive sense, no empirical justification for these claims is shown, and their implications for the model's function and representation are not demonstrated. I would suggest that the authors compare a range of Pcorrection values, for example, p=[1, 0.3, 0.1, 0.03, 0.01], and demonstrate how the network performance and spatial representation vary as a function of Pcorrection. Finally, though less important, it's unclear why this correction is probabilistic. This decision could be justified, e.g. with an experiment comparing the results of probabilistic versus deterministic/periodic corrections.

RNN-3 and Memory store<br /> This seems like a key feature of the model, yet its implementation gets very little attention in the results, and the description is conflicting and difficult to understand.

- Line 142 states that "the allocentric representations of RNN-3 were stored in the external memory slots as a second set of targets - being reactivated at each time step by comparison to the current state of the RNN-3". However, it's unclear what's meant by a "second" set of targets, or why this is unique to RNN-3. From the text, it seems that this could either refer to m(x)_3 (the memory map corresponding to RNN3), or s (the slots). However, from my interpretation of the methods as written, the m(x) parameters are learned, and s are activated by the joint activity of all three RNNs, not just RNN-3 (Equation 4). Why is this written as if it's a separate group of slots unique to RNN-3?

- Further, how is the activity of memory slots assessed? While I can imagine (though not found in the method), how the tuning curves of RNN-1-3 are calculated, because of the confusion with what this set of targets refers to I don't know how e.g. Figure 2E was calculated. I recommend this be included in the methods. Importantly, I recommend the authors expand the description of RNN-3 and its associated memory store in the results, and clarify its description in the methods section.

- Lines 320 and 322 states that the memory store contents corresponding to the RNNs m(x) are optimized parameters, while those corresponding to upstream inputs m(y) are not. However, Line 325 states that all contents are chosen and assigned (m(y), m(x)) := (y, x).

- Finally, no justification was given as to why RNN-3 was added. The authors justify the addition of RNN-2 by stating that "a single RNN receiving all the velocity inputs did not develop the whole range of representations" (Line 101). However, no justification is given for a third RNN that receives no input. As this is a key piece of the results, justifying and understanding its contribution is critical. Does this affect predictive performance, the ability to generalize to new environments, or utility for RL, or is it simply adding a representational similarity to hippocampal place fields and egoBVCs? I recommend that the authors show the results of a network with only RNN-1 and RNN-2, to justify the addition of RNN-3 and demonstrate its utility for prediction.

On the head direction attractor analysis<br /> - Lines 174-176 state, "To investigate how our model incorporates visual information in its representation of heading, we simulated the input of visual corrections (512 images from the training environment), However, this experiment does not tell you "how the model incorporates visual information", but only the response to selected images. The intuitive idea is that the network learns to map distal cues to specific angles, but not ambiguous images. To test this hypothesis, I would recommend that the authors compare the heading direction of the visual correction input to the direction on the attractor activated, i.e. to show that images that give an attractor point match the heading of that image. Further, because the corrections are given through an entirely different RNN cell (G), from that which (presumably) holds the attractor (F), I would recommend that the authors show how the correction input to G interacts with an existing action-driven point on the attractor via F. For example, what if an image is shown that disagrees with the current heading direction?

On the RL agent<br /> - Lines 200-202 state that "self-consistency is an adaptive characteristic allowing spatial behaviour learned in one environment to be quickly transferred to novel environments", and Line 223: "the spatial responses present in the SMP's RNN support rapid generalization to novel settings." While they've shown that the SMP can support RL and generalization, they haven't tested whether its spatial tuning is responsible for the performance. One way they could test this is to replace the SMP input to the RL agent with equivalent rate tuned units as inputs (whose rate is simply what would be expected from the tuning curve of each RNN unit). This experiment could be done for the pre-trained agent (to see if performance is maintained from the tuning curves alone, or if there's more information in the SMP that's being used), and possibly compared to a newly-trained agent.

This is what I've aimed to do with JOSS! These actions can and should be taken at 'edit time', rather than compile time or runtime. It's particularly interesting to see how the code will compile so that users can worry about optimisation if they so choose.

Debugging and debugging software

Debugging is the process of finding and removing errors (bugs) from a software program. Bugs occur in programs when a line of code or a statement conflicts with other elements of the code. We also call errors or defects in hardware bugs.

(comment with good examples of code review comments)

this paragraph seems unnecessary. too much info for this context

Code of Smart Contracts are not legal contracts

these tiny programs are not real contracts, they don't bind the downstream purchasers. And in fact, as we've seen, they can break over time.

data-target is used by bootstrap and it is part of their javascript package so you don't have to write the code to link the two. This links the button to the modal so that when you click the button the modal appears.

We already have QR code stickers on the floor as we are building robots like this for a customer, and we have to test them repeatedly.

Build technology that is acutely aware of its own limitations. How much memory does this program have access to left? How much power is this computer receiving? Will it run out of battery soon? Can we still serve this website?

Data like this can be presented to end users of the software - if broadcast over a server kind of system - or can provide immediate feedback to the computer - say, a scheduler - to decide what tasks to run when if there are many batch jobs to run queued in the background in order to optimize resource usage.

The question becomes, then, how to ensure all of this reading is done in a performant fashion and whether it's worthwhile to evaluate processes based on their resource consumption rather than performing some random OOM killing nonsense to preserve the device.

The best way to handle this really depends on the computer, but it's very clear that we can't morally build technology - or, specifically, write code - without acknowledging its resource consumption.

Reviewer #2 (Public Review):

The authors address a fascinating question: how can we map and identify homologous brain regions between the mouse brain (an important model organism) and the human brain. While previous studies have mostly focused on matching connectivity patterns or morphometric mapping, the authors propose a novel and imaginative approach: to directly register mouse and human brain into a common frame of reference using the spatial expression of homologous genes. To do this, they use the mouse and human whole-brain gene expression datasets from the Allen Institute. Using supervised learning, the authors show that matching gene expression patterns allows for finer-grained cross-species correspondence. In addition, they find that the sensorimotor cortex generally displays greater cross-species correspondence compared to the supramodal cortex.

This is an important step forward in identifying cross-species correspondences. The findings are sure to be of wide interest to the field and will inspire a lot of follow-up work. The work is written up and presented very clearly. The methods are rigorous and I commend the authors for providing their code openly.

Chrome DevTools Protocol

• to : https://hyp.is/_0bDhvkZEeynEB_xcCaxvw/github.com/chromedp/chromedp

This is sort of a failing of the code-as-content thing that we're going for here. Take a page from GPE.

This means, of course, that we can't allow the use of DbD services if the account type is not CC.

Bug 7873 - 2022.0 Modify Initial and Subsequent Filing to only allow DbD services for CC payment account code

These additional payment account types do not seem to be used in IN STAGE. We should probably update our code, including the web app, to reference payment account types by code id instead of code words.

This will certainly affect: * GetPaymentAccountTypeList * GetPaymentAccountList * CreatePaymentAccount * UpdatePaymentAccount * CreateGlobalPaymentAccount

Bug 7872 - 2022.0 Add UI support for new payment account types

Bug 7825 - 2022.0 Add support for new payment account types

Data set followed below shows information of importing to the US from Canada. You do need an account to access the websiteto see the actual import and export data, but it does give us the orign, quantity, destination, product describtion and the HS code.

Bakery import shipments in United States from Canada are 472, imported by 96 Buyers. Top 3 Product Categories of Bakery Imports in United States are HSN Code 230800 : 230800 HSN Code 230910 : 230910 HSN Code 190590 : HS : other: United States imports most of its Bakery from Canada. The top 1 import markets for Bakery are United States. United States is the largest importer of Bakery and accounts for 472 shipments. These facts are updated till 6 Oct 2021, and are based on Volza's United States Import data of Bakery sourced from 70 countries export import shipments with names of buyers, suppliers, top decision maker's contact information like phone, email and LinkedIn profiles.

Data set followed below shows information of importing to the US from Canada. You do need an account to access the websiteto see the actual import and export data, but it does give us the orign, quantity, destination, product describtion and the HS code.

The old adage comes to mind -- 'the fastest way to get code to production is to call it a 'demo.'"

Author Response

Reviewer #1 (Public Review):

In this study, He and collaborators analyse eight samples from six patients with acral melanoma through single-cell RNA sequencing. They describe the tumour microenvironment in these tumours, including descriptions of interactions among distinct cell types and potential biomarkers. I believe the work is thoroughly done, but I have identified a few concerns in their depiction and interpretation of their results.

Strengths:

1) One of the few available single-cell studies of acral melanoma, including a non-European cohort of patients.

2) Data will be very useful to study the immune landscape of these rare tumours.

3) Data include adjacent tissue, primary tumours and a metastatic sample, covering all disease stages.

4) Analyses seem to be carefully done.

Things to improve:

1) Figures need much more description to be understandable, in particular, axes should be clearly labeled and the colour code should be specified

Thank you for your generous comments and suggestions. We have improved the integrity of some figures and added some figure legends. I believe this will further improve the quality of our manuscript.

2) In some places, I would recommend the authors soften their interpretation of their analyses (for example, when they suggest targeting TNFRSF9+ T cells as a novel therapy), as these are nearly all bioinformatic in a small number of samples

As for the conclusions of TNFRSF9, we indeed provided a possibility that TNFRSF9 may serve as a novel therapy. We made some changes to soften the statement. In addition, we have added instructions and explanations in the Discussion section.

3) I don't think the experiments add much to the literature, as these test already known oncogenes on a common, non-acral melanoma cell line. Thanks for your comments regarding the experiments included in our study. We have pointed out this deficiency in the Discussion section, and made some experimental changes. For example, we have removed the TWIST1-related experiments from the main Results section and shown them only as non-focus work in the Supplementary Figure.

It is difficult for us to obtain AM cell lines. No commercial AM cell lines can be purchased in ATCC or ECACC. AM cell lines are more difficult to establish and there are few reports on methods for establishing primary acral melanoma cell cultures (PMID: 22578220, PMID: 17488338). Some Japanese and Chinese researchers have isolated the primary generation of AM cells (e.g., PMID: 17488338, PMID: 22578220, PMID: 34097822), but due to the customs policy and the COVID-19 epidemic, we could not receive them within a short period. Moreover, these studies also stated their limitations; namely, that the stability during serial passaging had not been evaluated. Therefore, it may be very time-consuming to obtain operable AM cell lines for functional assays. However, our research group would like to have the opportunity to separate and culture primary cells in subsequent studies, and improve relevant experiments according to your valuable suggestions. Man thanks again for your comments.

Reviewer #2 (Public Review):

The study presented by Zan He et al dissects the main interactions between malignant and stromal cells present in acral melanoma samples and in adjacent tissues using single cell RNA sequencing. The study describes factors that allow communication between the different cell types, with a special focus on macrophages, lymphocytes and fibroblasts, along with malignant cells. Factors playing a role in cell-cell communication are identified and suggested to be relevant prognostic makers and/or attractive therapeutic targets.

Historically, the study of acral melanomas has been neglected due to the low incidence among Europeandescents and this formed an important gap of knowledge in the field and hindered the development of effective therapies to control the disease. Therefore, studies that address this unmet need in melanoma research are very important and should be motivated. This includes singlecell sequencing studies that allow one to study the complexity of tumours, including microenvironment features that influence the development and effectiveness of certain types of treatment. The present study contributes information on how cells interact in the acral melanoma microenvironment and this could be a first step toward better understanding how these interactions influence acral melanoma development, progression, and therapy response.

However, there are a few points that should be carefully considered. The authors use 3 adjacent tissues (which in theory is composed of normal skin next to a cancer lesion), 4 primary tumor samples, and one lymph node metastasis as a model to study tumor progression. Adjacent tissue is not considered a stage of tumour progression and the sample size is too small to rule out sample-dependent effects. The study is descriptive in nature and could better contextualize the findings regarding what is known for other subtypes of melanomas or other tumours. This is especially important to help readers understand why it would be relevant to study cutaneous melanomas located in acral skin. It would be helpful to explain how different it is from nonacral cutaneous melanoma, and what this study adds compared to other single-cell studies from cutaneous acral and non-acral melanomas.

Thank you for your generous comments. It is not accurate to represent the adjacent tissue samples as ‘tumour progression’, and our study did not want to focus on the tumour developmental process. We have revised related description in the text. Tumour adjacent tissues (ATs) have always been the focus of research on TMEs. Some studies believe that there are a lot of mutations and clone amplification in normal tissues adjacent to cancer, which may be in a pre-cancerous state (PMID: 33004515), and many single-cell studies of tumours have also sampled and paired para-cancer tissues (e.g., PMID: 29988129; PMID: 35303421).

The problem of sample size limits the generality of the results, as we pointed out in the Discussion section. Most acral melanoma (AM) patients opt for surgical resection at an early stage to avoid the possibility of metastasis. Hence, we rarely encounter patients with lymph gland (LG) metastases. We only collected one metastatic sample, because it is very rare in clinic. However, the sample has a high quality, such as a high cell activity of single cell suspension after dissociation (95.30%), and a rich amount of tumour cells and other stroma cells. Therefore, we added its sequencing data into the overall analyses, hoping to contribute to the comprehensiveness of resources and research.

It is important to link this study with the findings regarding what is known for other subtypes of melanomas. We have already supplied the comparison of AMs with non-acral skin cutaneous melanomas (CMs), using the published data. Your comments and advices are entirely helpful to us, and we believe that the current manuscript is more comprehensive and complete.

Reviewer #1 (Public Review):

In this study, He and collaborators analyse eight samples from six patients with acral melanoma through single-cell RNA sequencing. They describe the tumour microenvironment in these tumours, including descriptions of interactions among distinct cell types and potential biomarkers. I believe the work is thoroughly done, but I have identified a few concerns in their depiction and interpretation of their results.

Strengths:

1. One of the few available single-cell studies of acral melanoma, including a non-European cohort of patients.<br /> 2. Data will be very useful to study the immune landscape of these rare tumours.<br /> 3. Data include adjacent tissue, primary tumours and a metastatic sample, covering all disease stages.<br /> 4. Analyses seem to be carefully done.

Things to improve:

1. Figures need much more description to be understandable, in particular, axes should be clearly labeled and the colour code should be specified<br /> 2. In some places, I would recommend the authors soften their interpretation of their analyses (for example, when they suggest targeting TNFRSF9+ T cells as a novel therapy), as these are nearly all bioinformatic in a small number of samples<br /> 3. I don't think the experiments add much to the literature, as these test already known oncogenes on a common, non-acral melanoma cell line.

Sample Code for Bank Account

Sample Code for VPA

The following endpoint adds a receiver to an existing virtual account. Move the endpoint code above the Watch Out

Split the Codes into two Normal and With Payout Details Create two separate code sections

DOI: 10.1016/j.immuni.2022.06.002

Resource: (IMSR Cat# JAX_034860,RRID:IMSR_JAX:034860)

Curator: @sophiastull

SciCrunch record: RRID:IMSR_JAX:034860

What is this?

DOI: 10.1016/j.immuni.2022.06.002

Resource: (IMSR Cat# JAX_004190,RRID:IMSR_JAX:004190)

Curator: @sophiastull

SciCrunch record: RRID:IMSR_JAX:004190

What is this?