Author Response

Reviewer #1:

This manuscript provides evidence that drug administration during a reconsolidation window does not necessarily prevent memory recall, as has been shown by many groups. The authors attempted to replicate several published experiments and despite demonstrating that the drugs had other effects on the animals' behavior and physiology (e.g. weight gain), no effects on memory were observed.

The paper is nicely prepared.

We sincerely thank the reviewer for these kind words and the support to publish our replication efforts.

Reviewer #2:

General assessment:

In this study, Luyten et al. aimed to replicate post-retrieval amnesia of auditory fear memories reported numerous times in the literature. They used a variety of behavioural approaches combined with systemic pharmacological treatments (propranolol, rapamycin, anisomycin, cycloheximide) after reactivation of fear memories. Interestingly, none of the treatments induced a significant decrease of freezing responses during subsequent retrieval tests. Authors strengthened their null results by using Bayesian statistics, confirming the absence of drug-induced amnesia.

Overall, the study is really interesting. Experiments and analyses are very well designed and bring some important findings to the debated topic of post-retrieval amnesia and its clinical relevance.

We are grateful that the reviewer appreciates our work and recognizes the general importance of our null findings. We genuinely thank them for the time that they took to evaluate our paper in detail and hope to provide some clarifications in our responses below.

I have nevertheless several comments for the authors to consider.

-Despite being very detailed, the authors should clarify and uniformize their Methods section and Supplemental information (e.g. number of CS, contexts used...) to improve the understanding of the different approaches. Similarly, methods for the reinstatement protocol (Exp 2) are missing.

We understand that the information in the main text is quite dense, but we explicitly chose to focus on the central message here, i.e., that we applied standard procedures that should have allowed us to detect amnestic effects in consideration of most of the published literature. In addition, the crucial overview of the number of training and test trials, as well as the context that was used for each session is depicted in Fig. 1-3, immediately above the results of the respective experiments.

In the Supplement, we provide a more extensive (and repetitive) report of the experimental procedures. The idea is that the reader can find the most important information in the main text, and all additional details in the Supplement (or in our preregistrations on the Open Science Framework: https://osf.io/j5dgx ). For example, in the main text, it is mentioned that reinstatement in Experiment 2 consisted of two US presentations in context A, one day before the final test (see p. 6 and Fig. 1C). The Supplement (p. 1) adds that the reinstatement session started with 300 s of acclimation, followed by the first US and 180 s later by the second US, and that the rat was removed from the context 120 s after last US onset. For all phases of Experiment 2, the US was a 0.7-mA, 1-s shock.

• In exp 5, tests 1 and 2 are supposed to have 12 CS each. However, only 8 dots are represented on the graph. Did the authors average some freezing values after the initial 4 first CS presentations?

Thank you for noticing this. We did not average freezing values, but just did not measure freezing on all trials, as we were not specifically interested in the concrete freezing levels on each trial, but rather in the overall extinction curve. As mentioned in the legend of Fig. 2, freezing during CS5-7-9-11 was not measured (and hence also not shown). In other words, the 8 dots on the graph represent CS1-2-3-4-6-8-10-12.

-There is an obvious difference in baseline freezing response before the test in Exp 7 (Figure 5A-B). Discussion of these differences is an important point and was thoroughly discussed by the authors in the Supplement.

Thank you for pointing this out.

-Ln 384-387: "... additional Bayesian analyses were carried out that collectively suggested substantial evidence for the absence of an amnestic effect". Despite the "substantial effect" given by the meta-analysis, I am a bit confused by the meaning of an "anecdotal evidence against drug < control" reported in half of the experiments. How do the authors interpret these results?

In short, Bayesian analyses provide evidence that is categorized starting from ‘no evidence’, to ‘anecdotal’, ‘substantial’, ‘strong’, etc. depending on the obtained Bayes factor. Grouping studies with anecdotal and substantial evidence in a meta-analysis can result in overall substantial evidence, which is what we observed here.

Addressing this remark in more detail, we want to point out that the use of frequentist analyses (ANOVAs and t-tests) allowed us to conclude that we could not replicate the amnestic effects of previously published studies – we did not obtain a statistically significant amnestic effect although we had sufficient power to detect the effect sizes that had been previously reported. However, those analyses do not permit us to make inferences about the evidence against an amnestic effect. Bayesian analyses, on the other hand, do allow us to quantify the obtained evidence against an amnestic effect (i.e., the null hypothesis) for each single experiment or by combining the results of several studies. When a single study suggests only anecdotal evidence against an amnestic effect, this implies that we cannot conclude based on that study alone that we have proper evidence for the absence of an effect. Rather, we can only conclude that we have no evidence for the presence of an amnestic effect and weak (‘anecdotal’) evidence for its absence. However, a collective analysis of our studies does lead to the conclusion of substantial evidence for the absence of an amnestic effect overall.

-The effect of cycloheximide on memory consolidation is indeed unexpected. Even if beyond the scope of the current study, what is the authors' hypothesis to explain that cycloheximide in their conditions induced a pro-mnesic effects on the consolidation of fear memories but altered the consolidation of extinction?

As indicated by the reviewer, this is beyond the scope of the current study. We have no additional data on this effect and can only guess at its meaning. Also note that the effect was rather small and disappeared quickly during the test under extinction.

One purely speculative hypothesis is that the injection with cycloheximide was more arousing than the vehicle injection, either due to sensations caused by the substance during injection or due to the rapidly emerging malaise it induced (or a combination of both), which we have documented in the Supplement (p. 5).

In line with work by McGaugh, Roozendaal and colleagues, such arousal around the time of training could, in theory, enhance consolidation of a fearful memory, and thus explain greater fear memory during test (see e.g., Roozendaal & McGaugh (2011), https://doi.org/10.1037/a0026187 ). Then again, a similar argument could be made for improved consolidation of the extinction memory (de Quervain et al. (2019), https://doi.org/10.1007/s00213-018-5116-0 ), which we did not observe. One could suggest that – assuming that we have observed ‘true’ effects here – the arousal component had the upper hand during the consolidation of the fear memory, while the protein synthesis inhibition overruled such effects during consolidation of the extinction memory. As this is all highly speculative, we prefer to not add this to the Discussion.

-Cycloheximide seemed to induced post reconsolidation amnesia of fear memory after extinction training (Exp 8, Fig 3G) but not after single CS reactivation. Can the authors please develop this point? Is it possible that several presentations of the CS is required to destabilise the initial memory trace?

First of all, it is important to emphasize that cycloheximide-treated rats in Experiment 8 (Fig. 3G) froze more during the CSs of Test 2 than control animals, arguing against a drug-induced reconsolidation blockade of the initial fear memory. Furthermore, the obvious within-session extinction during Test 1 in Experiment 8 suggests that it did not function as a typical reactivation-without-extinction session (Merlo et al. (2014), https://doi.org/10.1523/JNEUROSCI.4001-13.2014 ).

In light of the current literature, reactivation with a single CS is by far the most common way to destabilize a memory trace that was formed with one or three CS-US pairings. As mentioned in our paper, this should provide an appropriate degree of prediction error for the memory to become malleable (p. 12).

Theoretically, it is indeed possible that more than one (e.g., two) CS presentations could allow for destabilization of the memory trace, although others who have used reactivation sessions with more than one CS presentation did not find the amnestic effects that they did observe with a single CS (Merlo et al. (2014); Sevenster et al. (2014), https://doi.org/10.1101/lm.035493.114 ).

Reviewer #3:

Luyten et al's study examines the phenomenon of drug-induced post-retrieval amnesia for auditory fear memories in rats, and report that after several experiments using Propranolol, Rapamycin, Anisomycin or Cycloheximide that they essentially observe no disruption of reconsolidation, (i.e., no amnesia). This is a well-executed, written and meticulous study examining an important phenomenon. The author's lack of observing amnesia using these "reconsolidation blockers" highlights an important fact that systemic administration of these drugs at the time of memory retrieval may not robustly influence reconsolidation processes despite what the existing literature may collectively indicate. The author's data clearly indicate this point and it is important the scientific community be made aware of these difficulties in blocking reconsolidation using systemic administration of these drugs.

We are thankful for these generous comments and value the reviewer’s thorough and thoughtful assessment of our work. We also appreciate the reviewer’s position that it is important to get this message across to the scientific community.

This group has previously published similar studies disputing similar phenomena. First highlighting a lack of amnesia following the reconsolidation-extinction paradigm and then more recently demonstrating a lack of amnesia attempting to block the reconsolidation of context fear memories. This is now their third installment focusing on Cued fear memories. Certainly, these findings are important, but arguably the novelty of such findings may be diminished a bit.

We appreciate that the reviewer is well aware of some of our other work in this domain that supports a more general and widespread reproducibility crisis in this field.

Regarding the novelty, one key point to stress here, which is also articulated in the paper (p. 3, 13), is that the current rodent findings (which we could not replicate) are the ones that provide the most direct basis for the clinical translations that have been proposed (e.g., by giving patients a propranolol pill after retrieval of a traumatic or phobic memory, see e.g., https://kindtclinics.com/en/ or Kindt & van Emmerik (2016), https://doi.org/10.1177/2045125316644541 ), and are therefore critical in their own right, not only because of their fundamental scientific relevance, but certainly also in light of their clinical reach.

In one of the "control" experiments where the experimenters administer anisomycin immediately post training, they observe a paradoxical result - they observe memory strengthening instead of the expected blockade of consolidation and amnesia. This result highlights a number of things to consider when we interpret these overall results. For one protein synthesis inhibitors(PSIs) are toxic and when administered systemically usually result in inducing the animals to have diarrhea and generally just makes them sick. This of course will make the animals stressed and agitated and result in increasing their stress and likely amygdala activity. All of this could likely be the reason why the animals exhibited memory strengthening or no impairment in consolidation even with a PSI on board. See PMCID: PMC7147976. Figure 6. In this study, they could rescue the impairment of PSI on consolidation by increasing BLA principal neuron firing. Thus an important take away is something like this could easily be happening in the reconsolidation experiments - that there is no blockade because the animals are stressed either due to PSI on board or because some issues with experimenter/animal interactions, etc lead to higher BLA neural activity and rescue of the reconsolidation process.

We agree that (systemic) protein synthesis inhibitors can induce signs of sickness in the animals (particularly in the first hours after injection) and have provided a detailed description of our relevant observations in the Supplement (p. 4-5). The reviewer is completely correct in stating that this may cause some amygdala activation which could interfere with the amnestic effects that we expected to see, as described in the paper by Shrestha, Ayata et al. (2020), and in line with our reply to Reviewer #2’s first comment regarding our cycloheximide experiment. Yet, effective induction of amnesia with these drugs has repeatedly been reported in the literature.

Nevertheless, although relevant, the current remark has relatively little implications for our findings. In the large majority of our experiments, we did not use these toxic protein synthesis inhibitors (PSIs) (such as cycloheximide and anisomycin), but drugs that have generally been administered systemically throughout the literature (with successful amnestic effects). Furthermore, in the experiments where we did administer systemic cycloheximide or anisomycin, we observed no differences compared to vehicle-treated rats in contextual freezing (e.g., 9% on average in Experiment 7) immediately prior to the crucial test tones (Test 1, 24h after injection) – which argues against high levels of stress or agitation. Moreover, a blinded experimenter could not tell the difference between PSI-treated versus vehicle-treated animals while handling the animals for the test session, and observed no behavioral abnormalities, nor signs of pain or distress, as mentioned in the Supplement. We acknowledge that these experimenter observations may not entirely reflect what is happening in the animals’ amygdala, but they at least go against the notion that PSI-treated animals would be too sick to be tested properly.

I don't think the authors go far enough articulating the important differences between systemic and intra-cranial administration of these drugs. Time is a potential factor. Immediate administration of the drug at high concentration in the target brain region (BLA) versus many minutes until the drug gets to the target region with uncertain concentration levels that may not mirror levels reached with intracranial administration. It's unfortunate the authors were not able to include intra-BLA administration of these drugs in this study. I do not necessarily expect them to do such experiments, since they have already done so much and it is not clear the laboratory has the appropriate expertise to conduct such experiments, but this comparison would be helpful.

We fully agree that our results do not provide any information about the replicability of intracranial administration of drugs to induce post-retrieval amnesia of cued fear memories. We had already clearly acknowledged this in the first version of the paper (p. 11), but have now added an extra section to the Discussion (p. 13) to highlight this point in the new version posted on BioRxiv (Version 2). Notwithstanding the expertise of our laboratory to carry out intracranial infusions, we agree with the reviewer that such experiments are beyond the scope of this article.

It is, however, noteworthy that the drugs that we used in 6 experiments did not necessarily rely on intracranial administration in prior successful studies. Rapamycin, for example, has generally been used systemically (not intracranially). Propranolol has been used either systemically or intracranially in rodents and always systemically in human subjects (healthy and patients). Bearing in mind the timing issue that was raised by the reviewer, we moreover included an experiment with pre-reactivation administration of propranolol (Experiment 4), where the drug was injected 5-8 minutes before the rats heard the reactivation tone.

I think it is important that the authors make some statement of training conditions on cannulated versus cannulated rats. For example, every animal in Nader's 2000 study was bilaterally cannulated targeting the BLA. In contrast every animal in this study underwent no such surgery. I think this is relevant. In my experience non cannulated animals are a bit smarter than cannulated animals and the training conditions across these two differing groups may not equate to the same level of learning. And of course, differences in learning levels can lead to differences in the ability of the retrieved memory to destabilize.

Thank you for pointing this out. We are aware that there may be differences between operated and non-operated animals and already briefly discussed this matter in the Supplement (p. 4). We have now also added this issue to the Discussion in the new section (p. 13) where we emphasize the differences between systemic and intracranial drug administration in relation to the previous comment.

That being said, the comment regarding (non-)cannulated rats only really applies to Experiment 7 where we tested the effects of systemic anisomycin or cycloheximide. Prior cued fear conditioning studies indeed used intracranial administration of these drugs. The argument does not hold for Experiments 1-6, as systemic propranolol and rapamycin have repeatedly been reported to have amnestic effects in non-operated rats, with procedures identical to or closely resembling ours.

The authors mention possibly examining markers of memory destabilization. GluR1 phosphorylation, Glur2 surface levels, protein degradation/ubiquitination have all been used to assess if destabilization has occurred. I do not fully agree with their reasons for not performing such experiments. They could examine some or one of these phenomena across differing training conditions between retrieval, no-retrieval animals. This likely could be informative. However, the authors may not possess the necessary expertise to conduct such experiments, so I'm not stating these experiments need to be completed, but certainly the study could be strengthened with such data.

We agree that including yet more control experiments, using different experimental approaches could further strengthen the study. Nevertheless, the main conclusion of our paper – i.e., reconsolidation blockade using systemic administration of several drugs is considerably more difficult to reproduce than what the literature collectively indicates – is strongly and sufficiently supported by the data that we already report here. Overall, we believe that our conclusion does not require such additional controls. Moreover, even though the comparisons suggested by the reviewer could indeed be scientifically interesting, it is still unclear whether such experiments would provide sufficiently clear cut-offs as to which experimental condition would then allow for adequate memory destabilization and interference.

Experiment 3E - Propranolol without reactivation. I don't see any data for this on the graphs. Am I missing something?

Our apologies for the confusion. The legend shown next to Fig. 1F applies to all panels of Fig. 1, but only Experiment 1 (shown in Fig. 1A-B) contained a no-reactivation group as an additional control. Experiment 3 (shown in Fig. 1E-F) did not. We have moved the legend to the bottom of Fig. 1 to clarify this.

The authors should probably cite this paper too, PMID: 21688892. The authors in this study find no evidence that propranolol inhibits cued fear memory reconsolidation.

Thank you for bringing this to our attention. We were aware of this paper, but it had slipped through the cracks. We have cited it in the new version of the paper (p. 11).

Author Response

We thank the editors for considering our manuscript for publication in eLife and the reviewers for their work. However, we would like to discuss several of their comments.

The key issue seems to be a lack of novelty of our work, which is not correct in our opinion.

We would like to quickly reiterate why we think that our findings are novel and have very broad implications.

The importance of polygenic adaptation is becoming increasingly clear. Unfortunately, it is widely assumed that polygenic adaptation is very difficult, if not impossible, to study in natural populations, because the associated allele frequency shifts are too small to be experimentally characterized (Pritchard et al., 2010). Hence, typically the collective response of many loci are considered, which frequently results in wrong results due to population stratification (Berg et al., 2019; Sohail et al., 2019).

Therefore, we have used experimental evolution to characterize polygenic adaptation. Experimental evolution is widely recognized as a powerful tool because of the possibility to replicate experiments. Here, we expand the power of experimental evolution by an hitherto unrecognized aspect: the impact of linkage disequilibrium - we demonstrate that two founder populations with different levels of linkage disequilibrium (LD) result in entirely different selection responses. The consequence of different LD structures is shown by our observation that the same population (i.e. identical LD structure) evolving in two different environments shows the same selection response, but a different population with different LD structure in the same environment shows different selection responses.

This result has important implications for all studies of polygenic adaptation in natural populations because LD is not accounted for in studies of polygenic adaptation, but like in our study, haplotype blocks with multiple loci could result in a strongly selected allele. Hence, LD will determine the likelihood of this to occur. Furthermore, accounting for linkage provides the opportunity to study polygenic adaptation also in natural populations - a substantial change to the current testing paradigms.

The second key result of our study is that we demonstrate that selection in hot and cold environments does not fit the simple model of polygenic adaptation, where the same set of loci is responding in different directions, when opposing selection regimes are applied. As pointed out by reviewer #2, this is particularly important as it shows that current models of polygenic adaptation are not well-suited to understand adaptation imposed by contrasting ecological factors. We show that there is almost no overlap between the haplotype blocks selected in the hot and cold environment. Most importantly, this is not a matter of power as we show that the blocks responding in one selection regime are not changing their frequency in the opposite direction in the other selection regime. We anticipate that this insight will have a profound impact on theoretical models of polygenic adaptation. Furthermore, as we studied temperature adaptation, our results will have also important consequences for the battery of ongoing studies aiming to link selection signatures to response to climate change.

In brief, we think that very minor clarifications in our manuscript can solve the technical issues identified by the reviewers and will provide a clearer picture about the general implications of our findings.

A detailed response to the comments of the reviewers is given below.

Reviewer #1:

Otte et al. used an evolve and re-sequence strategy to explore "the genetic architecture of adaptive phenotypes". The authors previously found different genetic architectures across different founder populations evolving in a common hot environment. The authors chose one of these founder populations for replicated experimental evolution (5 replicate populations) in a cold environment for 50 generations. The authors were surprised to discover the same number of loci evolve under strong selection between the hot-evolved and cold-evolved replicate populations, though the 20-ish loci are largely non-overlapping. The distribution of selection coefficients was also similar. They interpret this commonality as evidence that the founder population history has a larger effect on adaptive architecture than the selection regime.

The study demonstrates a comprehensive effort to discover the number of genome regions and distribution of selection coefficients that emerge from a highly controlled experimental evolution project. The experienced team applies a sophisticated toolkit to this powerful experimental design - a toolkit that grows ever more sophisticated with each new experimental run that they perform. However, the authors set me up to learn why such different adaptive architectures emerge from different founder populations. Ultimately, the researchers acknowledge that they "cannot pinpoint the cause for the differences in the inferred adaptive architecture..."

Here, the reviewer correctly identified one of the main new questions that arose from the new experiment we performed in this study. In a large part of the discussion and the associated analyses we are providing answers to this question, i.e. possible alternative explanations for the different observed architectures in the Portugal vs. the Florida population. We can indeed not pinpoint "the" cause for the differences that the reviewer seems to request here as a definite answer, but we favour one of the explanations that has not yet been discussed in literature previously (LD).

Some results simply recapitulated the previous Portugal E&R study and other results recapitulated a D. melanogaster E&R study.

This statement about "some results" is ignoring the main new experiment of this study, which is the Portugal population evolving in a cold temperature. For this, we carried out a new selection experiment in a new environment, which finds different selection targets than the previously published experiments. This new experiment therefore does not recapitulate the previous results. We then compare this new experiment to a previous one, and this comparison raises a set of new questions that we address in this manuscript. Only for the purpose of making that comparison, we indeed "simply recapitulated" "some results" of the previous study. The statement is therefore misleading in the way it is put here. Furthermore, the D. melanogaster study is also not recapitulated: in that study, it was not possible to identify selected haplotypes. The D. melanogaster study was therefore unable to determine how many selection targets were shared between the hot and cold selection regimes. The identification of selected haplotypes was a major improvement in this study, which made it possible only now to determine how many targets are shared and to evaluate whether selection targets behave as predicted by the trait optimum model.

I did not find the "common adaptive architecture" across different selection regimes to be a particularly compelling discovery of sufficiently broad interest.

This is a very subjective opinion and it would be good if the reviewer had explained why this is no interesting discovery to her/him. We feel that this statement simply reflects that the reviewer does not fully appreciate the complexity of polygenic adaptation. We would like to point out again, that this result has important implications for the interpretation of selection signatures in natural populations.

Other concerns and questions can be found below:

Major concerns:

1) Pg. 4: It is my understanding that the power of multiple populations from a single founder evolving in parallel allows for more rigorous identification of loci targeted by selection. I found it surprising to discover that if a lack of replication emerges from an experimental evolution study, this outcome is interpreted as "genetic redundancy." First, genetic redundancy has a precise definition in genetics that muddles the author's meaning. And second this interpretation seems rather post-hoc.

This statement shows that the reviewer is disregarding the work of Barghi et al (2019, PLoS Biology) and the definition of redundancy in the context of polygenic adaptation as discussed by Laruson et al. (2020) or Barghi et al 2020 (Nature Reviews Genetics). In any case, this is a semantic issue and should not be considered as a major issue with our manuscript.

2) To "shed more light on the different selection responses" is a weak motivation. The introduction sets me up to understand why selection responses are so different but no major insights into the "why" emerge from the cold-adaptation experiment.

We modestly disagree - we clearly discuss different explanations of “why” and favor one of them (LD)

3) More explanation of figure 1 in the main text is needed. Does each point correspond to a SNP that consistently changes across all five populations? Or is this the union?

The reviewer does not seem to be familiar with the statistical analyses that have been used in our study in the same way as it is common practice in the field. Despite the common use of this test, we still provided a detailed explanation in M&M and explicitly mentioned the test in the figure legend. But this can easily be detailed even further and should not be a major issue with this manuscript.

4) Line 210: How did the researchers define "stress" and determine that the degree of stress is equivalent across two temperature regimes? The absence of these data undermine the potency of the comparison.

It is not clear why the reviewer requires a more elaborate definition of temperature stress - the concept of extreme temperatures imposing stress is well established and we cite the relevant literature for Drosophila in the text. Furthermore, it is not apparent why the reviewer requests the degree of stress to be equivalent between the two temperature regimes.

5) How can the authors be sure that the only difference between the hot and cold populations was temperature? Was competition/population size/etc held constant? Might the lack of overlap between hot and cold adapted loci stem from one such regime selecting for a different phenotype? (i.e., not temperature tolerance)

As clearly stated in M&M, the culture conditions were the same with the exception of temperature.

6) Line 237: The authors assert that most alleles show a temperature-specific response - a discovery with precedent in the literature, including from this team of researchers. The authors attribute the absence of common loci between temperature regimes to the high number of generations (50) compared to the number across seasons cited in Bergland et al. The researcher could easily look for common targets at earlier time points of experimental evolution to test this idea.

This is an interesting suggestion, but the reviewer fails to explain why the analysis of early generations should be more informative than the analysis of later generations. Several studies have already documented the opposite.

7) Line 292-293: This section reads as disingenuous - the researchers could have explored overlap between Portugal and Florida founders using only the selected loci coordinates and look for non-random overlap using simulations/resampling tests.

The reviewer seems to assume that we could easily apply the same test for overlap that we used for the hot vs. cold comparison within the Portugal population to the Portugal hot vs. Florida hot comparison. But this is not feasible, and we clearly explain why the comparison of selected haplotype blocks between different founder populations is not helpful (low LD results in different haplotype blocks - even with the same target)

8) Discussion: The speculation about why such different architectures emerged across Portugal and Florida was diluted by the absence of initial fitness estimation upon subjection to a cold environment (which would have offered evidence for different initial "optima" across founder populations) as well as the change in fitness from generation 0 to generation 50.

It is not apparent why the reviewer requests a fitness estimate at the cold environment. Our analysis only included a single population in the cold environment. Hence, the only informative comparison is the one in the hot environment which has been done for both populations and is referenced in the manuscript.

9) The simulations and corresponding discussion would make for an interesting review/opinion piece but not as new results for this manuscript.

Unlike the reviewer, we think that a good discussion puts the results into perspective with different hypotheses on how to explain it and link this to the current literature.

Minor Comments:

1) Pg. 3. The recurrent citation of Barghi et al. in the Introduction undermined the reader's impression that fundamental questions are being addressed in this article.

Maybe it escaped the reviewer’s attention that we cited three different Barghi et al. papers and only one reports experimental data (cited only once), while the others are required to describe the theoretical framework, including the concept of "redundancy" which the reviewer misunderstood. New fundamental questions in this current manuscript are addressed using the Portugal population, which was selected in a cold temperature regime (not hot-evolved Florida, which was the topic of Barghi et al. 2019).

2) Lines 33-39: The argument that parallel signatures of selection across distinct natural populations are insufficient to address the polygenic basis of adaptive phenotypes, and so comparatively more contrived E&R studies are required, was unconvincing.

Unfortunately, the reviewer does not provide support for this strong statement. In fact, we find the statement of “contrived E&R studies” not as objective as we would have liked to see in a scientific discourse.

3) Line 158: Confusing. Should "among" actually be "within"?

The reviewer is not right - the correct wording is "among" not within: multiple different haplotypes can carry the actual target of selection, and they can differ by additional variants which themselves are not selected for. Multiple haplotypes with the selection target are also experiencing more pronounced frequency changes than expected under neutrality. The correlation of their allele frequency trajectories depends, however, on the extent that hitchhiking SNPs are shared among these haplotypes. To account for this, we used a less stringent correlation cutoff.

4) Line 486: I believe that the authors would be hard-pressed to find in the literature a paper declaring that "single population...[is] sufficient to understand the genetic basis of adaptive traits".

In fact, many selection tests are targeting only a single population and most studies only apply them to a single population.

Reviewer #2:

This reviewer mainly asks us to discuss some of his/her ideas - this can be done, but since reviewer#1 felt already that there is too much discussion in our manuscript this is a bit of a mixed message.

Overall Review: This is another commendable study from the Schloterer lab that features next generation genome-wide sequencing of multiple evolving populations. It compares results obtained with two different selection regimes, one hot and one cold, and two different founding populations of Drosophila simulans, one from Portugal and one from Florida. The results reveal a lack of consistency among selection regimes and founding populations. Temperature-dependent adaptation is shown to be "local" or "contingent," rather than globally consistent. My chief recommendations concern the experimental and theoretical contexts within which this study should be interpreted.

Major points:

1) I do not require any additional data collection or statistical revision. My comments are organized in terms of experimental paradigm (A) and theoretical significance (B).

A.

2) The typical paradigm for experimental evolution in this and many other labs is the use of hybrid populations created from isofemale lines. This method for founding experimental populations can be expected to generate some degree of random "historicity" as the isofemale lines approach fixation of specific genotypes with high stochasticity. Then there are further stochastic and historical effects which arise when such lines are hybridized. The strengths and limitations of this paradigm should be addressed. Most importantly, such stochastic historical effects might be the source of the discrepancy between the replicate lines derived from Portugal and Florida.

We would like to emphasize that we were using freshly established isofemale lines kept in the laboratory for at most 10 generations, as stated in the M&M section.

3) As the authors themselves point out, there is a comparative difficulty arising from the different scales of replication used for the Florida versus Portugal experiments.

The reviewer is correct, and since we were aware of this, we performed statistical tests to account for this.

A further question for large-scale experimentation is whether a larger and uniform level of replication might produce more similar results, such as 20 evolving populations from each source. Or indeed, three sets of ten evolving populations from three distinct founders from the two sources, with a total of 60 evolving experimental lineages. The authors should discuss whether they believe that their findings would hold up with such an expanded experimental protocol.

This is an interesting thought of its own, but we feel that it does not contribute much to our current study.

4) The authors themselves point out at one point that their experiments might have benefitted from some phenotypic characterization of the presumed temperature adaptation. That raises the more general question of how the field of experimental evolution can progress with some labs just doing phenotypes and other labs just doing genome-wide sequencing. Surely this and other studies would be strengthened by combining the two types of assay. Furthermore, genomic evolution might be usefully analyzed in terms of the degree to which specific genomic changes can be associated with specific phenotypic changes, as that is the foundation for adaptation itself.

We would like to draw the attention to the fact that we performed a laboratory natural selection experiment, for which the environmental factor is known, but not the actually selected phenotype - hence the phenotyping is not as trivial as implied by the reviewer.

B.

5) This is yet another study that finds difficulties with the invocation of noroptimal selection along a one-dimensional functional gradient. Such models have been long-standing favorites of evolutionary theorists, such as Kimura and Lande. But that preference may arise more from the ease with which these models can be formulated and analyzed by theoreticians. Actual evolving populations don't seem to embody the precepts of such theory, whether the issue is the maintenance of genetic variation (see the work of Turelli, for example) or the evolution of closely studied populations, as illustrated by this study. An alternative point of view that the authors should discuss is that such models are indeed NOT usually correct.

It is very interesting that this reviewer feels that our data demonstrate that the prevailing model of polygenic adaptation is wrong, but our manuscript is still considered to be of insufficient novelty.

6) There are alternative theoretical frameworks that address the maintenance of genetic variation and the response to selection. Among these are schemes of protected polymorphism arising from overdominance, epistasis, and frequency-dependent selection. If the thrust of the preceding point 4 is accepted, then it would be theoretically salient for the authors to suggest what type of underlying population genetic machinery would best account for their findings, in place of the noroptimal selection-mutation balance model.

We thank the reviewer for these interesting suggestions. However, their predictions are not at all trivial to test. For this reason, generations of population geneticists tried to test them, so we feel that this task is well beyond the scope of this manuscript.

Reviewer #3:

In their manuscript 'The adaptive architecture is shaped by population ancestry and not by selection regime,' Otte and colleagues use an evolve and resequence strategy to examine the response of a Portugal population of D. simulans responds to cold temperature. The authors identify putative targets of selection and compare the number of targets, their location, and the distribution of selection coefficients to previous work on the same population exposed to hot temperatures as well as a different population exposed to hot temperatures. The topic is of general interest, the work is sound and the writing is clear and concise.

1) It is not clear what the novel contribution of this manuscript is. The title indicates that the key finding is that population of origin mediates response to selection rather than the selection regime. However, the authors fail to provide compelling data to support that. The data are from 1 population under two selection regimes and a second population under one of those regimes. There simply aren't enough comparisons to infer that population ancestry plays a bigger role than selection regime in adaptive evolution.

We disagree with the reviewer and would like to repeat the logic of our experiment:

Comparison 1: contrast of different populations in the same environment -> different architecture

Comparison 2: contrast of the same population in different environments -> same architecture

With this simple design it is possible to reach the conclusion that the architecture is affected by population history more than by selection regime and no more populations are needed to reach this conclusion. This insight has not been reported before.

2) The authors also seem to argue that a contribution of this paper is that it illustrates that temperature adaptation is not a single trait. This was the major finding of a 2014 paper from the same group in D. melanogaster- a single founder population was exposed to hot and cold temperatures and the authors found almost no overlap between the putatively selected variants in the two different temperature regimes.

We would like to point out that the analysis of Tobler et al. (2014) is on the basis of individual SNPs, which is difficult to interpret because of the many segregating inversions in D. melanogaster. All the complications of these data and the implications for the interpretation can be found in the discussion of Tobler et al. (2014). In the current study, we are identifying selected haplotype blocks, which is mandatory to compare the architectures and selection responses.

3) Beyond the limited impact of the current work, there are some additional specific issues. The authors note that it was 'remarkable' that the distribution of selection coefficients and the number of inferred selection targets between the hot and cold experiments was 'highly similar.' What is the null expectation? Where does the null come from?

This is a minor semantic issue. Naturally, there is no null model for the number of selection targets, but if two populations selected for the same trait provide different architectures, different selection regimes should be even more likely to generate different architectures.

4) The discussion is somewhat unsatisfying and largely speculative. The 'different trait optima' section reads as straw man; this could be reframed to better guide the reader.

Naturally, the discussion intends to put the results in a broader context. It would have been helpful to read how s/he envisions a reframing that would improve the manuscript.

There is little support for the 'differences in adaptive variation' hypothesis.

It would have been helpful to read which kind of support the reviewer would have expected beyond the evidence we have already provided.

The section on LD was interesting, but the simulation findings should reside in the results section.

This could be easily moved, but we feel that it is well-placed in the discussion as we use the simulations to compensate for the lack of literature on this field (again demonstrating the novelty of our manuscript).

References:

Barghi, N., R. Tobler, V. Nolte, A. M. Jakšić, F. Mallard, K. A. Otte, M. Dolezal, T. Taus, R. Kofler, & C. Schlötterer (2019). Genetic redundancy fuels polygenic adaptation in Drosophila. PLOS Biology 17: e3000128.

Barghi, N., J. Hermisson, & C. Schlötterer (2020). Polygenic adaptation: a unifying framework to understand positive selection. Nature Reviews Genetics . Berg, J.J., Harpak, A., Sinnott-Armstrong, N., Joergensen, A.M., Mostafavi, H., Field, Y., Boyle, E.A., Zhang, X., Racimo, F., Pritchard, J.K., et al. (2019). Reduced signal for polygenic adaptation of height in UK Biobank. Elife 8.

Bergland, A. O., E. L. Behrman, K. R. O’Brien, P. S. Schmidt, & D. A. Petrov (2014). Genomic Evidence of Rapid and Stable Adaptive Oscillations over Seasonal Time Scales in Drosophila. PLoS Genetics 10, e1004775.

Láruson, Á. J., S. Yeaman, & K. E. Lotterhos (2020). The Importance of Genetic Redundancy in Evolution. Trends in Ecology and Evolution 35: 809–822. Pritchard, J.K., Pickrell, J.K., and Coop, G. (2010). The genetics of human adaptation: hard sweeps, soft sweeps, and polygenic adaptation. Current biology : CB 20, R208-215.

Sohail, M., Maier, R.M., Ganna, A., Bloemendal, A., Martin, A.R., Turchin, M.C., Chiang, C.W., Hirschhorn, J., Daly, M.J., Patterson, N., et al. (2019). Polygenic adaptation on height is overestimated due to uncorrected stratification in genome-wide association studies. Elife 8.

Author Response

Note from the authors:

This is the authors' response to the reviewers' comments for the manuscript “Perceptual gating of a brainstem reflex facilitates speech understanding in humans” submitted to eLife via Preprint Review. We appreciate the time and effort the reviewers took to carefully revise our work. We believe all comments and suggestions will improve the manuscript for future publication. All the authors’ comments detailed in this response will be implemented in the next version of this manuscript.

Reviewer #1: [...] Reviewer 1-Comment 1: 1) An important aspect of assessing the efferent feedback through the CEOAEs and ABRs is to ensure that different stimuli have equal intensity. The authors write in the methodology that the speech stimuli were presented at 75 dB SPL. However, it is not stated if this applies to the speech stimuli only, such that the stimuli that include background noise would have a higher intensity, or to the net stimuli. If the intensity of the speech signals alone had been kept at 75 dB SPL while the background noise had been increased, this would render the net signal louder and influence the MOCR. In addition, it would have been better to determine the loudness of the signals according to frequency weighting of the human auditory system, especially regarding the vocoded speech, to ensure equal loudness. If that was not done, how can the authors control for differences in perceived loudness resulting from the different stimuli?

Response to Reviewer 1-Comment 1:

Controlling the stimulus level is a critical step when recording any type of OAE due to the potential activation of the middle ear muscle reflex (MEMR). High intensity sounds delivered to an ear can evoke contractions of both the stapedius and the tensor tympani muscles causing the ossicular chain to stiffen and the impedance of middle ear sound transmission to increase (Murata et al.,1986; Liberman & Guinan,1998). As a result, retrograde middle ear transmission of OAE magnitude can be reduced due to MEMR and not MOCR activation (Lee et al., 2006). For this reason, we were particularly careful to determine the presentation level of our stimuli.

As pointed out by the reviewer and stated in the Methods section: Experimental Protocol: “The speech tokens were presented at 75 dB SPL and the click stimulus at 75 dB p-p, therefore no MEMR contribution was expected given a minimum of 10 dB difference between MEMR thresholds and stimulus levels (ANSI S3.6-1996 standards for the conversion of dB SPL to dB HL)”. 75 dB SPL was indeed selected as the presentation level for all natural, noise vocoded and speech-in-noise tokens. All tokens were root-mean-square normalized and the calibration system (sound level meter (B&K G4) and microphone IEC 60711 Ear Simulator RA 0045 563 (BS EN 60645-3:2007), (see CEOAEs acquisition and analysis section)) was set to “A-Weighting” which matches the human auditory range. Therefore, the net signal was never above 75 dBA. We acknowledge the lack of details about the calibration procedure in the current manuscript and will consequently add them in a future Methods section.

Reviewer 1-Comment 2: 2) Many of the p-values that show statistical significance are actually near the threshold of 0.05 (such as in the paragraph lines 147-181). This is particularly concerning due to the large number of statistical tests that were carried out. The authors state in the Methods section that they used the Bonferroni correction to account for multiple comparisons. This is in principle adequate, but the authors do not detail what number of multiple comparisons they used for the correction for each of the tests. This should be spelled out, so that the correction for multiple comparisons can be properly verified.

Response to Reviewer 1-Comment 2:

Bonferroni corrections were explicitly chosen as the multiple comparisons adjustment across our post-hoc statistical analyses because they are a highly conservative test that protect from Type I error. All the p-values reported in our study are corrected p-values for post-hoc comparisons. However, we agree that for verification purposes, the number of comparisons for each statistical analysis should be clarified in the Methods section and will be added to a future version of the manuscript.

Reviewer 1-Comment 3: 3) Line 184-203: It is not clear what speech material is being discussed. Is it the noise vocoded speech, the speech in either type of background noise, or these data taken together?

Response to Reviewer 1-Comment 3:

Lines 184-203 correspond to “Auditory brainstem activity reflects changes in cochlear gain” in the Results section. Line 186 describes changes in ABR components during noise-vocoded speech: “Click-evoked ABRs—measured during simultaneous presentation of vocoded speech—showed task-engagement-specific effects similar to the effects observed for CEOAE measurements.” The subsequent 3 sentences refer to the same (noise-vocoded) condition, whereas the remaining sentences in the section refer to the speech-in-noise conditions. As pointed out by the reviewer we did not specify a specific masked condition in the sentence: “Conversely, although wave III was unchanged in both masked conditions for active vs. passive listening, wave V was significantly enhanced: [F (1, 26) = 5.67, p = 0.025 and F (1, 25) = 8.91, p = 0.006] when a lexical decision was required.” Here the rANOVAs correspond to masked conditions: speech in babble noise and speech-shaped noise respectively. This will be rectified in a future version of the manuscript.

Reviewer 1-Comment 4: 4) Line 202-203: The authors write that "the ABR data suggest different brain mechanisms are tapped across the different speech manipulations in order to maintain iso-performance levels". It is not clear what evidence supports this conclusion. In particular, from Figure 1D, it appears plausible that the effects seen in the auditory brainstem may be entirely driven by the MOCR effect. To see this, please note that absence of statistical significance does not imply that there is no effect. In particular, although some differences between active and passive listening conditions are non-significant, this may be due to noise, which may mask significant effects. Importantly, where there are significant differences between the active and the passive scenario, they are in the same direction for the different measures (CEOAEs, Wave III, Wave V). Of course, that does not mean that nothing else might happen at the brainstem level, but the evidence for this is lacking.

Response to Reviewer 1-Comment 4:

Lines 202-203 also correspond to “Auditory brainstem activity reflects changes in cochlear gain” in the Results section. As suggested by the reviewer, the effects observed in the ABRs may be driven by the MOCR. We agree with this observation in lines 195-197, explaining that the decreased magnitude of ABR components is consistent with reduced magnitude of CEOAEs measured during active listening in the vocoded condition, since a reduction in cochlear gain can reduce the activity of auditory nerve (AN) afferents synapsing in the cochlear nucleus (CN). However, we did not explain that this trend is also observed during the passive listening of speech-in-noise, therefore demonstrating that vocoded and speech-in-noise are differently processed at the level of the brainstem and midbrain. In a future version of the manuscript, we will restrict our interpretation to statistical comparisons in the Results and leave potential mechanisms for the Discussion section.

Reviewer 1-Comment 5: 5) The way the output from the computational model is analyzed appears to bias the results towards the author's preferred conclusion. In particular, the authors use the correlation between the simulated neural output for a degraded speech signal, say speech in noise, and the neural output to the speech signal in quiet with the efferent feedback activated. They then compute how this correlation changes when the degraded speech signal is processed by the computational model with or without efferent feedback. However, the way the correlation is computed clearly biases the results to favor processing by a model with efferent feedback.

The result that the noise-vocoded speech has a higher correlation when processed with the efferent feedback on is therefore entirely expected, and not a revelation of the computational model. More surprising is the observation that, for speech in noise, the correlation value is larger without the efferent feedback. This could due to the scaling of loudness of the acoustic input (see point 1), but more detail is needed to pin this down. In summary, the computational model unfortunately does not allow for a meaningful conclusion.

Response to Reviewer 1-Comment 5:

While claims of bias would be understandable had we used shuffled auto-correlograms (SACs) to compare the expression of temporal fine structure (TFS) cues for natural speech versus vocoded stimuli (TFS cues reconstructed from the envelope of our vocoded stimuli would have differed dramatically from those original TFS cues in natural speech) (Shamma and Lorenzi, 2013), there is no inherent reason for SAC analysis of envelopes cues being biased towards either vocoded or speech-in-noise conditions as both stimuli retain the original envelope cues from natural speech. Indeed, since the purpose of our simulations was to compare the relative effects of adding efferent feedback on the reconstruction of the stimulus’ envelope cues in the AN for the two degraded stimuli, SACs offered a targeted analysis tool to extract the relevant information with fewer intermediate steps and presumptions than either encoder models or automatic speech recognition systems.

We do agree with the reviewer that results of our simulations for the vocoded condition may have been less unexpected than those of speech-in-noise, as the envelopes of vocoded stimuli closely resemble those of natural speech in the absence of a masking noise. However, our results also demonstrate that adding efferent feedback could generate negative correlation changes for a number of vocoded words: either at individual frequencies (low and high spontaneous rate AN fibres (see raw data)) or on average across all frequencies tested [high spontaneous rate AN fibres only (Fig Supplement 3)]. This suggests that noise-vocoding speech (i.e. implementing the envelope from broader channel bandwidths while also scrambling spectrotemporal information in said channels) can disrupt envelope representation in the 1-2kHz range of certain words enough that efferent feedback should not be automatically presumed able to rectify their envelope cue reconstruction in AN fibres.

As for the speech-in-noise conditions, our intuition for the negative correlation changes observed is that the signal-to-noise ratios (SNRs) tested were not large enough to allow for the isolated extraction of the target signal’s envelope by expanding the dynamic range of AN fibres. As the test stimuli and their SNRs were directly acquired by finding iso-performance in the psychophysical portion of this study (and appropriately normalized as input for the MAP_BS model), we consider the results of the simulation to be indicative of the actual benefit/disadvantage that activating efferent feedback might have on envelope representation of vocoded or speech-in-noise tasks in the AN [and not artefacts of poorly calibrated stimulus presentation level (see Responses to Reviewer1-Comment 1 and 6 for more details about methodology)]. Although this result may be surprising when viewed in the context of physiological and modelling studies demonstrating efferent feedback’s masking effect, our results may help to explain why MOCR anti-masking appears SNR- and stimulus- specific in numerous human studies (de Boer et al., 2012; Mertes et al., 2019).

Reviewer 1-Comment 6: 6) The experiment on the ERPs in relation to the speech onsets is not properly controlled. In particular, the different acoustics of the considered speech signals -- speech in quiet, vocoded speech, speech in background noise -- will cause differences in excitation within the cochlea which will then affect every subsequent processing stage, from the brainstem and on to the cortex, thereby leading to different ERPs. As an example, babble noise allows for 'dip listening', while with its flat envelope speech-shaped noise does not. Analyzing differences in the ERPs with the goal of relating these to something different than the purely acoustic differences, such as to attention, would require these acoustic differences to be controlled, which is not the case in the current results.

Response to Reviewer 1-Comment 6:

Our fundamental methodological strategy was not to compare or even control the acoustics of the signals (although we did this to some extent by normalizing the presentation level and long-term spectrum across all signals), but instead to maintain iso-performance across conditions and, in doing so, allow the identification of brain mechanisms underlaying performance in a lexical decision task where speech intelligibility was manipulated.

We do acknowledge the reviewer’s comment regarding acoustic differences across our speech signals. This is why in the Results section we describe that: “Early auditory cortical responses (P1 and N1) are largely driven by acoustic features of the stimulus (Getzmann et al., 2015; Grunwald et al., 2003)”. Therefore, our ERP analysis instead focuses on later, less stimulus-driven components such as P2, N400 and LPC: “Later ERP components, such as P2, N400 and the Late Positivity Complex (LPC), have been linked to speech- and task-specific, top-down (context-dependent) processes (Getzmann et al., 2015; Potts, 2004).”

With regards to the reviewer’s example: “…babble noise allows for 'dip listening', while with its flat envelope speech-shaped noise does not”. We could argue that in our specific listening conditions “dip listening” did not offer a perceptual advantage over speech in speech shaped noise because:

1) Higher SNR was required in the babble noise conditions to achieve the same level of performance than for the speech-shaped noise manipulations.

2) Listeners have fewer chances to use the spectral and temporal dips compared to sentences(Rosen 2013) when listening to monosyllabic words (used in our study)

3) The dips in the signal are expected to decrease both in depth and frequency with the number of talkers in a babble noise masker (8-talker babble used in our study), with no differences in masking effectiveness for more than 4-talker babble noise (Rosen et al., 2012).

Overall, we believe that having modulated maskers effectively impaired speech intelligibility (Kwon and Turner 2001), but the most effective one was babble noise confirming that the best speech is its own best masker (Miller, 1947).

Reviewer #2: [...] Reviewer 2-Comment 1: 1) A core premise of the experiment is that the non-invasive measures recorded in response to click sounds in one ear provide a direct measure of top-down modulation of responses to the speech sounds presented to the opposite ear. This is not acknowledged anywhere in the paper, and is simply not justifiable. The click and speech stimuli in the different ears will activate different frequency ranges and neural sources in the auditory pathway, as will the various noises added to the speech sounds. Furthermore, the click and speech sounds play completely different roles in the task, which makes identical top-down modulation illogical. The situation is further complicated by the fact that the clicks, speech and noise will each elicit MOCR activation in both ipsi- and contralateral ears via different crossed and uncrossed pathways, which implies different MOCR activation in the two ears.

Response to Reviewer 2-Comment 1:

We employed broadband clicks across all stimulus manipulations and listening conditions to activate the entire cochlea so that resulting OAEs could be used to measure modulation of cochlear gain by olivocochlear efferents.

Historically, studies have applied clicks in one ear (to evoke OAEs) and a broadband noise suppressor in the other to monitor contralateral MOCR activation, demonstrating that clicks are suppressed consistently when subjects actively perform either an auditory (Froehlich et al., 1993, Maison et al., 2001; Garinis et al., 2011) or visual tasks (Puel et al., 1988; Froehlich et al., 1990; Avan & Bonfils 1992; Meric & Collet 1994). Therefore, while we acknowledge that the presence of clicks may have made the task of discriminating vocoded and words-in-noise more difficult, we would have expected to observe suppression of click-evoked OAEs for all stimulus manipulations whether subjects were actively or passively listening to speech stimuli in order to minimize the impact of the irrelevant clicks. In contrast, we observed that contralateral suppression of CEOAEs was both stimulus- and task-dependent. Unlike natural and vocoded speech, active listening of speech-in-noise did not produce significant MOCR activation; while passive listening (equivalent to visual attention) generated an MOCR effect in the opposite direction to their active-listening analogues for all 3 speech manipulations.

Despite spectrotemporal, level and task-difficulty similarities between noise-vocoded speech and speech-in-noise manipulations, the stimulus-dependence of these results suggests that MOCR activation was controlled in a top-down manner according to the auditory scene presented. We speculated that this arises from improved peripheral processing of specific speech cues during active listening, whereas the opposite effects in passive listening are associated with attenuating auditory inputs to prioritize visual information. In line with this, we observed that introducing efferent feedback to our auditory periphery model differentially affected the auditory nerve output for the 3 most challenging speech manipulations: the resulting enhancement or deterioration of envelope cue representation offering an explanation for divergent patterns of MOCR gating for noise-vocoded and speech-in-noise.

In summary, we predict that observed changes in CEOAE amplitudes in the contralateral ear will mirror cochlear gain inhibition in the ear processing speech. Bilateral descending control of the MOCR despite speech being presented monaurally is not unexpected for two reasons:

1) Unlike simple pure tone stimuli, speech activates both left and right auditory cortices even when presented unilaterally to either ear (Heggdal et al., 2019)

2) Cortical gating of the MOCR in humans does not appear restricted to direct ipsilaterally descending processes that impact cortical gain control in the opposite ear instead likely incorporating polysynaptic, decussating processes to affect both cochlear gain in both ears (Khalfa et al., 2001).

Together this evidence makes it difficult to envisage a case where unilaterally-presented speech does not influence top-down control of cochlear gain bilaterally.

Reviewer 2-Comment 2: 2) The vocoded conditions were recorded from a different group of participants than the masked speech conditions. Comparing between these two, which forms the essential point in this paper, is therefore highly confounded by inter-individual differences, which we know are substantial for these measures. More generally, the high variability of results in this research field should caution any strong conclusions based on comparing just these two experiments. A more useful approach would have been to perform the exact same task in the two experiments, to examine the reproducibility.

Response to Reviewer 2-Comment 2:

We ensured that the two populations tested across the three experiments were all normal hearing adults assessed using the same criteria. They were also age- and gender- matched and were recruited from undergraduate courses at Macquarie University (therefore presumably possessed similar literacy); however, we acknowledge this as an important issue and controlled for these issues, as far as we could, by:

1) Ensuring that CEOAE SNRs were above a 6 dB minimum which allowed for more reliable and replicable recordings within and between subjects (Goodman et al., 2013).

2) Carefully analysing and selecting ABR waveforms above the residual noise. Residual noise was calculated by applying a weighted average method based on Bayesian inference that weighs individual sweeps proportionally to their estimated precision (Box & Tiao, 1973). This helped preserve all trials without any rejection required for artefacts. ABR waveforms with residual noise equal to or higher than the averaged signal were discarded.

3) Ensuring that individual ERP components represented a reliable individual average by: a) removing noisy trials (trials between -200 ms and 1.2 sec from sound onset which had absolute amplitude values higher than 75 μV) and b) maintaining between 60-80% of total trials per condition.

In addition, we assessed potential differences across common variables between experiments such as, lexical performance during natural speech (see Results section), ABR components and CEOAE magnitude changes relative to the baseline during the Active and Passive listening of natural speech (as part of the 1st author’s thesis dissertation: Hernandez Perez, H., & Macquarie University. Department of Linguistics, degree granting institution. (2018). Disentangling the Influence of Attention in the Auditory Efferent System during Speech Processing / Heivet Hernandez Perez): “During active or passive listening of natural speech, no statistical differences between the populations assessed in the noise-vocoded and speech-in-noise experiments for: wave V-III amplitude ratio- Active listening [t (12) = 0.90, p=0.39], Passive listening: [t (23) = 1.58, p=0.13]; wave V-Active listening: [t (23) = 0.09, p=0.93]; Passive listening: [t (24) = -0.24, p=0.81]; CEOAE magnitude changes-Active listening [t (23) = -0.21, p=0.83; Passive listening [t (24) = -0.36, p=0.72].”

These results ruled out the possibility that the effects observed across the three experiments were due to intrinsic differences between the populations tested. This would be discussed in a future version of the manuscript and added as supplemental material.

Reviewer 2-Comment 3: 3) The interpretation presented here is essentially incompatible with the anti-masking model for the MOCR that first started of this field of research, in which the noise response is suppressed more than the signal, which is contradictory to the findings and model presented here, which suggest no role for the MOCR in improving speech in noise perception.

Response to Reviewer 2-Comment 3:

Physiological evidence for the MOCR anti-masking effect in animal models (Wiederhold, 1970; Winslow & Sachs 1987; Guinan & Gifford 1988; Kawase et al., 1993) has led to the hypothesis that the MOCR may play an important role in aiding humans to perceive speech in noise (Giraud et al., 1997; Liberman & Guinan 1998). The strictly non-invasive nature of human experiments has made measuring MOCR effects on OAE amplitudes the main technique for testing this anti-masking hypothesis. However, OAE inhibition (the MOCR-mediated reduction in OAE amplitude) has been reported as either increased (Giraud et al., 1997; Mishra and Lutman, 2014), reduced (de Boer et al., 2012; Harkrider and Bowers, 2009) or being unaffected (Stuart and Butler, 2012; Wagner et al., 2008) in participants with improved speech-in-noise perception. More recently, Mertes et al. (2019) suggested that the SNR used to explore speech-in-noise abilities might explain the contradicting results in the literature. The authors found that the MOCR only contributed to perception at the lowest SNR they tested (-12 dB), suggesting that the role of the MOCR for listening-in-noise may be highly dependent on the SNR, which in turns influences the extent to which the MOCR does or does not provide a benefit for hearing in noise. Therefore, our human and modelling data not only expands but also challenges the classical MOCR anti-masking effect by suggesting that, in humans, this effect is not only SNR-specific (which we controlled) but it is also task-specific (i.e whether participants are attending to the contralateral masker or not) and stimuli-dependent (i.e masker intrinsically noisy Vs signal-in-noise). We acknowledge that we can discuss further how our data advances the current state of the MOCR anti-masking effect in a future version of the manuscript.

Reviewer 2-Comment 4: 4) The analysis of measures becomes increasingly selective and lacking in detail as the paper progresses: numerous 'outliers' are removed from the ABR recordings, with very uneven numbers of outliers between conditions. ABRs were averaged across conditions with no explicit justification. The statistical analysis of the ABRs is flawed as it does not compare across conditions (vocoded vs masked) but only within each condition separately (active v passive) - from which no across-condition difference can be inferred. The model simulation includes only 3 out of 9 active conditions. For the cortical responses, again only 3 conditions are discussed, with little apparent relevance.

Response to Reviewer 2-Comment 4:

In regard to the reviewer’s comment “The analysis of measures becomes increasingly selective and lacking in detail as the paper progresses: numerous 'outliers' are removed from the ABR recordings, with very uneven numbers of outliers between conditions. ABRs were averaged across conditions with no explicit justification.” During the analysis of the ABR measurements, we not only dealt with outliers but also with several missing data points (ABR components below the residual noise). The statistical analysis used to assess potential differences within ABR components was rANOVAs. This type of analysis is particularly restrictive when dealing with missing data points, because it will only include participants with all data available: (2 Conditions X 4 Stimuli manipulations for the noise vocoded experiment). This is why, ABR components’ sample sizes across experiments appeared uneven.

Regarding the reviewer’s comment: “ABRs were averaged across conditions with no explicit justification.” Our rANOVA had the following design: Factor 1 (Conditions: Active Vs Passive); Factor 2 (Stimuli: natural, 8 channels noise vocoded (Voc8) …etc) and finally the Interaction (Conditions x Stimuli). ABR conditions were not simply averaged together; we only found a significant Conditions effect in the rANOVA that collapses all stimuli manipulations into Active Vs Passive conditions. Therefore, it was only statistically valid, to make inferences and potential interpretations about the Conditions main effect. This would be clarified in both the statistical design and in the Results section of a future version of this manuscript.

In regard to the reviewer’s comment: “The statistical analysis of the ABRs is flawed as it does not compare across conditions (vocoded vs masked) but only within each condition separately (active v passive) - from which no across-condition difference can be inferred”. Up to this point in our data analysis, we were only interested in within-speech-manipulations comparisons (similar to the CEOAE analysis i.e, within noise-vocoded manipulations). We agree with the reviewer that a simple comparison between speech manipulations (noise-vocoded Vs masked speech) for the variables that are reflecting attentional changes (Active Vs Passive listening) could be useful to infer differences across experiments (noise-vocoded Vs speech-in-noise). This analysis will be added in a future version of the paper.

Finally, regarding the comment:” The model simulation includes only 3 out of 9 active conditions. For the cortical responses, again only 3 conditions are discussed, with little apparent relevance”. At this stage of our analysis, we wanted to understand the potential reasons why the control of the cochlear gain appeared to be dependent on the way speech was being degraded i.e, noise vocoding the speech signal Vs speech-in-noise. Iso-performance being achieved in 3 task-difficulty levels, we thought to test how both the biophysical model and the auditory cortex (ERP components) would respond to the hardest and most challenging speech degradations (noise vocoded 8 channels, speech in babble noise +5 dB snr and speech in speech-shaped noise +3 dB snr) (see Figure 1B in Results section), where differences in the cochlear gain are most evident across experiments (see Figure 1B in Results section). In these extreme conditions we hypothesized that both the model and the auditory cortex activity would display the most obvious differences in the processing of the different speech degradations. We acknowledge the reviewer’s comment and in a future version of this manuscript, this line of thought will be more clearly described.

Reviewer 2-Comment 5: 5) The assumption that changes in non-invasive measures, which represent a selective, random, mixed and jumbled by-product of underlying physiological processes, can be linked causally to auditory function, i.e. that changes in these responses necessarily have a definable and directional functional correlate in perception, is very tenuous and needs to be treated with much more caution.

Response to Reviewer 2-Comment 5:

We acknowledge the reviewer’s view about being cautious when interpreting non-invasive measures associated with human perception. However, the physiological measurements used in this study are not new in the field of auditory or speech perception, they are gold-standard methods to assess auditory function in both animal and human models. The novelty of our approach lays in imposing attentional states (Active listening) and (Passive listening) while concurrently probing along the auditory pathway in order to gain a holistic understanding of MOCR-mediated changes during a speech comprehension task. The strength of our methodology arises from extensively and continuously monitoring both the attentional states and the quality of our physiological measurements.

Reviewer #3: [...] Reviewer 3-Comment 1: 1) However, I have several substantial concerns with the design, conceptualization, data analysis and interpretation of the results. I have had challenges to understand the hypotheses and rationale behind this study. A number of experimental paradigms have been employed, including peripheral/brainstem physiological measure, as well as cortical auditory responses during active versus 'passive' listening. Different noise conditions were tested but it is not clear to me what rationale was behind these stimulus choices. The authors claim that "our data comparing active and passive listening conditions highlight a categorical distinction between speech manipulation, a difference between processing a single, but degraded, auditory stream (vocoded speech) and parsing a complex acoustic scene to hear out a stream from multiple competing and spectrally similarly sounds" (lines 401-403). This seems like too much of a mouthful. I cannot see that the data support this pretty broad interpretation.

Response to Reviewer 3-Comment 1:

The main objective of this study is to examine the role of the auditory efferent system in active vs. passive listening tasks for three commonly employed speech manipulations. To address this, speech intelligibility was degraded in three ways: 1) noise vocoding the speech signal; 2) adding babble noise (BN) to the speech signal at different SNRs or 3) adding speech-shaped noise (SSN) to the speech signal at different SNRs. The reason for using noise-vocoded speech while contralaterally recording CEOAEs is that it allowed speech intelligibility to be manipulated without increasing noise levels (a classical way of evoking the MOCR (Berlin et al., 1993; Norman & Thornton 1993; Kalaiah et al., 2017b)). This avoided confounding CEOAE magnitude changes due to purely stimulus-driven MOCR activation with attention-driven MOCR on CEOAE magnitudes. Moreover, because the level of the speech spectrum decreases with increasing frequency, white noise (which is the most commonly used stimulus to evoke MOCR in the literature) predominantly masks only the high frequency component of the speech signal, therefore it is not considered an efficient speech masker. However, BN (besides representing a more ethological auditory type of noise) and SSN (which is the spectrally matched long-term averaged of the speech signal) have the same long-term average spectrum as speech. Therefore, these noises were able to mask the speech signal equally across frequencies.

Reviewer 3-Comment 2: 2) Despite maintaining iso-difficulty between vocoded vs speech-in-noise (SIN) conditions, the authors neither address (a) the fundamental differences in understanding vocoded vs. SIN speech nor (b) any theoretical basis for how the noise manifests in vocoded speech. If the tasks are indeed so obviously 'categorically' different - then it should not be surprising they engage different processing (the 'denoising' may not be comparable). I would prefer much more clearly defined and targeted hypotheses and a justification of the specific stimulus and paradigm choices to test such hypotheses. It appears to me that numerous measures have been obtained (reflecting in fact very different processes along the auditory pathway) and then it has been attempted to make up some coherent conclusions from these data - but the assumptions are not clear, the data are very complex and many aspects of the discussion are speculative. To me, the most interesting element is the reversal of the MOCR behavior in the attended vs ignored conditions. However, ignoring a stimulus is not a passive task! It would have been interesting to also see cortical unattended results.

Response to Reviewer 3-Comment 2:

The motivation behind this study arises from controversy in the literature regarding attentional effects at both the level of the cochlear (via MOCR) and the brainstem. Previous studies of attentional effects on CEOAEs have not only prevented direct comparison among them but have also distorted the interpretation of their results. Most have implemented paradigms with large differences in their arousal state [or alertness levels (Eysenck, 2012)] and stimulus type between the active auditory task (e.g. speech stimuli presented while CEOAEs are recorded) and passive listening conditions (no task, CEOAEs recorded during no-noise conditions or with-noise conditions) (Froehlich et al., 1990; Meric et al., 1994; Srinivasan et al., 2012). Our experimental paradigm addressed these issues in three main ways: 1) using the same stimuli for both active and passive listening conditions; 2) using a controlled visual scene across the experimental sessions; and 3) attempting to control for differences in alertness during the passive condition by asking subjects to watch an engaging cartoon movie. The homogeneity of visual and auditory scenes across the experiments allowed the effects of attending to the speech on CEOAE magnitude to be disentangled from the stimulus-driven effects.

In addition, it was never assumed that the “Passive listening” or the “auditory-ignored” condition was a passive task. In this condition subjects were asked to ignore the auditory stimuli and to watch a non-subtitled, stop-motion movie. To ensure participants’ attention during this condition, they were monitored with a video camera and were asked questions at the end of this session (e.g. What happened in the movie? How many characters were present?) (See Methods section). The aim of a passive or an auditory-ignoring condition is to shift attentional resources away from the auditory scene and towards the visual scene. As shown in (Figure supplement 4) all ERP components were also obtained in the Passive listening condition and they are of a smaller magnitude than ERP components observed in the active listening conditions, demonstrating that cortical representation of the speech-onset was enhanced in all active listening conditions.

Reviewer 3-Comment 3: 2) Overall, I'm struggling with this study that touches upon various concepts and paradigms (efferent feedback, active vs. passive listening, neural representation of listening effort, modeling of efferent signal processing, stream segregation, speech-in-noise coding, peripheral vs cortical representations...) where each of them in isolation already provides a number of challenges and has been discussed controversially. In my view, it would be more valuable to specify and clarify the research question and focus on those paradigms that can help verify or falsify the research hypotheses.

Response to Reviewer 3-Comment 3:

In our study, we sought to explore how active listening of degraded speech modulates CEOAE magnitudes (as a proxy for efferent-MOCR effects). With the specific Research question: Does auditory attention modulate cochlear gain, via the auditory efferent system, in a task-dependent manner? and Hypothesis: Decreases in speech intelligibility raise auditory attention and this reduces cochlear gain (measured using CEOAEs).

In particular, unlike previously published studies, we assessed auditory changes objectively and subjectively as part of a highly controlled experimental paradigm, maintaining a constant performance across three experimental manipulations of speech intelligibility as well as minimizing influences of MEMR activation and controlling for homogeneity of both visual and auditory scenes across conditions. We agree with the reviewer that due to the complexity of our study, each section should be more explicit in its hypothesis and aims. This will be clarified in a future version of this manuscript.

Scientist, N. (n.d.). How to sniff out the good coronavirus studies from the bad. New Scientist. Retrieved July 1, 2020, from https://www.newscientist.com/article/2242835-how-to-sniff-out-the-good-coronavirus-studies-from-the-bad/

Peer review should be an honest, but collegial, conversation. (2020). Nature, 582(7812), 314–314. https://doi.org/10.1038/d41586-020-01622-z

Meylan, P. (2020, March 24). The Most Credible Journalists on COVID-19. The Factual. https://blog.thefactual.com/credible-journalists-covid-19

The authors have expertise in the field based on their credentials.

The article was written by staff writers.

Authors are industry experts. You can click their names to learn more about their backgrounds.

One indication of trade publications is that authors are industry experts.

Holcombe, A. (2019). Farewell authors, hello contributors. Nature, 571(7764), 147–147. https://doi.org/10.1038/d41586-019-02084-8

Alex Holcombe en Twitter: “Large numbers of researchers are coming together to work on new projects, because of COVID-19, for example with @PsySciAcc. But journals’’ authorship ‘guidelines’ (rules) deter these large-scale collaborations." / Twitter.” (n.d.). Twitter. Retrieved April 15, 2020, from https://twitter.com/ceptional/status/1242033904346730496

Will Fithian en Twitter: “The authors said by email that they used a built-in Stata function and aren’t sure themselves how the software used the input weights. I suspect they misapplied that function (too complicated to tweet why) but I don’t know Stata well enough to be sure; it seems neither do they.” / Twitter. (n.d.). Twitter. Retrieved April 27, 2020, from https://twitter.com/wfithian/status/1252692362037362693

unidad_COVID2019

The author.

Here is some info about the author:

"John Warner, writer/editor/speaker/consultant with more than twenty years of experience teaching college-level writing. His newest books are Why They Can't Write: Killing the Five-Paragraph Essay and Other Necessities, and The Writer's Practice: Building Confidence in Your Nonfiction Writing. He is editor emeritus of McSweeney's Internet Tendency and you can read his weekly column at the Chicago Tribune. "

See Author Q&A "Power to the People..."with B.G. Tzorvaras and M.P. Ball at http://gigasciencejournal.com/blog/open-humans-qa

Cool Gray City of Love: 49 Views of San Francisco

Chair in Technical Innovation and Entrepreneurship at the Rotman School of Management, University of Toronto.[1] Until 2011, he was an economics professor at Melbourne Business School in Australia. His research focuses on competition policy and intellectual property protection. He is the author of several textbooks and policy books, as well as numerous articles in economics journals.

Author. Learn more about him from his resume: https://www.slideshare.net/slideshow/embed_code/key/xJUyg0OnJ8LcNx

Great author!

It is found here on the author's own web site.

arguably not the best example since cinema is now an equally credible art form, and benjamin was critical only because he did not see the potential of the medium (or any technologically-aided artistic practices).

offering a place for readers to engage in the activities mentioned, encouraging growth in the practices she values

interrelated reading strategies

limited views arise from ignorance/lack of in-depth investigation

effective summary of how some view digital reading habits

personal experiences are valuable in rationalising, testing and expanding understanding of what is learned through active readings of academic studies.

importance of fact-checking any material before accepting the information it presents

important to evaluate sources

thoughtful critique of an accredited source.

Arvind Singh

Shivalika Saxena

Babul Moni Ram

S. Adeel Husain Zaidi,

Check out Heena's author profile!

In publishing circles, this has long been known as platform or author platform--ie that thing that made you famous in the first place that gives you the space to attempt to try to use that fame to sell books.

The source is taking an objective approach and analyzes both sides of the argument.

Again, an article that presents the conflicting nature of a purpose brand. This clearly states the new CEO of Unilver is going to put profit first. This is my last annotation. Overall, I would say that I still find the 50 foods campaign reliable. If you look at it simply as an informative document I think it is accurate, and a good publication However I think it is worth it to understand the authors as well. Unilever is not a perfect company, nor is WWF. Far from it. I hope that we can support this 50 foods campaign and other good choices while still holding Knorr Unilever and WWF accountable for their contradictions, hypocrisy, corruption, and bad choices.

I think this is one of the most objective reviews of former CEO of Unilever, and is accurate about the current state of Unilever. I think we should always take what a company says about sustainability with a grain of salt because it is still trying to profit. But, we need people who care in business. Businesses contribute to pollution more than anyone else. Unilever is still kind of in a gray area, but I think their efforts still make them reputable overall, at least in the eyes of the public.

This adds to the conflicting reputation and credibility of WWF. I think that sometimes they put animals above people when, in reality, we need to honor both animals and people for sustainability. We're all part of the ecosystem. Having 14 million displaced people is not sustainable. WWF is very complicated; they seem to have great intentions but sometimes poor execution. It's hard to say whether or not to trust them.

Dorothy Shaver designed the report. This article shows she is personally committed to the cause.

Still unsure how credible I find WWF but they seem to have good ideas about food sustainability.

This article is interesting. I don't think in this instance that WWF was involved in spreading fake news, but it does show they are capable of devising plans that don't necessarily put ethics first. It's a good reminder that WWF is still involved in trying to market itself and get press. I think that WWF doesn't take a comprehensive approach to understanding the ivory trade, which is largely a result of poverty. This makes them a little less credible to me. Although, some people might find them more credible for going so far for a cause.

Again, this is very hard to ignore. This is the biggest thing cutting into the campaign. It makes me suspicious. Even if everything WWF said in the campaign was true and ethical, I think it's a bad idea to work with a company that's involved in such abuses. Hopefully Unilever was unaware of these problems. If they had known and collaborated with WWF anyway, that would be a serious knock to their credibility and reliability.

This shows that WWF breaks its own rules. It makes me wonder if their partnership with Unilever is about sustainability or money. Unfortunately I think very few people know of this scandal, so it hasn't impacted WWF's reputation. But I think it could.

This comprehensive article is the biggest blow to Unilever's campaign. WWF is one of the main partners who wrote the report. Although WWF has a history of doing good things for the planet, this article is very hard to swallow. It made me completely distrust WWF.

This portion of the document explains every detail that went into picking each food. The process includes many different measures of sustainability and health. All of the science is current and accurate.

This comprehensive list of varied references makes the document very reliable.

I believe that this makes Knorr Unilever seem reliable as a source as well as making the content seem reliable, and the author objective and understanding. This is because the 3 authors of the document collaborated with so many different sources to write the paper. It would seem that have a well-rounded grasp of the topic.

This article describes Unilever's plans to change the way it uses plastic. It shows that Unilever cares about sustainability because they are transparent about the economic benefits of being more sustainable as well as the benefits to the planet.

This is one part of Unilevers comprehensive website about sustainability. The site shows that Unilever frequently collaborates with sustainable organizations and that they care about many sustainable issues.

Adam Drewnowski is the main author. He not only has a degree in disease studies, he is the director of a public health center, director of UW obesity research, and a cancer research institute. These qualifications and experiences with a variety of educational and research institutions shows us that he throughly understands his topic.