Díjkalkuláció szintje sorozatok esetén.

It determines the date on which the fee payment has to affect the accrued fee value.

ez felsorolás legyen

További általános díjbeállítás szabályok továbbá, amely a Portfólió Szabályokban állítható be:

szabad

Csak kivétel esetén töltendő, ha üresen marad, akkor a kerekítési szabály: díj összeg az alapdeviza az alap/sorozat devizájának kerekítése szerint van meghatározva.

fee amount is usually rounded based on the rounding defined in the portfolio base data.

Ezt töröljük pls!

Ezt a részt töröljük ki!

Magyar szöveg A portfolióhoz kapcsolt naptár szerinti munkanapok alapján.

Default = actual basis (number of actual days) Only applicable to average value basis fees

value is calculated for the entire period

Magyar szöveg: a korábbi felhalmozott értékhez adódik a napi elhatárolás

Magyar szöveg: Negyedév eleji

Last official capital value from series

Thunderbirds 4K cinema double bill

The ice cream at the sweetie shop

Bicycle races down the street

Riding in a little electric car

Kayaking and paddleboarding

The most awesome cruise ever, the Independence

The Ballad Of Smallhope & Pennyroyal reminding me of Thunderbirds

Nostalgic French Chocapic adverts

A game of baseball

Friends that make me feel like I belong

Zecora being my mentor

yes

no

no

no

no

yes

I am a traditional student, the advantage is I don't have a job so after practice I'm able to direct my attention straight to my work.

No

No

No I've spent my whole life here.

no I'm not.

yes

yes

after high school

Larger firms could afford the "race to the bottom" so to speak. Given this, smaller companies got eliminated from the market because they did not have the hefty cash reserves that would allow them to invest in extra machinery as well as expand their workforce. Thus, limiting their ability to operate on thin margins during the "race".

Segundo objetivo: Motivar

Proveer

Objetivo 1 Proveer

Objetico 2 Motivar

Objetivo 2: Motivar

Objetivo 1: Proveer

Segundo Objetivo.

Motivar

Objetivo # 1

Objetivo dos.

Segundo objetivo

Primer Objetivo.

Proveer

Objetivo #1

Objetivo 2

Objetivo # 2

Objetivo uno.

Primer objetivo

Objetivo # 1

for - quote/key insight - perception serves reproduction, not seeing reality as it is

quote / key insight - perception serves reproduction, not seeing reality as it is - Donald Hoffman - From an evolutionary point of view, perception is expensive. - It takes a lot of calories. - You have to eat a lot of food - to run your brain and - to power your eyes and your ears. - - And so you need to do shortcuts. - You need to make your sensory systems not chew up so much of your energy. - The more expensive your perceptual systems are, - the more you've got to eat to to power those. - So that means you have to go out there and forage and put yourself at harm. - So there's a trade-off. - We try to do things cheaply in evolution. And you don't need to actually go for the truth because that's very very expensive

for - quote - probability of zero that sensory organs are designed to help us see objective reality - Donald Hoffman

for - find - Donald Hoffman papers

for - quote - Evolution shapes us not for truth, but to successfully reproduce - Donald Hoffman

I can annotate this page!

I will hopefully open my own business with the education i've received due to college and high school , and be successful.

all of the above

5

4

3

5

5

5

4

4

5

4

5

4

3

3

3

5

5

4

5

T

4

F

F

4

1

4

T

4

2

the increase of your workload, and the time you have to study instead of having free time.

4

5

4

1

3

2

3

4

My free time.

4

3

I value my knowledge.

5

4

Yes I'm confident in finishing college by getting support from my family

All of the above.

Having time for a job and school work at the same time

Around 2-3 courses

I anticipate being in college for 4-5 years

1,4,2,,1,3,0,5,4,0,4,5,5,0,3,4,2,5,4,4,5,2,5,5,2,1,2,5,4,5,5,5,5,5,5,2,5,5,5.

I feel like the most difficult part will be keeping up with everything, but I am very confident I will overcome any difficulties with God by my side, and me putting in time.

I plan on being in college for about 2-4 years. I will need to take 6-8 courses I believe.

attitude of the mob

end of the story

A and Guard -- duty

maybe

refusing privilege

images, the public

stop

dialectic

status

why?

true?

creon/antig - priv morality

cops

@jared.lyvers Need more spacing on both sides of the "/" on the last three instances in the CREATIVE CAPABILITIES SECTIOn (Like you did on the first two) Thanks!

eLife Assessment

This study provides an important extension of credibility-based learning research with a well-controlled paradigm by showing how feedback reliability can distort reward-learning biases in a disinformation-like bandit task. The strength of evidence is convincing for the core effects reported (greater learning from credible feedback; robust computational accounts, parameter recovery) but incomplete for the specific claims about heightened positivity bias at low credibility, which depend on a single dataset, metric choices (absolute vs relative), and potential perseveration or cueing confounds. Limitations concerning external validity and task-induced cognitive load, and the use of relatively simple Bayesian comparators, suggest that incorporating richer active-inference/HGF benchmarks and designs that dissociate positivity bias from choice history would further strengthen this paper.

Reviewer #1 (Public review):

This is a well-designed and very interesting study examining the impact of imprecise feedback on outcomes on decision-making. I think this is an important addition to the literature and the results here, which provide a computational account of several decision-making biases, are insightful and interesting.

I do not believe I have substantive concerns related to the actual results presented; my concerns are more related to the framing of some of the work. My main concern is regarding the assertion that the results prove that non-normative and non-Bayesian learning is taking place. I agree with the authors that their results demonstrate that people will make decisions in ways that demonstrate deviations from what would be optimal for maximizing reward in their task under a strict application of Bayes rule. I also agree that they have built reinforcement learning models which do a good job of accounting for the observed behavior. However, the Bayesian models included are rather simple- per the author descriptions, applications of Bayes' rule with either fixed or learned credibility for the feedback agents. In contrast, several versions of the RL models are used, each modified to account for different possible biases. However more complex Bayes-based models exist, notably active inference but even the hierarchical gaussian filter. These formalisms are able to accommodate more complex behavior, such as affect and habits, which might make them more competitive with RL models. I think it is entirely fair to say that these results demonstrate deviations from an idealized and strict Bayesian context; however, the equivalence here of Bayesian and normative is I think misleading or at least requires better justification/explanation. This is because a great deal of work has been done to show that Bayes optimal models can generate behavior or other outcomes that are clearly not optimal to an observer within a given context (consider hallucinations for example) but which make sense in the context of how the model is constructed as well as the priors and desired states the model is given.

As such, I would recommend that the language be adjusted to carefully define what is meant by normative and Bayesian and to recognize that work that is clearly Bayesian could potentially still be competitive with RL models if implemented to model this task. An even better approach would be to directly use one of these more complex modelling approaches, such as active inference, as the comparator to the RL models, though I would understand if the authors would want this to be a subject for future work.

Abstract:

The abstract is lacking in some detail about the experiments done, but this may be a limitation of the required word count? If word count is not an issue, I would recommend adding details of the experiments done and the results. One comment is that there is an appeal to normative learning patterns, but this suggests that learning patterns have a fixed optimal nature, which may not be true in cases where the purpose of the learning (e.g. to confirm the feeling of safety of being in an in-group) may not be about learning accurately to maximize reward. This can be accommodated in a Bayesian framework by modelling priors and desired outcomes. As such the central premise that biased learning is inherently non-normative or non-Bayesian I think would require more justification. This is true in the introduction as well.

Introduction:

As noted above the conceptualization of Bayesian learning being equivalent to normative learning I think requires either further justification. Bayesian belief updating can be biased an non-optimal from an observer perspective, while being optimal within the agent doing the updating if the priors/desired outcomes are set up to advantage these "non-optimal" modes of decision making.

Results:

I wonder why the agent was presented before the choice - since the agent is only relevant to the feedback after the choice is made. I wonder if that might have induced any false association between the agent identity and the choice itself. This is by no means a critical point but would be interesting to get the authors' thoughts.

The finding that positive feedback increases learning is one that has been shown before and depends on valence, as the authors note. They expanded their reinforcement learning model to include valence; but they did not modify the Bayesian model in a similar manner. This lack of a valence or recency effect might also explain the failure of the Bayesian models in the preceding section where the contrast effect is discussed. It is not unreasonable to imagine that if humans do employ Bayesian reasoning that this reasoning system has had parameters tuned based on the real world, where recency of information does matter; affect has also been shown to be incorporable into Bayesian information processing (see the work by Hesp on affective charge and the large body of work by Ryan Smith). It may be that the Bayesian models chosen here require further complexity to capture the situation, just like some of the biases required updates to the RL models. This complexity, rather than being arbitrary, may be well justified by decision making in the real world.

The methods mention several symptom scales- it would be interesting to have the results of these and any interesting correlations noted. It is possible that some of individual variability here could be related to these symptoms, which could introduce precision parameter changes in a Bayesian context and things like reward sensitivity changes in an RL context.

Discussion:

(For discussion, not a specific comment on this paper): One wonders also about participant beliefs about the experiment or the intent of the experimenters. I have often had participants tell me they were trying to "figure out" a task or find patterns even when this was not part of the experiment. This is not specific to this paper, but it may be relevant in the future to try and model participant beliefs about the experiment especially in the context of disinformation, when they might be primed to try and "figure things out".

As a general comment, in the active inference literature, there has been discussion of state-dependent actions, or "habits", which are learned in order to help agents more rapidly make decisions, based on previous learning. It is also possible that what is being observed is that these habits are at play, and that they represent the cognitive biases. This is likely especially true given, as the authors note, the high cognitive load of the task. It is true that this would mean that full-force Bayesian inference is not being used in each trial, or in each experience an agent might have in the world, but this is likely adaptive on the longer timescale of things, considering resource requirements. I think in this case you could argue that we have a departure from "normative" learning, but that is not necessarily a departure from any possible Bayesian framework, since these biases could potentially be modified by the agent or eschewed in favor of more expensive full-on Bayesian learning when warranted. Indeed in their discussion on the strategy of amplifying credible news sources to drown out low-credibility sources, the authors hint to the possibility of longer term strategies that may produce optimal outcomes in some contexts, but which were not necessarily appropriate to this task. As such, the performance on this task- and the consideration of true departure from Bayesian processing- should be considered in this wider context. Another thing to consider is that Bayesian inference is occurring, but that priors present going in produce the biases, or these biases arise from another source, for example factoring in epistemic value over rewards when the actual reward is not large. This again would be covered under an active inference approach, depending on how the priors are tuned. Indeed, given the benefit of social cohesion in an evolutionary perspective, some of these "biases" may be the result of adaptation. For example, it might be better to amplify people's good qualities and minimize their bad qualities in order to make it easier to interact with them; this entails a cost (in this case, not adequately learning from feedback and potentially losing out sometimes), but may fulfill a greater imperative (improved cooperation on things that matter). Given the right priors/desired states, this could still be a Bayes-optimal inference at a social level and as such may be ingrained as a habit which requires effort to break at the individual level during a task such as this.

The authors note that this task does not relate to "emotional engagement" or "deep, identity-related, issues". While I agree that this is likely mostly true, it is also possible that just being told one is being lied to might elicit an emotional response that could bias responses, even if this is a weak response.

Comments on revisions:

In their updated version the authors have made some edits to address my concerns regarding the framing of the 'normative' bayesian model, clarifying that they utilized a simple bayesian model which is intended to adhere in an idealized manner to the intended task structure, though further simulations would have been ideal.

The authors, however, did not take my recommendation to explore the symptoms in the symptom scales they collected as being a potential source of variability. They note that these were for hypothesis generation and were exploratory, fair enough, but this study is not small and there should have been sufficient sample size for a very reasonable analysis looking at symptom scores.

However, overall the toned down claims and clarifications of intent are adequate responses to my previous review.

Reviewer #2 (Public review):

This important paper studies the problem of learning from feedback given by sources of varying credibility. The convincing combination of experiment and computational modeling helps to pin down properties of learning, while opening unresolved questions for future research.

Summary:

This paper studies the problem of learning from feedback given by sources of varying credibility. Two bandit-style experiments are conducted in which feedback is provided with uncertainty, but from known sources. Bayesian benchmarks are provided to assess normative facets of learning, and alternative credit assignment models are fit for comparison. Some aspects of normativity appear, in addition to possible deviations such as asymmetric updating from positive and negative outcomes.

Strengths:

The paper tackles an important topic, with a relatively clean cognitive perspective. The construction of the experiment enables the use of computational modeling. This helps to pinpoint quantitatively the properties of learning and formally evaluate their impact and importance. The analyses are generally sensible, and advanced parameter recovery analyses (including cross-fitting procedure) provide confidence in the model estimation and comparison. The authors have very thoroughly revised the paper in response to previous comments.

Weaknesses:

The authors acknowledge the potential for cognitive load and the interleaved task structure to play a meaningful role in the results, though leave this for future work. This is entirely reasonable, but remains a limitation in our ability to generalize the results. Broadly, some of the results obtain in cases where the extent of generalization is not always addressed and remains uncertain.

Reviewer #3 (Public review):

Summary

This paper investigates how disinformation affects reward learning processes in the context of a two-armed bandit task, where feedback is provided by agents with varying reliability (with lying probability explicitly instructed). They find that people learn more from credible sources, but also deviate systematically from optimal Bayesian learning: They learned from uninformative random feedback, learned more from positive feedback, and updated too quickly from fully credible feedback (especially following low-credibility feedback). Overall, this study highlights how misinformation could distort basic reward learning processes, without appeal to higher order social constructs like identity.

Strengths

• The experimental design is simple and well-controlled; in particular, it isolates basic learning processes by abstracting away from social context
• Modeling and statistics meet or exceed standards of rigor
• Limitations are acknowledged where appropriate, especially those regarding external validity
• The comparison model, Bayes with biased credibility estimates, is strong; deviations are much more compelling than e.g. a purely optimal model
• The conclusions are of substantial interest from both a theoretical and applied perspective

Weaknesses

The authors have addressed most of my concerns with the initial submission. However, in my view, evidence for the conclusion that less credible feedback yields a stronger positivity bias remains weak. This is due to two issues.

Absolute or relative positivity bias?

The conclusion of greater positivity bias for lower credible feedback (Fig 5) hinges on the specific way in which positivity bias is defined. Specifically, we only see the effect when normalizing the difference in sensitivity to positive vs. negative feedback by the sum. I appreciate that the authors present both and add the caveat whenever they mention the conclusion. However, without an argument that the relative definition is more appropriate, the fact of the matter is that the evidence is equivocal.

There is also a good reason to think that the absolute definition is more appropriate. As expected, participants learn more from credible feedback. Thus, normalizing by average learning (as in the relative definition) amounts to dividing the absolute difference by increasingly large numbers for more credible feedback. If there is a fixed absolute positivity bias (or something that looks like it), the relative bias will necessarily be lower for more credible feedback. In fact, the authors own results demonstrate this phenomenon (see below). A reduction in relative bias thus provides weak evidence for the claim.

It is interesting that the discovery study shows evidence of a drop in absolute bias. However, for me, this just raises questions. Why is there a difference? Was one a just a fluke? If so, which one?

Positivity bias or perseveration?

Positivity bias and perseveration will both predict a stronger relationship between positive (vs. negative) feedback and future choice. They can thus be confused for each other when inferred from choice data. This potentially calls into question all the results on positivity bias.

The authors clearly identify this concern in the text and go to considerable lengths to rule it out. However, the new results (in revision 1) show that a perseveration-only model can in fact account for the qualitative pattern in the human data (the CA parameters). This contradicts the current conclusion:

Critically, however, these analyses also confirmed that perseveration cannot account for our main finding of increased positivity bias, relative to the overall extent of CA, for low-credibility feedback.

Figure 24c shows that the credibility-CA model does in fact show stronger positivity bias for less credible feedback. The model distribution for credibility 1 is visibly lower than for credibilities 0.5 and 0.75.

The authors need to be clear that it is the magnitude of the effect that the perseveration-only model cannot account for. Furthermore, they should additionally clarify that this is true only for models fit to data; it is possible that the credibility-CA model could capture the full size of the effect with different parameters (which could fit best if the model was implemented slightly differently).

The authors could make the new analyses somewhat stronger by using parameters optimized to capture just the pattern in CA parameters (for example by MSE). This would show that the models are in principle incapable of capturing the effect. However, this would be a marginal improvement because the conclusion would still rest on a quantitative difference that depends on specific modeling assumptions.

New simulations clearly demonstrate the confound in relative bias

Figure 24 also speaks to the relative vs. absolute question. The model without positivity bias shows a slightly stronger absolute "positivity bias" for the most credible feedback, but a weaker relative bias. This is exactly in line with the logic laid out above. In standard bandit tasks, perseveration can be quite well-captured by a fixed absolute positivity bias, which is roughly what we see in the simulations (I'm not sure what to make of the slight increase; perhaps a useful lead for the authors). However, when we divide by average credit assignment, we now see a reduction. This clearly demonstrates that a reduction in relative bias can emerge without any true differences in positivity bias.

Given everything above, I think it is unlikely that the present data can provide even "solid" evidence for the claim that positivity bias is greater with less credible feedback. This confound could be quickly ruled out, however, by a study in which feedback is sometimes provided in the absence of a choice. This would empirically isolate positivity bias from choice-related effects, including perseveration.

Author response:

The following is the authors’ response to the original reviews

Reviewer #1 (Public review):

This is a well-designed and very interesting study examining the impact of imprecise feedback on outcomes in decision-making. I think this is an important addition to the literature, and the results here, which provide a computational account of several decision-making biases, are insightful and interesting.

We thank the reviewer for highlighting the strengths of this work.

I do not believe I have substantive concerns related to the actual results presented; my concerns are more related to the framing of some of the work. My main concern is regarding the assertion that the results prove that non-normative and non-Bayesian learning is taking place. I agree with the authors that their results demonstrate that people will make decisions in ways that demonstrate deviations from what would be optimal for maximizing reward in their task under a strict application of Bayes' rule. I also agree that they have built reinforcement learning models that do a good job of accounting for the observed behavior. However, the Bayesian models included are rather simple, per the author's descriptions, applications of Bayes' rule with either fixed or learned credibility for the feedback agents. In contrast, several versions of the RL models are used, each modified to account for different possible biases. However, more complex Bayes-based models exist, notably active inference, but even the hierarchical Gaussian filter. These formalisms are able to accommodate more complex behavior, such as affect and habits, which might make them more competitive with RL models. I think it is entirely fair to say that these results demonstrate deviations from an idealized and strict Bayesian context; however, the equivalence here of Bayesian and normative is, I think, misleading or at least requires better justification/explanation. This is because a great deal of work has been done to show that Bayes optimal models can generate behavior or other outcomes that are clearly not optimal to an observer within a given context (consider hallucinations for example), but which make sense in the context of how the model is constructed as well as the priors and desired states the model is given.

As such, I would recommend that the language be adjusted to carefully define what is meant by normative and Bayesian and to recognize that work that is clearly Bayesian could potentially still be competitive with RL models if implemented to model this task. An even better approach would be to directly use one of these more complex modelling approaches, such as active inference, as the comparator to the RL models, though I would understand if the authors would want this to be a subject for future work.

We thank the reviewer for raising this crucial and insightful point regarding the framing of our results and the definitions of 'normative' and 'Bayesian' learning. Our primary aim in this work was to characterize specific behavioral signatures that demonstrate deviations from predictions generated by a strict, idealized Bayesian framework when learning from disinformation (which we term “biases”). We deliberately employed relatively simple Bayesian models as benchmarks to highlight these specific biases. We fully agree that more sophisticated Bayes-based models (as mentioned by the reviewer, or others) could potentially offer alternative mechanistic explanations for participant behavior. However, we currently do not have a strong notion about which Bayesian models can encompass our findings, and hence, we leave this important question for future work.

To enhance clarity within the current manuscript we now avoided the use of the term “normative” to refer to our Bayesian models, using the term “ideal” instead. We also define more clearly what exactly we mean by that notion when the idea model is described:

“This model is based on an idealized assumptions that during the feedback stage of each trial, the value of the chosen bandit is updated (based on feedback valence and credibility) according to Bayes rule reflecting perfect adherence to the instructed task structure (i.e., how true outcomes and feedback are generated).”

Moreover, we have added a few sentences in the discussion commenting on how more complex Bayesian models might account for our empirical findings:

“However, as hypothesized, when facing potential disinformation, we also find that individuals exhibit several important biases i.e., deviations from strictly idealized Bayesian strategies. Future studies should explore if and under what assumptions, about the task’s generative structure and/or learner’s priors and objectives, more complex Bayesian models (e.g., active inference (58)) might account for our empirical findings.”

Abstract:

The abstract is lacking in some detail about the experiments done, but this may be a limitation of the required word count. If word count is not an issue, I would recommend adding details of the experiments done and the results.

We thank the reviewer for their valuable suggestion. We have now included more details about the experiment in the abstract:

“In two experiments, participants completed a two-armed bandit task, where they repeatedly chose between two lotteries and received outcome-feedback from sources of varying credibility, who occasionally disseminated disinformation by lying about true choice outcome (e.g., reporting non reward when a reward was truly earned or vice versa).”

One comment is that there is an appeal to normative learning patterns, but this suggests that learning patterns have a fixed optimal nature, which may not be true in cases where the purpose of the learning (e.g. to confirm the feeling of safety of being in an in-group) may not be about learning accurately to maximize reward. This can be accommodated in a Bayesian framework by modelling priors and desired outcomes. As such, the central premise that biased learning is inherently non-normative or non-Bayesian, I think, would require more justification. This is true in the introduction as well.

Introduction:

As noted above, the conceptualization of Bayesian learning being equivalent to normative learning, I think requires further justification. Bayesian belief updating can be biased and non-optimal from an observer perspective, while being optimal within the agent doing the updating if the priors/desired outcomes are set up to advantage these "non-optimal" modes of decision making.

We appreciate the reviewer's thoughtful comment regarding the conceptualization of "normative" and "Bayesian" learning. We fully agree that the definition of "normative" is nuanced and can indeed depend on whether one considers reward-maximization or the underlying principles of belief updating. As explained above we now restrict our presentation to deviations from “ideal Bayes” learning patterns and we acknowledge the reviewer’s concern in a caveat in our discussion.

Results:

I wonder why the agent was presented before the choice, since the agent is only relevant to the feedback after the choice is made. I wonder if that might have induced any false association between the agent identity and the choice itself. This is by no means a critical point, but it would be interesting to get the authors' thoughts.

We thank the reviewer for raising this interesting point regarding the presentation of the agent before the choice. Our decision to present the agent at this stage was intentional, as our original experimental design aimed to explore the possible effects of "expected source credibility" on participants' choices (e.g., whether knowledge of feedback credibility will affect choice speed and accuracy). However, we found nothing that would be interesting to report.

The finding that positive feedback increases learning is one that has been shown before and depends on valence, as the authors note. They expanded their reinforcement learning model to include valence, but they did not modify the Bayesian model in a similar manner. This lack of a valence or recency effect might also explain the failure of the Bayesian models in the preceding section, where the contrast effect is discussed. It is not unreasonable to imagine that if humans do employ Bayesian reasoning that this reasoning system has had parameters tuned based on the real world, where recency of information does matter; affect has also been shown to be incorporable into Bayesian information processing (see the work by Hesp on affective charge and the large body of work by Ryan Smith). It may be that the Bayesian models chosen here require further complexity to capture the situation, just like some of the biases required updates to the RL models. This complexity, rather than being arbitrary, may be well justified by decision-making in the real world.

Thanks for these additional important ideas which speak more to the notion that more complex Bayesian frameworks may account for biases we report.

The methods mention several symptom scales- it would be interesting to have the results of these and any interesting correlations noted. It is possible that some of the individual variability here could be related to these symptoms, which could introduce precision parameter changes in a Bayesian context and things like reward sensitivity changes in an RL context.

We included these questionnaires for exploratory purposes, with the aim of generating informed hypotheses for future research into individual differences in learning. Given the preliminary nature of these analyses, we believe further research is required about this important topic.

Discussion:

(For discussion, not a specific comment on this paper): One wonders also about participants' beliefs about the experiment or the intent of the experimenters. I have often had participants tell me they were trying to "figure out" a task or find patterns even when this was not part of the experiment. This is not specific to this paper, but it may be relevant in the future to try and model participant beliefs about the experiment especially in the context of disinformation, when they might be primed to try and "figure things out".

We thank the reviewer for this important recommendation. We agree and this point is included in our caveat (cited above) that future research should address what assumptions about the generative task structure can allow Bayesian models to account for our empirical patterns.

As a general comment, in the active inference literature, there has been discussion of state-dependent actions, or "habits", which are learned in order to help agents more rapidly make decisions, based on previous learning. It is also possible that what is being observed is that these habits are at play, and that they represent the cognitive biases. This is likely especially true given, as the authors note, the high cognitive load of the task. It is true that this would mean that full-force Bayesian inference is not being used in each trial, or in each experience an agent might have in the world, but this is likely adaptive on the longer timescale of things, considering resource requirements. I think in this case you could argue that we have a departure from "normative" learning, but that is not necessarily a departure from any possible Bayesian framework, since these biases could potentially be modified by the agent or eschewed in favor of more expensive full-on Bayesian learning when warranted.<br /> Indeed, in their discussion on the strategy of amplifying credible news sources to drown out low-credibility sources, the authors hint at the possibility of longer-term strategies that may produce optimal outcomes in some contexts, but which were not necessarily appropriate to this task. As such, the performance on this task- and the consideration of true departure from Bayesian processing- should be considered in this wider context.

Another thing to consider is that Bayesian inference is occurring, but that priors present going in produce the biases, or these biases arise from another source, for example, factoring in epistemic value over rewards when the actual reward is not large. This again would be covered under an active inference approach, depending on how the priors are tuned. Indeed, given the benefit of social cohesion in an evolutionary perspective, some of these "biases" may be the result of adaptation. For example, it might be better to amplify people's good qualities and minimize their bad qualities in order to make it easier to interact with them; this entails a cost (in this case, not adequately learning from feedback and potentially losing out sometimes), but may fulfill a greater imperative (improved cooperation on things that matter). Given the right priors/desired states, this could still be a Bayes-optimal inference at a social level and, as such, may be ingrained as a habit that requires effort to break at the individual level during a task such as this.

We thank the reviewer for these insightful suggestions speaking further to the point about more complex Bayesian models.

The authors note that this task does not relate to "emotional engagement" or "deep, identity-related issues". While I agree that this is likely mostly true, it is also possible that just being told one is being lied to might elicit an emotional response that could bias responses, even if this is a weak response.

We agree with the reviewer that a task involving performance-based bonuses, and particularly one where participants are explicitly told they are being lied to, might elicit weak emotional response. However, our primary point is that the degree of these responses is expected to be substantially weaker than those typically observed in the broader disinformation literature, which frequently deals with highly salient political, social, or identity-related topics that inherently carry strong emotional and personal ties for participants, leading to much more pronounced affective engagement and potential biases. Our task deliberately avoids such issues thus minimizing the potential for significant emotion-driven biases. We have toned down the discussion accordingly:

“This occurs even when the decision at hand entails minimal emotional engagement or pertinence to deep, identity-related, issues.”

Reviewer #2 (Public review):

This valuable paper studies the problem of learning from feedback given by sources of varying credibility. The solid combination of experiment and computational modeling helps to pin down properties of learning, although some ambiguity remains in the interpretation of results.

Summary:

This paper studies the problem of learning from feedback given by sources of varying credibility. Two banditstyle experiments are conducted in which feedback is provided with uncertainty, but from known sources. Bayesian benchmarks are provided to assess normative facets of learning, and alternative credit assignment models are fit for comparison. Some aspects of normativity appear, in addition to deviations such as asymmetric updating from positive and negative outcomes.

Strengths:

The paper tackles an important topic, with a relatively clean cognitive perspective. The construction of the experiment enables the use of computational modeling. This helps to pinpoint quantitatively the properties of learning and formally evaluate their impact and importance. The analyses are generally sensible, and parameter recovery analyses help to provide some confidence in the model estimation and comparison.

We thank the reviewer for highlighting the strengths of this work.

Weaknesses:

(1) The approach in the paper overlaps somewhat with various papers, such as Diaconescu et al. (2014) and Schulz et al. (forthcoming), which also consider the Bayesian problem of learning and applying source credibility, in terms of theory and experiment. The authors should discuss how these papers are complementary, to better provide an integrative picture for readers.

Diaconescu, A. O., Mathys, C., Weber, L. A., Daunizeau, J., Kasper, L., Lomakina, E. I., ... & Stephan, K. E. (2014). Inferring the intentions of others by hierarchical Bayesian learning. PLoS computational biology, 10(9), e1003810.

Schulz, L., Schulz, E., Bhui, R., & Dayan, P. Mechanisms of Mistrust: A Bayesian Account of Misinformation Learning. https://doi.org/10.31234/osf.io/8egxh

We thank the reviewers for pointing us to this relevant work. We have updated the introduction, mentioning these precedents in the literature and highlighting our specific contributions:

“To address these questions, we adopt a novel approach within the disinformation literature by exploiting a Reinforcement Learning (RL) experimental framework (36). While RL has guided disinformation research in recent years (37–41), our approach is novel in using one of its most popular tasks: the “bandit task”.”

We also explain in the discussion how these papers relate to the current study:

“Unlike previous studies wherein participants had to infer source credibility from experience (30,37,72), we took an explicit-instruction approach, allowing us to precisely assess source-credibility impact on learning, without confounding it with errors in learning about the sources themselves. More broadly, our work connects with prior research on observational learning, which examined how individuals learn from the actions or advice of social partners (72–75). This body of work has demonstrated that individuals integrate learning from their private experiences with learning based on others’ actions or advice—whether by inferring the value others attribute to different options or by mimicking their behavior (57,76). However, our task differs significantly from traditional observational learning. Firstly, our feedback agents interpret outcomes rather than demonstrating or recommending actions (30,37,72).”

(2) It isn't completely clear what the "cross-fitting" procedure accomplishes. Can this be discussed further?

We thank the reviewer for requesting further clarification on the cross-fitting procedure. Our study utilizes two distinct model families: Bayesian models and CA models. The credit assignment parameters from the CA models can be treated as “data/behavioural features” corresponding to how choice feedback affects choice-propensities. The cross fitting-approach allows us in effect to examine whether these propensity features are predicted from our Bayesian models. To the extent they are not, we can conclude empirical behavior is “biased”.

Thus, in our cross-fitting procedure we compare the CA model parameters extracted from participant data (empirical features) with those that would be expected if our Bayesian agents performed the task. Specifically, we first fit participant behavior with our Bayesian models, then simulate this model using the best-fitted parameters and fit those simulations with our CA models. This generates a set of CA parameters that would be predicted if participants behavior is reduced to a Bayesian account. By comparing these predicted Bayesian CA parameters with the actual CA parameters obtained from human participants, the cross-fitting procedure allows us to quantitatively demonstrate that the observed participant parameters are indeed statistically significant deviations from normative Bayesian processing. This provides a robust validation that the biases we identify are not artifacts of the CA model's structure but true departures from normative learning.

We also note that Reviewer 3 suggested an intuitive way to think about the CA parameters—as analogous to logistic regression coefficients in a “sophisticated regression” of choice on (recencyweighted) choice-feedback. We find this suggestion potentially helpful for readers. Under this interpretation, the purpose of the cross-fitting method can be seen simply as estimating the regression coefficients that would be predicted by our Bayesian agents, and comparing those to the empirical coefficients.

In our manuscript we now explain this issues more clearly by explaining how our model is analogous to a logistic regression:

“The probability to choose a bandit (say A over B) in this family of models is a logistic function of the contrast choice-propensities between these two bandits. One interpretation of this model is as a “sophisticated” logistic regression, where the CA parameters take the role of “regression coefficients” corresponding to the change in log odds of repeating the just-taken action in future trials based on the feedback (+/- CA for positive or negative feedback, respectively; the model also includes gradual perseveration which allows for constant log-odd changes that are not affected by choice feedback) . The forgetting rate captures the extent to which the effect of each trial on future choices diminishes with time. The Q-values are thus exponentially decaying sums of logistic choice propensities based on the types of feedback a bandit received.”

We also explain our cross-fitting procedure in more detail:

“To further characterise deviations between behaviour and our Bayesian learning models, we used a “crossfitting” method. Treating CA parameters as data-features of interest (i.e., feedback dependent changes in choice propensity), our goal was to examine if and how empirical features differ from features extracted from simulations of our Bayesian learning models. Towards that goal, we simulated synthetic data based on Bayesian agents (using participants’ best fitting parameters), but fitted these data using the CA-models, obtaining what we term “Bayesian-CA parameters” (Fig. 2d; Methods). A comparison of these BayesianCA parameters, with empirical-CA parameters obtained by fitting CA models to empirical data, allowed us to uncover patterns consistent with, or deviating from, ideal-Bayesian value-based inference. Under the sophisticated logistic-regression interpretation of the CA-model family the cross-fitting method comprises a comparison between empirical regression coefficients (i.e., empirical CA parameters) and regression coefficient based on simulations of Bayesian models (Bayesian CA parameters).”

(3) The Credibility-CA model seems to fit the same as the free-credibility Bayesian model in the first experiment and barely better in the second experiment. Why not use a more standard model comparison metric like the Bayesian Information Criterion (BIC)? Even if there are advantages to the bootstrap method (which should be described if so), the BIC would help for comparability between papers.

We thank the reviewer for this important comment regarding our model comparison approach. We acknowledge that classical information criteria like AIC and BIC are widely used in RL studies. However, we argue our method for model-comparison is superior.

We conducted a model recovery analysis demonstrating a significant limitation of using AIC or BIC for model-comparison in our data. Both these methods are strongly biased in favor of the Bayesian models. Our PBCM method, on the other hand, is both unbiased and more accurate. We believe this is because “off the shelf” methods like AIC and BIC rely on strong assumptions (such as asymptotic sample size and trial-independence) that are not necessarily met in our tasks (Data is finite; Trials in RL tasks depend on previous trials). PBCM avoids such assumptions to obtain comparison criteria specifically tailored to the structure and size of our empirical data. We have now mentioned this fact in the results section of the main text:

“We considered using AIC and BIC, which apply “off-the shelf” penalties for model-complexity. However, these methods do not adapt to features like finite sample size (relying instead on asymptotic assumption) or temporal dependence (as is common in reinforcement learning experiments). In contrast, the parametric bootstrap cross-fitting method replaces these fixed penalties with empirical, data-driven criteria for modelselection. Indeed, model-recovery simulations confirmed that whereas AIC and BIC were heavily biased in favour of the Bayesian models, the bootstrap method provided excellent model-recovery (See Fig. S20).”

We have also included such model recovery in the SI document:

(4) As suggested in the discussion, the updating based on random feedback could be due to the interleaving of trials. If one is used to learning from the source on most trials, the occasional random trial may be hard to resist updating from. The exact interleaving structure should also be clarified (I assume different sources were shown for each bandit pair). This would also relate to work on RL and working memory: Collins, A. G., & Frank, M. J. (2012). How much of reinforcement learning is working memory, not reinforcement learning? A behavioral, computational, and neurogenetic analysis. European Journal of Neuroscience, 35(7), 10241035.

We thank the reviewer for this point. The specific interleaved structure of the agents is described in the main text:

“Each agent provided feedback for 5 trials for each bandit pair (with the agent order interleaved within the bandit pair).”

As well as in the methods section:

“Feedback agents were randomly interleaved across trials subject to the constraint that each agent appeared on 5-trials for each bandit pair.”

We also thank the reviewer for mentioning the relevant work on working memory. We have now added it to our discussion point:

“In our main study, we show that participants revised their beliefs based on entirely non-credible feedback, whereas an ideal Bayesian strategy dictates such feedback should be ignored. This finding resonates with the “continued-influence effect” whereby misleading information continues to influence an individual's beliefs even after it has been retracted (59,60). One possible explanation is that some participants failed to infer that feedback from the 1-star agent was statistically void of information content, essentially random (e.g., the group-level credibility of this agent was estimated by our free-credibility Bayesian model as higher than 50%). Participants were instructed that this feedback would be “a lie” 50% of the time but were not explicitly told that this meant it was random and should therefore be disregarded. Notably, however, there was no corresponding evidence random feedback affected behaviour in our discovery study. It is possible that an individual’s ability to filter out random information might have been limited due to a high cognitive load induced by our main study task, which required participants to track the values of three bandit pairs and juggle between three interleaved feedback agents (whereas in our discovery study each experimental block featured a single bandit pair). Future studies should explore more systematically how the ability to filter random feedback depends on cognitive load (61).”

(5) Why does the choice-repetition regression include "only trials for which the last same-pair trial featured the 3-star agent and in which the context trial featured a different bandit pair"? This could be stated more plainly.

We thank the reviewer for this question. When we previously submitted our manuscript, we thought that finding enhanced credit-assignment for fully credible feedback following potential disinformation from a different context would constitute a striking demonstration of our “contrast effect”. However, upon reexamining this finding we found out we had a coding error (affecting how trials were filtered). We have now rerun and corrected this analysis. We have assessed the contrast effect for both "same-context" trials (where the contextual trial featured the same bandit pair as the learning trial) and "different-context" trials (where the contextual trial featured a different bandit pair). Our re-analysis reveals a selective significant contrast effect in the samecontext condition, but no significant effect in the different-context condition. We have updated the main text to reflect these corrected findings and provide a clearer explanation of the analysis:

“A comparison of empirical and Bayesian credit-assignment parameters revealed a further deviation from ideal Bayesian learning: participants showed an exaggerated credit-assignment for the 3-star agent compared with Bayesian models [Wilcoxon signed-rank test, instructed-credibility Bayesian model (median difference=0.74, z=11.14); free-credibility Bayesian model (median difference=0.62, z=10.71), all p’s<0.001] (Fig. 3a). One explanation for enhanced learning for the 3-star agents is a contrast effect, whereby credible information looms larger against a backdrop of non-credible information. To test this hypothesis, we examined whether the impact of feedback from the 3-star agent is modulated by the credibility of the agent in the trial immediately preceding it. More specifically, we reasoned that the impact of a 3-star agent would be amplified by a “low credibility context” (i.e., when it is preceded by a low credibility trial). In a binomial mixed effects model, we regressed choice-repetition on feedback valence from the last trial featuring the same bandit pair (i.e., the learning trial) and the feedback agent on the trial immediately preceding that last trial (i.e., the contextual credibility; see Methods for model-specification). This analysis included only learning trials featuring the 3-star agent, and context trials featuring the same bandit pair as the learning trial (Fig. 4a). We found that feedback valence interacted with contextual credibility (F(2,2086)=11.47, p<0.001) such that the feedback-effect (from the 3-star agent) decreased as a function of the preceding context-credibility (3-star context vs. 2-star context: b= -0.29, F(1,2086)=4.06, p=0.044; 2star context vs. 1-star context: b=-0.41, t(2086)=-2.94, p=0.003; and 3-star context vs. 1-star context: b=0.69, t(2086)=-4.74, p<0.001) (Fig. 4b). This contrast effect was not predicted by simulations of our main models of interest (Fig. 4c). No effect was found when focussing on contextual trials featuring a bandit pair different than the one in the learning trial (see SI 3.5). Thus, these results support an interpretation that credible feedback exerts a greater impact on participants’ learning when it follows non-credible feedback, in the same learning context.”

We have modified the discussion accordingly as well:

“A striking finding in our study was that for a fully credible feedback agent, credit assignment was exaggerated (i.e., higher than predicted by our Bayesian models). Furthermore, the effect of fully credible feedback on choice was further boosted when it was preceded by a low-credibility context related to current learning. We interpret this in terms of a “contrast effect”, whereby veridical information looms larger against a backdrop of disinformation (21). One upshot is that exaggerated learning might entail a risk of jumping to premature conclusions based on limited credible evidence (e.g., a strong conclusion that a vaccine is produces significant side-effect risks based on weak credible information, following non-credible information about the same vaccine). An intriguing possibility, that could be tested in future studies, is that participants strategically amplify the extent of learning from credible feedback to dilute the impact of learning from noncredible feedback. For example, a person scrolling through a social media feed, encountering copious amounts of disinformation, might amplify the weight they assign to credible feedback in order to dilute effects of ‘fake news’. Ironically, these results also suggest that public campaigns might be more effective when embedding their messages in low-credibility contexts , which may boost their impact.”

And we have included some additional analyses in the SI document:

“3.5 Contrast effects for contexts featuring a different bandit

Given that we observed a contrast effect when both the learning and the immediately preceding "context trial” involved the same pair of bandits, we next investigated whether this effect persisted when the context trial featured a different bandit pair – a situation where the context would be irrelevant to the current learning. Again, we used in a binomial mixed effects model, regressing choice-repetition on feedback valence in the learning trial and the feedback agent in the context trial. This analysis included only learning trials featuring the 3-star agent, and context trials featuring a different bandit pair than the learning trial (Fig. S22a). We found no significant evidence of an interaction between feedback valence and contextual credibility (F(2,2364)=0.21, p=0.81) (Fig. S22b). This null result was consistent with the range of outcomes predicted by our main computational models (Fig. S22c).

We aimed to formally compare the influence of two types of contextual trials: those featuring the same bandit pair as the learning trial versus those featuring a different pair. To achieve this, we extended our mixedeffects model by incorporating a new predictor variable, "CONTEXT_TYPE" which coded whether the contextual trial involved the same bandit pair (coded as -0.5) or a different bandit pair (+0.5) compared to the learning trial. The Wilkinson notation for this expanded mixed-effects model is:

𝑅𝐸𝑃𝐸𝐴𝑇 ~ 𝐶𝑂𝑁𝑇𝐸𝑋𝑇_𝑇𝑌𝑃𝐸 ∗ 𝐹𝐸𝐸𝐷𝐵𝐴𝐶𝐾 ∗ (𝐶𝑂𝑁𝑇𝐸𝑋𝑇_2-star + 𝐶𝑂𝑁𝑇𝐸𝑋𝑇_3-star) + 𝐵𝐸𝑇𝑇𝐸𝑅 + (1|𝑝𝑎𝑟𝑡𝑖𝑐𝑖𝑝𝑎𝑛𝑡)

This expanded model revealed a significant three-way interaction between feedback valence, contextual credibility, and context type (F(2,4451) = 7.71, p<0.001). Interpreting this interaction, we found a 2-way interaction between context-source and feedback valence when the context was the same (F(2,4451) = 12.03, p<0.001), but not when context was different (F(2,4451) = 0.23, p = 0.79). Further interpreting the double feedback-valence * context-source interaction (for the same context) we obtained the same conclusions as reported in the main text.”

(6) Why apply the "Truth-CA" model and not the Bayesian variant that it was motivated by?

Thanks for this very useful suggestion. We are unsure if we fully understand the question. The Truth-CA model was not motivated by a new Bayesian model. Our Bayesian models were simply used to make the point that participants may partially discriminate between truthful and untruthful feedback (for a given source). This led to the idea that perhaps more credit is assigned for truth (than lie) trials, which is what we found using our Truth-CA model. Note we show that our Bayesian models cannot account for this modulation.

We have now improved our "Truth-CA" model. Previously, our Truth-CA model considered whether feedback on each trial was true or not based on realized latent true outcomes. However, it is possible that the very same feedback would have had an opposite truth-status if the latent true outcome was different (recall true outcomes are stochastic). This injects noise into the trial classification in our previous model. To avoid this, in our new model feedback is modulated by the probability the reported feedback is true (marginalized over stochasticity of true outcome).

We have described this new model in the methods section:

“Additionally, we formulated a “Truth-CA” model, which worked as our Credibility-CA model, but incorporated a free truth-bonus parameter (TB). This parameter modulates the extent of credit assignment for each agent based on the posterior probability of feedback being true (given the credibility of the feedback agent, and the true reward probability of the chosen bandit). The chosen bandit was updated as follows:

𝑄 ← (1 – 𝑓_Q) ∗ 𝑄 + [𝐶𝐴(𝑎𝑔𝑒𝑛𝑡) + 𝑇𝐵 ∗ (𝑃(𝑡𝑟𝑢𝑡ℎ) − 0.5)] ∗ 𝐹

where P(truth) is the posterior probability of the feedback being true in the current trial (for exact calculation of P(truth) see “Methods: Bayesian estimation of posterior belief that feedback is true”).”

All relevant results have been updated accordingly in the main text:

“To formally address whether feedback truthfulness modulates credit assignment, we fitted a new variant of the CA model (the “Truth-CA” model) to the data. This variant works as our Credibility-CA model but incorporated a truth-bonus parameter (TB) which increases the degree of credit assignment for feedback as a function of the experimenter-determined likelihood the feedback is true (which is read from the curves in Fig 6a when x is taken to be the true probability the bandit is rewarding). Specifically, after receiving feedback, the Q-value of the chosen option is updated according to the following rule: 𝑄 ← (1 – 𝑓_Q) ∗ 𝑄 + [𝐶𝐴(𝑎𝑔𝑒𝑛𝑡) + 𝑇𝐵 ∗ (𝑃(𝑡𝑟𝑢𝑡ℎ) − 0.5)] ∗ 𝐹 where 𝑇𝐵 is the free parameter representing the truth bonus, and 𝑃(𝑡𝑟𝑢𝑡ℎ) is the probability the received feedback being true (from the experimenter’s perspective). We acknowledge that this model falls short of providing a mechanistically plausible description of the credit assignment process, because participants have no access to the experimenter’s truthfulness likelihoods (as the true bandit reward probabilities are unknown to them). Nonetheless, we use this ‘oracle model’ as a measurement tool to glean rough estimates for the extent to which credit assignment Is boosted as a function of its truthfulness likelihood. Fitting this Truth-CA model to participants' behaviour revealed a significant positive truth-bonus (mean=0.21, t(203)=3.12, p=0.002), suggesting that participants indeed assign greater weight to feedback that is likely to be true (Fig. 6c; see SI 3.3.1 for detailed ML parameter results). Notably, simulations using our other models (Methods) consistently predicted smaller truth biases (compared to the empirical bias) (Fig. 6d). Moreover, truth bias was still detected even in a more flexible model that allowed for both a positivity bias and truth-bias (see SI 3.7). The upshot is that participants are biased to assign higher credit based on feedback that is more likely to be true in a manner that is inconsistent with out Bayesian models and above and beyond the previously identified positivity biases.“

Finally, the Supplementary Information for the discovery study has also been revised to feature this analysis:

“We next assessed whether participants infer whether the feedback they received on each trial was true or false and adjust their credit assignment based on this inference. We again used the “Truth-CA” model to obtain estimates for the truth bonus (TB), the increase in credit assignment as a function of the posterior probability of feedback being true. As in our main study, the fitted truth bias parameter was significantly positive, indicating that participants assign greater weight to feedback they believe is likely to be true (Fig, S4a; see SI 3.3.1 for detailed ML parameter results). Strikingly, model-simulations (Methods) predicted a lower truth bonus than the one observed in participants (Fig. S4b).”

(7) "Overall, the results from this study support the exact same conclusions (See SI section 1.2) but with one difference. In the discovery study, we found no evidence for learning based on 50%-credibility feedback when examining either the feedback effect on choice repetition or CA in the credibility-CA model (SI 1.2.3)" - this seems like a very salient difference, when the paper reports the feedback effect as a primary finding of interest, though I understand there remains a valence-based difference.

We agree with the reviewer and thank them for this suggestion. We now state explicitly throughout the manuscript that this finding was obtained only in one of our two studies. In the section “Discovery study” of the results we state explicitly this finding was not found in the discovery study:

“However, we found no evidence for learning based on 50%-credibility feedback when examining either the feedback effect on choice repetition or CA in the credibility-CA model (SI 1.2.3).”

We also note that related to another concern from R3 (that perseveration may masquerade as positivity bias) we conducted additional analyses (detailed in SI 3.6.2). These analyses revealed that the observed positivity bias for the 1-star agent in the discovery study falls within the range predicted by simple choice-perseveration. Consequently, we have removed the suggestion that participants still learn from the random agent in the discovery study. Furthermore, we have modified the discussion section to include a possible explanation for this discrepancy between the two studies:

“Notably, however, there was no corresponding evidence random feedback affected behaviour in our discovery study. It is possible that an individual’s ability to filter out random information might have been limited due to a high cognitive load induced by our main study task, which required participants to track the values of three bandit pairs and juggle between three interleaved feedback agents (whereas in our discovery study each experimental block featured a single bandit pair). Future studies should explore more systematically how the ability to filter random feedback depends on cognitive load (61).”

(8) "Participants were instructed that this feedback would be "a lie 50% of the time but were not explicitly told that this meant it was random and should therefore be disregarded." - I agree that this is a possible explanation for updating from the random source. It is a meaningful caveat.

Thank you for this thought. While this can be seen as a caveat—since we don’t know what would have happened with explicit instructions—we also believe it is interesting from another perspective. In many real-life situations, individuals may have all the necessary information to infer that the feedback they receive is uninformative, yet still fail to do so, especially when they are not explicitly told to ignore it.

In future work, we plan to examine how behaviour changes when participants are given more explicit instructions—for example, that the 50%-credibility agent provides purely random feedback.

(9) "Future studies should investigate conditions that enhance an ability to discard disinformation, such as providing explicit instructions to ignore misleading feedback, manipulations that increase the time available for evaluating information, or interventions that strengthen source memory." - there is work on some of this in the misinformation literature that should be cited, such as the "continued influence effect". For example: Johnson, H. M., & Seifert, C. M. (1994). Sources of the continued influence effect: When misinformation in memory affects later inferences. Journal of experimental psychology: Learning, memory, and cognition, 20(6), 1420.

We thank the reviewer for pointing us towards the relevant literature. We have now included citations about the “continued influence effect” of misinformation in the discussion:

“In our main study, we show that participants revised their beliefs based on entirely non-credible feedback, whereas an ideal Bayesian strategy dictates such feedback should be ignored. This finding resonates with the “continued-influence effect” whereby misleading information continues to influence an individual's beliefs even after it has been retracted (59,60).”

(10) Are the authors arguing that choice-confirmation bias may be at play? Work on choice-confirmation bias generally includes counterfactual feedback, which is not present here.

We agree with the reviewer that a definitive test for choice-confirmation bias typically requires counterfactual feedback, which is not present in our current task. In our discussion, we indeed suggest that the positivity bias we observe may stem from a form of choice-confirmation, drawing on the extensive literature on this bias in reinforcement learning (Lefebvre et al., 2017; Palminteri et al., 2017; Palminteri & Lebreton, 2022). However, we fully acknowledge that this link is a hypothesis and that explicitly testing for choice-confirmation bias would necessitate a future study specifically incorporating counterfactual feedback. We have included a clarification of this point in the discussion:

“Previous reinforcement learning studies, report greater credit-assignment based on positive compared to negative feedback, albeit only in the context of veridical feedback (43,44,62). Here, supporting our a-priori hypothesis we show that this positivity bias is amplified for information of low and intermediate credibility (in absolute terms in the discovery study, and relative to the overall extent of CA in both studies) . Of note, previous literature has interpreted enhanced learning for positive outcomes in reinforcement learning as indicative of a confirmation bias (42,44). For example, positive feedback may confirm, to a greater extent than negative feedback one’s choice as superior (e.g., “I chose the better of the two options”). Leveraging the framework of motivated cognition (35), we posited that feedback of uncertain veracity (e.g., low credibility) amplifies this bias by incentivising individuals to self-servingly accept positive feedback as true (because it confers positive, desirable outcomes), and explain away undesirable, choice-disconfirming, negative feedback as false. This could imply an amplified confirmation bias on social media, where content from sources of uncertain credibility, such as unknown or unverified users, is more easily interpreted in a self-serving manner, disproportionately reinforcing existing beliefs (63). In turn, this could contribute to an exacerbation of the negative social outcomes previously linked to confirmation bias such as polarization (64,65), the formation of ‘echo chambers’ (19), and the persistence of misbelief regarding contemporary issues of importance such as vaccination (66,67) and climate change (68–71). We note however, that further studies are required to determine whether positivity bias in our task is indeed a form of confirmation bias.”

Reviewer #3 (Public review):

Summary

This paper investigates how disinformation affects reward learning processes in the context of a two-armed bandit task, where feedback is provided by agents with varying reliability (with lying probability explicitly instructed). They find that people learn more from credible sources, but also deviate systematically from optimal Bayesian learning: They learned from uninformative random feedback, learned more from positive feedback, and updated too quickly from fully credible feedback (especially following low-credibility feedback). Overall, this study highlights how misinformation could distort basic reward learning processes, without appeal to higher-order social constructs like identity.

Strengths

(1) The experimental design is simple and well-controlled; in particular, it isolates basic learning processes by abstracting away from social context.

(2) Modeling and statistics meet or exceed the standards of rigor.

(3) Limitations are acknowledged where appropriate, especially those regarding external validity.

(4) The comparison model, Bayes with biased credibility estimates, is strong; deviations are much more compelling than e.g., a purely optimal model.

(5) The conclusions are interesting, in particular the finding that positivity bias is stronger when learning from less reliable feedback (although I am somewhat uncertain about the validity of this conclusion)

We deeply thank the reviewer for highlighting the strengths of this work.

Weaknesses

(1) Absolute or relative positivity bias?

In my view, the biggest weakness in the paper is that the conclusion of greater positivity bias for lower credible feedback (Figure 5) hinges on the specific way in which positivity bias is defined. Specifically, we only see the effect when normalizing the difference in sensitivity to positive vs. negative feedback by the sum. I appreciate that the authors present both and add the caveat whenever they mention the conclusion (with the crucial exception of the abstract). However, what we really need here is an argument that the relative definition is the right way to define asymmetry....

Unfortunately, my intuition is that the absolute difference is a better measure. I understand that the relative version is common in the RL literature; however previous studies have used standard TD models, whereas the current model updates based on the raw reward. The role of the CA parameter is thus importantly different from a traditional learning rate - in particular, it's more like a logistic regression coefficient (as described below) because it scales the feedback but not the decay. Under this interpretation, a difference in positivity bias across credibility conditions corresponds to a three-way interaction between the exponentially weighted sum of previous feedback of a given type (e.g., positive from the 75% credible agent), feedback positivity, and condition (dummy coded). This interaction corresponds to the nonnormalized, absolute difference.

Importantly, I'm not terribly confident in this argument, but it does suggest that we need a compelling argument for the relative definition.

We thank the reviewer for raising this important point about the definition of positivity bias, and for their thoughtful discussion on the absolute versus relative measures. We believe that the relative valence bias offers a distinct and valuable perspective on positivity bias. Conceptually, this measure describes positivity bias in a manner akin to a “percentage difference” relative to the overall level of learning which allows us to control for the overall decreases in the overall amount of credit assignment as feedback becomes less credible. We are unsure if one measure is better or more correct than the other and we believe that reporting both measures enriches the understanding of positivity bias and allows for a more comprehensive characterization of this phenomenon (as long as these measures are interpreted carefully). We have stated the significance of the relative measure in the results section:

“Following previous research, we quantified positivity bias in 2 ways: 1) as the absolute difference between credit-assignment based on positive or negative feedback, and 2) as the same difference but relative to the overall extent of learning. We note that the second, relative, definition, is more akin to “percentage change” measurements providing a control for the overall lower levels of credit-assignment for less credible agent.”

We also wish to point out that in our discovery study we had some evidence for amplification of positivity bias in absolute sense.

(2) Positivity bias or perseveration?

A key challenge in interpreting many of the results is dissociating perseveration from other learning biases. In particular, a positivity bias (Figure 5) and perseveration will both predict a stronger correlation between positive feedback and future choice. Crucially, the authors do include a perseveration term, so one would hope that perseveration effects have been controlled for and that the CA parameters reflect true positivity biases. However, with finite data, we cannot be sure that the variance will be correctly allocated to each parameter (c.f. collinearity in regressions). The fact that CA- is fit to be negative for many participants (a pattern shown more strongly in the discovery study) is suggestive that this might be happening. A priori, the idea that you would ever increase your value estimate after negative feedback is highly implausible, which suggests that the parameter might be capturing variance besides that it is intended to capture.

The best way to resolve this uncertainty would involve running a new study in which feedback was sometimes provided in the absence of a choice - this would isolate positivity bias. Short of that, perhaps one could fit a version of the Bayesian model that also includes perseveration. If the authors can show that this model cannot capture the pattern in Figure 5, that would be fairly convincing.

We thank the reviewer for this very insightful and crucial point regarding the potential confound between positivity bias and perseveration. We entirely agree that distinguishing these effects can be challenging. To rigorously address this concern and ascertain that our observed positivity bias, particularly its inflation for low-credibility feedback, is not merely an artifact of perseveration, we conducted additional analyses as suggested.

First, following the reviewer’s suggestion we simulated our Bayesian models, including a perseveration term, for both our main and discovery studies. Crucially, none of these simulations predicted the specific pattern of inflated positivity bias for low-credibility feedback that we identified in participants.

Additionally, taking a “devil’s advocate” approach, we tested whether our credibility-CA model (which includes perseveration but not a feedback valence bias) can predict our positivity bias findings. Thus, we simulated 100 datasets using our Credibility-CA model (based on empirical best-fitting parameters). We then fitted each of these simulated datasets using our CredibilityValence CA model. By examining the distribution of results across these synthetic datasets fits and comparing them to the actual results from participants, we found that while perseveration could indeed lead (as the reviewer suspected) to an artifactual positivity bias, it could not predict the magnitude of the observed inflation of positivity bias for low-credibility feedback (whether measured in absolute or relative terms).

Based on these comprehensive analyses, we are confident that our main results concerning the modulation of a valence bias as a function of source-credibility cannot be accounted by simple choice-perseveration. We have briefly explained these analyses in the main results section:

“Previous research has suggested that positivity bias may spuriously arise from pure choice-perseveration (i.e., a tendency to repeat previous choices regardless of outcome) (49,50). While our models included a perseveration-component, this control may not be preferent. Therefore, in additional control analyses, we generated synthetic datasets using models including choice-perseveration but devoid of feedback-valence bias, and fitted them with our credibility-valence model (see SI 3.6.1). These analyses confirmed that perseveration can masquerade as an apparent positivity bias. Critically, however, these analyses also confirmed that perseveration cannot account for our main finding of increased positivity bias, relative to the overall extent of CA, for low-credibility feedback.”

Additionally, we have added a detailed description of these additional analyses and their findings to the Supplementary Information document:

“3.6 Positivity bias results cannot be explained by a pure perseveration

3.6.1 Main study

Previous research has suggested it may be challenging to dissociate between a feedback-valence positivity bias and perseveration (i.e., a tendency to repeat previous choices regardless of outcome). While our Credit Assignment (CA) models already include a perseveration mechanism to account for this, this control may not be perfect. We thus conducted several tests to examine if our positivity-bias related results could be accounted for by perseveration.

First we examined whether our Bayesian-models, augmented by a perseveration mechanism (as in our CA model) can generate predictions similar to our empirical results. We repeated our cross-fitting procedure to these extended Bayesian models. To briefly recap, this involved fitting participant behavior with them, generating synthetic datasets based on the resulting maximum likelihood (ML) parameters, and then fitting these simulated datasets with our Credibility-Valence CA model (which is designed to detect positivity bias). This test revealed that adding perseveration to our Bayesian models did not predict a positivity bias in learning. In absolute terms there was a small negativity bias (instructed-credibility Bayesian: b=−0.19, F(1,1218)=17.78, p<0.001, Fig. S23a-b; free-credibility Bayesian: b=−0.17, F(1,1218)=13.74, p<0.001, Fig. S23d-e). In relative terms we detected no valence related bias (instructed-credibility Bayesian: b=−0.034, F(1,609)=0.45, p=0.50, Fig. S22c; free-credibility Bayesian: b=−0.04, F(1,609)=0.51, p=0.47, Fig. S23f). More critically, these simulations also did not predict a change in the level of positivity bias as a function of feedback credibility, neither at an absolute level (instructed-credibility Bayesian: F(2,1218)=0.024, p=0.98, Fig. S23b; free-credibility Bayesian: F(2,1218)=0.008, p=0.99, Fig. S23e), nor at a relative level (instructedcredibility Bayesian: F(2,609)=1.57, p=0.21, Fig. S23c; free-credibility Bayesian: F(2,609)=0.13, p=0.88, Fig. S23f). The upshot is that our positivity-bias findings cannot be accounted for by our Bayesian models even when these are augmented with perseveration.

However, it is still possible that empirical CA parameters from our credibility-valence model (reported in main text Fig. 5) were distorted, absorbing variance from a perseveration. To address this, we took a “devil's advocate” approach testing the assumption that CA parameters are not truly affected by feedback valance and that there is only perseveration in our data. Towards that goal, we simulated data using our CredibilityCA model (which includes perseveration but does not contain a valence bias in its learning mechanism) and then fitted these synthetic datasets using our Credibility-Valence CA model to see if the observed positivity bias could be explained by perseveration alone. Specifically, we generated 101 “group-level” synthetic datasets (each including one simulation for each participant, based on their empirical ML parameters), and fitted each dataset with our Credibility-Valence CA model. We then analysed the resulting ML parameters in each dataset using the same mixed-effects models as described in the main text, examining the distribution of effects of interest across these simulated datasets. Comparing these simulation results to the data from participants revealed a nuanced picture. While the positivity bias observed in participants is within the range predicted by a pure perseveration account when measured in absolute terms (Fig. S24a), it is much higher than predicted by pure perseveration when measured relative to the overall level of learning (Fig. S24c). More importantly, the inflation in positivity bias for lower credibility feedback is substantially higher in participants than what would be predicted by a pure perseveration account, a finding that holds true for both absolute (Fig. S24b) and relative (Fig. S24d) measures.”

“3.6.2 Discovery study

We then replicated these analyses in our discovery study to confirm our findings. We again checked whether extended versions of the Bayesian models (including perseveration) predicted the positivity bias results observed. Our cross-fitting procedure showed that the instructed-credibility Bayesian model with perseveration did predict a positivity bias for all credibility levels in this discovery study, both when measured in absolute terms [50% credibility (b=1.74,t(824)=6.15), 70% credibility (b=2.00,F(1,824)=49.98), 85% credibility (b=1.81,F(1,824)=40.78), 100% credibility (b=2.42,F(1,824)=72.50), all p's<0.001], and in relative terms [50% credibility (b=0.25,t(412)=3.44), 70% credibility (b=0.31,F(1,412)=17.72), 85% credibility (b=0.34,F(1,412)=21.06), 100% credibility (b=0.42,F(1,412)=31.24), all p's<0.001]. However, importantly, these simulations did not predict a change in the level of positivity bias as a function of feedback credibility, neither at an absolute level (F(3,412)=1.43,p=0.24), nor at a relative level (F(3,412)=2.06,p=0.13) (Fig. S25a-c). In contrast, simulations of the free-credibility Bayesian model (with perseveration) predicted a slight negativity bias when measured in absolute terms (b=−0.35,F(1,824)=5.14,p=0.024), and no valence bias when measured relative to the overall degree of learning (b=0.05,F(1,412)=0.55,p=0.46). Crucially, this model also did not predict a change in the level of positivity bias as a function of feedback credibility, neither at an absolute level (F(3,824)=0.27,p=0.77), nor at a relative level (F(3,412)=0.76,p=0.47) (Fig. S25d-f).

As in our main study, we next assessed whether our Credibility-CA model (which includes perseveration but no valence bias) predicted the positivity bias results observed in participants in the discovery study. This analysis revealed that the average positivity bias in participants is higher than predicted by a pure perseveration account, both when measured in absolute terms (Fig. S26a) and in relative terms (Fig. S26c). Specifically, only the aVBI for the 70% credibility agent was above what a perseveration account would predict, while the rVBI for all agents except the completely credible one exceeded that threshold. Furthermore, the inflation in positivity bias for lower credibility feedback (compared to the 100% credibility agent) is significantly higher in participants than would be predicted by a pure perseveration account, in both absolute (Fig. S26b) and relative (Fig. S26d) terms.

Together, these results show that the general positivity bias observed in participants could be predicted by an instructed-credibility Bayesian model with perseveration, or by a CA model with perseveration. Moreover, we find that these two models can predict a positivity bias for the 50% credibility agent, raising a concern that our positivity bias findings for this source may be an artefact of not-fully controlled for perseveration. However, the credibility modulation of this positivity bias, where the bias is amplified for lower credibility feedback, is consistently not predicted by perseveration alone, regardless of whether perseveration is incorporated into a Bayesian or a CA model. This finding suggests that participants are genuinely modulating their learning based on feedback credibility, and that this modulation is not merely an artifact of choice perseveration.”

(3) Veracity detection or positivity bias?

The "True feedback elicits greater learning" effect (Figure 6) may be simply a re-description of the positivity bias shown in Figure 5. This figure shows that people have higher CA for trials where the feedback was in fact accurate. But assuming that people tend to choose more rewarding options, true-feedback cases will tend to also be positive-feedback cases. Accordingly, a positivity bias would yield this effect, even if people are not at all sensitive to trial-level feedback veracity. Of course, the reverse logic also applies, such that the "positivity bias" could actually reflect discounting of feedback that is less likely to be true. This idea has been proposed before as an explanation for confirmation bias (see Pilgrim et al, 2024 https://doi.org/10.1016/j.cognition.2023.105693and much previous work cited therein). The authors should discuss the ambiguity between the "positivity bias" and "true feedback" effects within the context of this literature....

Before addressing these excellent comments, we first note that we have now improved our "TruthCA" model. Previously, our Truth-CA model considered whether feedback on each trial was true or not based on realized latent true outcomes. However, it is possible that the very same feedback would have had an opposite truth-status if the latent true outcome was different (recall true outcomes are stochastic). This injects noise into the trial classification in our former model. To avoid this, in our new model feedback is modulated by the probability the reported feedback is true (marginalized over stochasticity of true outcome). Please note in our responses below that we conducted extensive analysis to confirm that positivity bias doesn’t in fact predict the truthbias we detect using our truth biased model

We have described this new model in the methods section:

“Additionally, we formulated a “Truth-CA” model, which worked as our Credibility-CA model, but incorporated a free truth-bonus parameter (TB). This parameter modulates the extent of credit assignment for each agent based on the posterior probability of feedback being true (given the credibility of the feedback agent, and the true reward probability of the chosen bandit). The chosen bandit was updated as follows:

𝑄 ← (1 – 𝑓_Q) ∗ 𝑄 + [𝐶𝐴(𝑎𝑔𝑒𝑛𝑡) + 𝑇𝐵 ∗ (𝑃(𝑡𝑟𝑢𝑡ℎ) − 0.5)] ∗ 𝐹

where P(truth) is the posterior probability of the feedback being true in the current trial (for exact calculation of P(truth) see “Methods: Bayesian estimation of posterior belief that feedback is true”).”

All relevant results have been updated accordingly in the main text:

To formally address whether feedback truthfulness modulates credit assignment, we fitted a new variant of the CA model (the “Truth-CA” model) to the data. This variant works as our Credibility-CA model, but incorporated a truth-bonus parameter (TB) which increases the degree of credit assignment for feedback as a function of the experimenter-determined likelihood the feedback is true (which is read from the curves in Fig 6a when x is taken to be the true probability the bandit is rewarding). Specifically, after receiving feedback, the Q-value of the chosen option is updated according to the following rule:

𝑄 ← (1 – 𝑓_Q) ∗ 𝑄 + [𝐶𝐴(𝑎𝑔𝑒𝑛𝑡) + 𝑇𝐵 ∗ (𝑃(𝑡𝑟𝑢𝑡ℎ) − 0.5)] ∗ 𝐹

where 𝑇𝐵 is the free parameter representing the truth bonus, and 𝑃(𝑡𝑟𝑢𝑡ℎ) is the probability the received feedback being true (from the experimenter’s perspective). We acknowledge that this model falls short of providing a mechanistically plausible description of the credit assignment process, because participants have no access to the experimenter’s truthfulness likelihoods (as the true bandit reward probabilities are unknown to them). Nonetheless, we use this ‘oracle model’ as a measurement tool to glean rough estimates for the extent to which credit assignment Is boosted as a function of its truthfulness likelihood.

Fitting this Truth-CA model to participants' behaviour revealed a significant positive truth-bonus (mean=0.21, t(203)=3.12, p=0.002), suggesting that participants indeed assign greater weight to feedback that is likely to be true (Fig. 6c; see SI 3.3.1 for detailed ML parameter results). Notably, simulations using our other models (Methods) consistently predicted smaller truth biases (compared to the empirical bias) (Fig. 6d). Moreover, truth bias was still detected even in a more flexible model that allowed for both a positivity bias and truth-bias (see SI 3.7). The upshot is that participants are biased to assign higher credit based on feedback that is more likely to be true in a manner that is inconsistent with out Bayesian models and above and beyond the previously identified positivity biases.”

Finally, the Supplementary Information for the discovery study has also been revised to feature this analysis:

“We next assessed whether participants infer whether the feedback they received on each trial was true or false and adjust their credit assignment based on this inference. We again used the “Truth-CA” model to obtain estimates for the truth bonus (TB), the increase in credit assignment as a function of the posterior probability of feedback being true. As in our main study, the fitted truth bias parameter was significantly positive, indicating that participants assign greater weight to feedback they believe is likely to be true (Fig, S4a; see SI 3.3.1 for detailed ML parameter results). Strikingly, model-simulations (Methods) predicted a lower truth bonus than the one observed in participants (Fig. S4b).”

Additionally, we thank the reviewer for pointing us to the relevant work by Pilgrim et al. (2024). We agree that the relationship between "true feedback" and "positivity bias" effects is nuanced, and their potential overlap warrants careful consideration. Note our analyses suggest that this is not solely the case. Firstly, simulations of our Credibility-Valence CA model predict only a small "truth bonus" effect, which is notably smaller than what we observed in participants. Secondly, we formulated an extension of our "Truth-CA" model that includes a valence bias in credit assignment. If our truth bonus results were merely an artifact of positivity bias, this extended model should absorb that variance, producing a null truth bonus parameter. However, fitting this model to participant data still revealed a significant positive truth bonus, which again exceeds the range predicted by simulations of our Credibility CA model:

“3.7 Truth inference is still detected when controlling for valence bias

Given that participants frequently select bandits that are, on average, mostly rewarding, it is reasonable to assume that positive feedback is more likely to be objectively true than negative feedback. This raises a question if the "truth inference" effect we observed in participants might simply be an alternative description of a positivity bias in learning. To directly test this idea, we extended our Truth-CA model to explicitly account for a valence bias in credit assignment. This extended model features separate CA parameters for positive and negative feedback for each agent. When we fitted this new model to participant behavior, it still revealed a significant truth bonus in both the main study (Wilkoxon’s signrank test: median = 0.09, z(202)=2.12, p=0.034; Fig. S27a) and the discovery study (median = 3.52, z(102)=7.86, p<0.001; Fig. S27c). Moreover, in the main study, this truth bonus remained significantly higher than what was predicted by all the alternative models, with the exception of the instructed-credibility bayesian model (Fig. S27b). In the discovery study, the truth bonus was significantly higher than what was predicted by all the alternative models (Fig. S27d).”

Together, these findings suggest that our truth inference results are not simply a re-description of a positivity bias.

Conversely, we acknowledge the reviewer's point that our positivity bias results could potentially stem from a more general truth inference mechanism. We believe that this possibility should be addressed in a future study where participants rate their belief that received feedback is true (rather than a lie).We have extended our discussion to clarify this possibility and to include the suggested citation:

“Our findings show that individuals increase their credit assignment for feedback in proportion to the perceived probability that the feedback is true, even after controlling for source credibility and feedback valence. Strikingly, this learning bias was not predicted by any of our Bayesian or credit-assignment (CA) models. Notably, our evidence for this bias is based on a “oracle model” that incorporates the probability of feedback truthfulness from the experimenter's perspective, rather than the participant’s. This raises an important open question: how do individuals form beliefs about feedback truthfulness, and how do these beliefs influence credit assignment? Future research should address this by eliciting trial-by-trial beliefs about feedback truthfulness. Doing so would also allow for testing the intriguing possibility that an exaggerated positivity bias for non-credible sources reflects, to some extent, a truth-based discounting of negative feedback—i.e., participants may judge such feedback as less likely to be true. However, it is important to note that the positivity bias observed for fully credible sources (here and in other literature) cannot be attributed to a truth bias—unless participants were, against instructions, distrustful of that source.”

The authors get close to this in the discussion, but they characterize their results as differing from the predictions of rational models, the opposite of my intuition. They write:

“Alternative "informational" (motivation-independent) accounts of positivity and confirmation bias predict a contrasting trend (i.e., reduced bias in low- and medium credibility conditions) because in these contexts it is more ambiguous whether feedback confirms one's choice or outcome expectations, as compared to a full-credibility condition.”

I don't follow the reasoning here at all. It seems to me that the possibility for bias will increase with ambiguity (or perhaps will be maximal at intermediate levels). In the extreme case, when feedback is fully reliable, it is impossible to rationally discount it (illustrated in Figure 6A). The authors should clarify their argument or revise their conclusion here.

We apologize for the lack of clarity in our previous explanation. We removed the sentence you cited (it was intended to make a different point which we now consider non-essential). Our current narration is consistent with the point you are making.

(4) Disinformation or less information?

Zooming out, from a computational/functional perspective, the reliability of feedback is very similar to reward stochasticity (the difference is that reward stochasticity decreases the importance/value of learning in addition to its difficulty). I imagine that many of the effects reported here would be reproduced in that setting. To my surprise, I couldn't quickly find a study asking that precise question, but if the authors know of such work, it would be very useful to draw comparisons. To put a finer point on it, this study does not isolate which (if any) of these effects are specific to disinformation, rather than simply less information. I don't think the authors need to rigorously address this in the current study, but it would be a helpful discussion point.

We thank the reviewer for highlighting the parallel (and difference) between feedback reliability and reward stochasticity. However, we have not found any comparable results in the literature. We also note that our discussion includes a paragraph addressing the locus of our effects making the point that more studies are necessary to determine whether our findings are due to disinformation per se or sources being less informative. While this paragraph was included in the previous version it led us to infer our Discussion was too long and we therefore shortened it considerably:

“An important question arises as to the psychological locus of the biases we uncovered. Because we were interested in how individuals process disinformation—deliberately false or misleading information intended to deceive or manipulate—we framed the feedback agents in our study as deceptive, who would occasionally “lie” about the true choice outcome. However, statistically (though not necessarily psychologically), these agents are equivalent to agents who mix truth-telling with random “guessing” or “noise” where inaccuracies may arise from factors such as occasionally lacking access to true outcomes, simple laziness, or mistakes, rather than an intent to deceive. This raises the question of whether the biases we observed are driven by the perception of potential disinformation as deceitful per se or simply as deviating from the truth. Future studies could address this question by directly comparing learning from statistically equivalent sources framed as either lying or noisy. Unlike previous studies wherein participants had to infer source credibility from experience (30,37,72), we took an explicit-instruction approach, allowing us to precisely assess source-credibility impact on learning, without confounding it with errors in learning about the sources themselves. More broadly, our work connects with prior research on observational learning, which examined how individuals learn from the actions or advice of social partners (72–75). This body of work has demonstrated that individuals integrate learning from their private experiences with learning based on others’ actions or advice—whether by inferring the value others attribute to different options or by mimicking their behavior (57,76). However, our task differs significantly from traditional observational learning. Firstly, our feedback agents interpret outcomes rather than demonstrating or recommending actions (30,37,72). Secondly, participants in our study lack private experiences unmediated by feedback sources. Finally, unlike most observational learning paradigms, we systematically address scenarios with deliberately misleading social partners. Future studies could bridge this by incorporating deceptive social partners into observational learning, offering a chance to develop unified models of how individuals integrate social information when credibility is paramount for decision-making.”

(5) Over-reliance on analyzing model parameters

Most of the results rely on interpreting model parameters, specifically, the "credit assignment" (CA) parameter. Exacerbating this, many key conclusions rest on a comparison of the CA parameters fit to human data vs. those fit to simulations from a Bayesian model. I've never seen anything like this, and the authors don't justify or even motivate this analysis choice. As a general rule, analyses of model parameters are less convincing than behavioral results because they inevitably depend on arbitrary modeling assumptions that cannot be fully supported. I imagine that most or even all of the results presented here would have behavioral analogues. The paper would benefit greatly from the inclusion of such results. It would also be helpful to provide a description of the model in the main text that makes it very clear what exactly the CA parameter is capturing (see next point).

We thank the reviewer for this important suggestion which we address together with the following point.

(6) RL or regression?

I was initially very confused by the "RL" model because it doesn't update based on the TD error. Consequently, the "Q values" can go beyond the range of possible reward (SI Figure 5). These values are therefore not Q values, which are defined as expectations of future reward ("action values"). Instead, they reflect choice propensities, which are sometimes notated $h$ in the RL literature. This misuse of notation is unfortunately quite common in psychology, so I won't ask the authors to change the variable. However, they should clarify when introducing the model that the Q values are not action values in the technical sense. If there is precedent for this update rule, it should be cited.

Although the change is subtle, it suggests a very different interpretation of the model.

Specifically, I think the "RL model" is better understood as a sophisticated logistic regression, rather than a model of value learning. Ignoring the decay term, the CA term is simply the change in log odds of repeating the just-taken action in future trials (the change is negated for negative feedback). The PERS term is the same, but ignoring feedback. The decay captures that the effect of each trial on future choices diminishes with time. Importantly, however, we can re-parameterize the model such that the choice at each trial is a logistic regression where the independent variables are an exponentially decaying sum of feedback of each type (e.g., positive-cred50, positive-cred75, ... negative-cred100). The CA parameters are simply coefficients in this logistic regression.

Critically, this is not meant to "deflate" the model. Instead, it clarifies that the CA parameter is actually not such an assumption-laden model estimate. It is really quite similar to a regression coefficient, something that is usually considered "model agnostic". It also recasts the non-standard "cross-fitting" approach as a very standard comparison of regression coefficients for model simulations vs. human data. Finally, using different CA parameters for true vs false feedback is no longer a strange and implausible model assumption; it's just another (perfectly valid) regression. This may be a personal thing, but after adopting this view, I found all the results much easier to understand.

We thank the reviewer for their insightful and illuminating comments, particularly concerning the interpretation of our model parameters and the nature of our Credit assignment model. We believe your interpretation of the model is accurate and we now narrate it to readers in the hope that our modelling will become clearer and more intuitively. We also present to readers how these recasts our “cross-fitting” approach in the way you suggested (we return to this point below).

Broadly, while we agree that modelling results depend on underlying assumptions, we believe that “model-agnostic” approaches also have important limitations—especially in reinforcement learning (RL), where choices are shaped by histories of past events, which such approaches often fail to fully account for. As students of RL, we are frequently struck by how careful modelling demonstrates that seemingly meaningful “model-agnostic” patterns can emerge as artefacts of unaccounted-for variables. We also note that the term “model-agnostic” is difficult to define—after all, even regression models rely on assumptions, and some computational models make richer or more transparent assumptions than others. Ideally, we aim to support our findings using converging methods wherever possible.

We want to clarify that many of our reported findings indeed stem from straightforward behavioral analyses (e.g., simple regressions of choice-repetition), which do not rely on complex modeling assumptions. The two key results that primarily depend on the analysis of model parameters are our findings related to positivity bias and truth inference.

Regarding the positivity bias, identifying truly model-agnostic behavioral signatures, distinct from effects like choice-perseveration, has historically been a significant challenge in the literature. Classical research on this bias rests on the interpretation of model parameters (Lefebvre et al., 2017; Palminteri et al., 2017), or at least on the use of models to assess what an “unbiased learner” baseline should look like (Palminteri & Lebreton, 2022). Some researchers have suggested possible regressions incorporating history effects to detect positivity bias from choicerepetition behavior, but these regressions (as our model) rely on subtle assumptions about forgetting and history effects (Toyama et al., 2019). Specifically, in our case, this issue is also demonstrated by analysis we conducted related to the previous point the reviewer made (about perseveration masquerading as positivity bias). We believe that dissociating clearly positivity bias from perseveration is an important challenge for the field going forward.

For our truth inference results, obtaining purely behavioral signatures is similarly challenging due to the intricate interdependencies (the reviewer has identified in previous points) between agent credibility, feedback valence, feedback truthfulness, and choice accuracy within our task design.

Finally, we agree with the reviewer that regression coefficients are often interpreted as a “modelagnostic” pattern. From this perspective even our findings regarding positivity and truth bias are not a case of over-reliance on complex model assumptions but are rather a way to expose deviations between empirical “sophisticated” regression coefficients and coefficients predicted from Bayesian models.

We have now described the main learning rule of our model in the main text to ensure that the meaning of the CA parameters is clearer for readers:

“Next, we formulated a family of non-Bayesian computational RL models. Importantly, these models can flexibly express non-Bayesian learning patterns and, as we show in following sections, can serve to identify learning biases deviating from an idealized Bayesian strategy. Here, an assumption is that during feedback, the choice propensity for the chosen bandit (which here is represented by a point estimate, “Q value“, rather than a distribution) either increases or decreases (for positive or negative feedback, respectively) according to a magnitude quantified by the free “Credit-Assignment (CA)” model parameters (47):

𝑄(𝑐ℎ𝑜𝑠𝑒𝑛) ← (1 – 𝑓_Q) ∗ 𝑄(𝑐ℎ𝑜𝑠𝑒𝑛) + 𝐶𝐴(𝑎𝑔𝑒𝑛𝑡, 𝑣𝑎𝑙𝑒𝑛𝑐𝑒) ∗ 𝐹

where F is the feedback received from the agents (coded as 1 for reward feedback and -1 for non-reward feedback), while fQ (∈[0,1]) is the free parameter representing the forgetting rate of the Q-value (Fig. 2a, bottom panel; Fig. S5b; Methods). The probability to choose a bandit (say A over B) in this family of models is a logistic function of the contrast choice-propensities between these two bandits. One interpretation of this model is as a “sophisticated” logistic regression, where the CA parameters take the role of “regression coefficients” corresponding to the change in log odds of repeating the just-taken action in future trials based on the feedback (+/- CA for positive or negative feedback, respectively; the model also includes gradual perseveration which allows for constant log-odd changes that are not affected by choice feedback; see “Methods: RL models”) . The forgetting rate captures the extent to which the effect of each trial on future choices diminishes with time. The Q-values are thus exponentially decaying sums of logistic choice propensities based on the types of feedback a bandit received.”

We also explain the implications of this perspective for our cross-fitting procedure:

“To further characterise deviations between behaviour and our Bayesian learning models, we used a “crossfitting” method. Treating CA parameters as data-features of interest (i.e., feedback dependent changes in choice propensity), our goal was to examine if and how empirical features differ from features extracted from simulations of our Bayesian learning models. Towards that goal, we simulated synthetic data based on Bayesian agents (using participants’ best fitting parameters), but fitted these data using the CA-models, obtaining what we term “Bayesian-CA parameters” (Fig. 2d; Methods). A comparison of these BayesianCA parameters, with empirical-CA parameters obtained by fitting CA models to empirical data, allowed us to uncover patterns consistent with, or deviating from, ideal-Bayesian value-based inference. Under the sophisticated logistic-regression interpretation of the CA-model family the cross-fitting method comprises a comparison between empirical regression coefficients (i.e., empirical CA parameters) and regression coefficient based on simulations of Bayesian models (Bayesian CA parameters). Using this approach, we found that both the instructed-credibility and free-credibility Bayesian models predicted increased BayesianCA parameters as a function of agent credibility (Fig. 3c; see SI 3.1.1.2 Tables S8 and S9). However, an in-depth comparison between Bayesian and empirical CA parameters revealed discrepancies from ideal Bayesian learning, which we describe in the following sections.”

Recommendations for the authors:

Reviewer #3 (Recommendations for the authors):

(1) Keep terms consistent, e.g., follow-up vs. main; hallmark vs. traditional.

We have now changed the text to keep terms consistent.

(2) CA model is like a learning rate; but it's based on the raw reward, not the TD error - this seems strange.

We thank the reviewer for this comment. We understand that the use of a CA model instead of a TD error model may seem unusual at first glance. However, the CA model offers an important advantage: it more easily accommodates what we term "negative learning rates". This means that some participants may treat certain agents (especially the random one) as consistently deceitful, leading them to effectively increase/reduce choice tendencies following negative/positive feedback. A CA model handles this naturally by allowing negative CA parameters as a simple extension of positive ones. In contrast, adapting a TD error model to account for this is more complex. For instance, attempting to introduce a "negative learning rate" makes the RW model behave in a non-stable manner (e.g., Q values become <0 or >1). At the initial stages of our project, we explored different approaches to dealing with this issue and we found the CA model provides the best approach. For these reasons, we decided to proceed with our CA model.

Additionally, we used the CA model in previous studies (e.g., Moran, Dayan & Dolan (2021)) where we included (in SI) a detailed discussion of the similarities and difference between creditassignment and Rescorla-Wagner models

(3) Why was the follow-up study not pre-registered?

We appreciate the reviewer's comment regarding preregistration, which we should have done. Unfortunately, this is now “water under the bridge” but going forward we hope to pre-register increasing parts of our work.

(4) Other work looking at reward stochasticity?

As noted in point 4 of the main weaknesses, previous work on reward stochasticity primarily focused on explaining the increase/decrease in learning and its mechanistic bases under varying stochasticity levels. In our study, we uniquely characterize several specific learning biases that are modulated by source credibility, a topic not extensively explored within the existing reward stochasticity framework, as far as we know.

(5) Equation 1 is different from the one in the figure?

The reviewer is completely correct. The figure provides a simplified visual representation, primarily focusing on the feedback-based update of the Q-value, and for simplicity, it omits the forgetting term present in the full Equation 1. To ensure complete clarity and prevent any misunderstanding, we have now incorporated a more detailed explanation of the model, including the complete Equation 1 and its components, directly within the main text. This comprehensive description will ensure that readers are fully aware of how the model operates.

“Next, we formulated a family of non-Bayesian computational RL models. Importantly, these models can flexibly express non-Bayesian learning patterns and, as we show in following sections, can serve to identify learning biases deviating from an idealized Bayesian strategy. Here, an assumption is that during feedback, the choice propensity for the chosen bandit (which here is represented by a point estimate, “Q value“, rather than a distribution) either increases or decreases (for positive or negative feedback, respectively) according to a magnitude quantified by the free “Credit-Assignment (CA)” model parameters (47):

𝑄(𝑐ℎ𝑜𝑠𝑒𝑛) ← (1 – 𝑓_Q) ∗ 𝑄(𝑐ℎ𝑜𝑠𝑒𝑛) + 𝐶𝐴(𝑎𝑔𝑒𝑛𝑡, 𝑣𝑎𝑙𝑒𝑛𝑐𝑒) ∗ 𝐹

where F is the feedback received from the agents (coded as 1 for reward feedback and -1 for non-reward feedback), while fQ (∈[0,1]) is the free parameter representing the forgetting rate of the Q-value (Fig. 2a, bottom panel; Fig. S5b; Methods).”

(6) Please describe/plot the distribution of all fitted parameters in the supplement. I would include the mean and SD in the main text (methods) as well.

Following the reviewer’s suggestions, we have included in the Supplementary Document tables displaying the mean and SD of fitted parameters from participants for our main models of interest. We have also plotted the distributions of such parameters. Both for the main study:

(7) "A novel approach within the disinformation literature by exploiting a Reinforcement Learning (RL) experimental framework".

The idea of applying RL to disinformation is not new. Please tone down novelty claims. It would be nice to cite/discuss some of this work as well.

https://arxiv.org/abs/2106.05402?utm_source=chatgpt.com https://www.scirp.org/pdf/jbbs_2022110415273931.pdf https://papers.ssrn.com/sol3/papers.cfm?abstract_id=4173312

We thank the reviewer for pointing us towards relevant literature. We have now toned down the sentence in the introduction and cited the references provided:

“To address these questions, we adopt a novel approach within the disinformation literature by exploiting a Reinforcement Learning (RL) experimental framework (36). While RL has guided disinformation research in recent years (37–40), our approach is novel in using one of its most popular tasks: the “bandit task”.”

(8) Figure 3a - The figures should be in the order that they're referenced (3 is referenced before 2).

We generally try to stick to this important rule but, in this case, we believe that our ordering serves better the narrative and hope the reviewer will excuse this small violation.

(9) "Additionally, we found a positive feedback-effect for the 3-star agent"

What is the analysis here? To avoid confusion with the "positive feedback" effect, consider using "positive effect of feedback". The dash wasn't sufficient to avoid confusion in my case.

We have now updated the terms in the text to avoid confusion.

(10) The discovery study revealed even stronger results supporting a conclusion that the credibility-CA model was superior to both Bayesian models for most subjects

This is very subjective, but I'll just mention that my "cherry-picking" flag was raised by this sentence. Are you only mentioning cases where the discovery study was consistent with the main study? Upon a closer read, I think the answer is most likely "no", but you might consider adopting a more systematic (perhaps even explicit) policy on when and how you reference the discovery study to avoid creating this impression in a more casual reader.

We thank the reviewer for this valuable suggestion. To prevent any impression of "cherry-picking", we have removed specific references to the discovery study from the main body of the text. Instead, all discussions regarding the convergence and divergence of results between the two studies are now in the dedicated section focusing on the discovery study:

“The discovery study (n=104) used a disinformation task structurally similar to that used in our main study, but with three notable differences: 1) it included 4 feedback agents, with credibilities of 50%, 70%, 85% and 100%, represented by 1, 2, 3, and 4 stars, respectively; 2) each experimental block consisted of a single bandit pair, presented over 16 trials (with 4 trials for each feedback agent); and 3) in certain blocks, unbeknownst to participants, the two bandits within a pair were equally rewarding (see SI section 1.1). Overall, this study's results supported similar conclusions as our main study (see SI section 1.2) with a few differences. We found convergent support for increased learning from more credible sources (SI 1.2.1), superior fit for the CA model over Bayesian models (SI 1.2.2) and increased learning from feedback inferred to be true (SI 1.2.6). Additionally, we found an inflation of positivity bias for low-credibility both when measured relative to the overall level of credit assignment (as in our main study), or in absolute terms (unlike in our main study) (Fig. S3; SI 1.2.5). Moreover, choice-perseveration could not predict an amplification of positivity bias for low-credibility sources (see SI 3.6.2). However, we found no evidence for learning based on 50%-credibility feedback when examining either the feedback effect on choice repetition or CA in the credibility-CA model (SI 1.2.3).”

(11) An in-depth comparison between Bayesian and empirical CA parameters revealed discrepancies from normative Bayesian learning.

Consider saying where this in-depth comparison can be found (based on my reading, I think you're referring to the next section?

We have now modified the sentence for better clarity:

“However, an in-depth comparison between Bayesian and empirical CA parameters revealed discrepancies from ideal Bayesian learning, which we describe in the following sections.”

(12) "which essentially provides feedback" Perhaps you meant "random feedback"?

We have modified the text as suggested by the reviewer.

<(13) Essentially random

Why "essentially"? Isn't it just literally random?

We have modified the text as suggested by the reviewer.

(14) Both Bayesian models predicted an attenuated credit-assignment for the 3-star agent

Attenuated relative to what? I wouldn't use this word if you mean weaker than what we see in the human data. Instead, I would say people show an exaggerated credit-assignment, since Bayes is the normative baseline.

We changed the text according to the reviewer’s suggestion:

“A comparison of empirical and Bayesian credit-assignment parameters revealed a further deviation from ideal Bayesian learning: participants showed an exaggerated credit-assignment for the 3-star agent compared with Bayesian models.”

(15) "there was no difference between 2-star and 3-star agent contexts (b=0.051, F(1,2419)=0.39, p=0.53)"

You cannot confirm the null hypothesis! Instead, you can write "The difference between 2-star and 3-star agent contexts was not significant". Although even with this language, you should be careful that your conclusions don't rest on the lack of a difference (the next sentence is somewhat ambiguous on this point).

Additionally, the reported b coefs do not match the figure, which if anything, suggests a larger drop from 0.75 (2-star) to 1 (3-star). Is this a mixed vs fixed effects thing? It would be helpful to provide an explanation here.

We thank the reviewer for this question. When we previously submitted our manuscript, we thought that finding enhanced credit-assignment for fully credible feedback following potential disinformation from a DIFFERENT context would constitute a striking demonstration of our “contrast effect”. However, upon reexamining this finding we found out we had a coding error (affecting how trials were filtered). We have now rerun and corrected this analysis. We have assessed the contrast effect for both "same-context" trials (where the contextual trial featured the same bandit pair as the learning trial) and "different-context" trials (where the contextual trial featured a different bandit pair). Our re-analysis reveals a selective significant contrast effect in the same-context condition, but no significant effect in the different-context condition. We have updated the main text to reflect these corrected findings and provide a clearer explanation of the analysis:

“A comparison of empirical and Bayesian credit-assignment parameters revealed a further deviation from ideal Bayesian learning: participants showed an exaggerated credit-assignment for the 3-star agent compared with Bayesian models [Wilcoxon signed-rank test, instructed-credibility Bayesian model (median difference=0.74, z=11.14); free-credibility Bayesian model (median difference=0.62, z=10.71), all p’s<0.001] (Fig. 3a). One explanation for enhanced learning for the 3-star agents is a contrast effect, whereby credible information looms larger against a backdrop of non-credible information. To test this hypothesis, we examined whether the impact of feedback from the 3-star agent is modulated by the credibility of the agent in the trial immediately preceding it. More specifically, we reasoned that the impact of a 3-star agent would be amplified by a “low credibility context” (i.e., when it is preceded by a low credibility trial). In a binomial mixed effects model, we regressed choice-repetition on feedback valence from the last trial featuring the same bandit pair (i.e., the learning trial) and the feedback agent on the trial immediately preceding that last trial (i.e., the contextual credibility; see Methods for model-specification). This analysis included only learning trials featuring the 3-star agent, and context trials featuring the same bandit pair as the learning trial (Fig. 4a). We found that feedback valence interacted with contextual credibility (F(2,2086)=11.47, p<0.001) such that the feedback-effect (from the 3-star agent) decreased as a function of the preceding context-credibility (3-star context vs. 2-star context: b= -0.29, F(1,2086)=4.06, p=0.044; 2star context vs. 1-star context: b=-0.41, t(2086)=-2.94, p=0.003; and 3-star context vs. 1-star context: b=0.69, t(2086)=-4.74, p<0.001) (Fig. 4b). This contrast effect was not predicted by simulations of our main models of interest (Fig. 4c). No effect was found when focussing on contextual trials featuring a bandit pair different than the one in the learning trial (see SI 3.5). Thus, these results support an interpretation that credible feedback exerts a greater impact on participants’ learning when it follows non-credible feedback, in the same learning context.”

We have modified the discussion accordingly as well:

“A striking finding in our study was that for a fully credible feedback agent, credit assignment was exaggerated (i.e., higher than predicted by our Bayesian models). Furthermore, the effect of fully credible feedback on choice was further boosted when it was preceded by a low-credibility context related to current learning. We interpret this in terms of a “contrast effect”, whereby veridical information looms larger against a backdrop of disinformation (21). One upshot is that exaggerated learning might entail a risk of jumping to premature conclusions based on limited credible evidence (e.g., a strong conclusion that a vaccine produces significant side-effect risks based on weak credible information, following non-credible information about the same vaccine). An intriguing possibility, that could be tested in future studies, is that participants strategically amplify the extent of learning from credible feedback to dilute the impact of learning from noncredible feedback. For example, a person scrolling through a social media feed, encountering copious amounts of disinformation, might amplify the weight they assign to credible feedback in order to dilute effects of ‘fake news’. Ironically, these results also suggest that public campaigns might be more effective when embedding their messages in low-credibility contexts, which may boost their impact.”

And we have included some additional analyses in the SI document:

“3.5 Contrast effects for contexts featuring a different bandit Given that we observed a contrast effect when both the learning and the immediately preceding "context trial” involved the same pair of bandits, we next investigated whether this effect persisted when the context trial featured a different bandit pair – a situation where the context would be irrelevant to the current learning. Again, we used in a binomial mixed effects model, regressing choice-repetition on feedback valence in the learning trial and the feedback agent in the context trial. This analysis included only learning trials featuring the 3-star agent, and context trials featuring a different bandit pair than the learning trial (Fig. S22a). We found no significant evidence of an interaction between feedback valence and contextual credibility (F(2,2364)=0.21, p=0.81) (Fig. S22b). This null result was consistent with the range of outcomes predicted by our main computational models (Fig. S22c).”

We aimed to formally compare the influence of two types of contextual trials: those featuring the same bandit pair as the learning trial versus those featuring a different pair. To achieve this, we extended our mixedeffects model by incorporating a new predictor variable, "CONTEXT_TYPE" which coded whether the contextual trial involved the same bandit pair (coded as -0.5) or a different bandit pair (+0.5) compared to the learning trial. The Wilkinson notation for this expanded mixed-effects model is:

𝑅𝐸𝑃𝐸𝐴𝑇 ~ 𝐶𝑂𝑁𝑇𝐸𝑋𝑇_𝑇𝑌𝑃𝐸 ∗ 𝐹𝐸𝐸𝐷𝐵𝐴𝐶𝐾 ∗ (𝐶 𝐶𝑂𝑁𝑇𝐸𝑋𝑇_2-star + 𝐶𝑂𝑁𝑇𝐸𝑋𝑇_3-star) + 𝐵𝐸𝑇𝑇𝐸𝑅 + (1|𝑝𝑎𝑟𝑡𝑖𝑐𝑖𝑝𝑎𝑛𝑡)

This expanded model revealed a significant three-way interaction between feedback valence, contextual credibility, and context type (F(2,4451) = 7.71, p<0.001). Interpreting this interaction, we found a 2-way interaction between context-source and feedback valence when the context was the same (F(2,4451) = 12.03, p<0.001), but not when context was different (F(2,4451) = 0.23, p = 0.79). Further interpreting the double feedback-valence * context-source interaction (for the same context) we obtained the same conclusions as reported in the main text.”

(16) "Strikingly, model-simulations (Methods) showed this pattern is not predicted by any of our other models"

Why doesn't the Bayesian model predict this?

Thanks for the comment. Overall, Bayesian models do predict a slight truth inference effect (see Figure 6d). However, these effects are not as strong as the ones observed in participants, suggesting that our results go beyond what would be predicted by a Bayesian model.

Conceptually, it's important to note that the Bayesian model can infer (after controlling for source credibility and feedback valence) whether feedback is truthful based solely on prior beliefs about the chosen bandit. Using this inferred truth to amplify the weight of truthful feedback would effectively amount to “bootstrapping on one’s own beliefs.” This is most clearly illustrated with the 50% agent: if one believes that a chosen bandit yields rewards 70% of the time, then positive feedback is more likely to be truthful than negative feedback. However, a Bayesian observer would also recognize that, given the agent’s overall unreliability, such feedback should be ignored regardless.

(17) "A striking finding in our study was that for a fully credible feedback agent, credit assignment was exaggerated (i.e., higher than predicted by a Bayesian strategy)".

"Since we did not find any significant interactions between BETTER and the other regressors, we decided to omit it from the model formulation".

Was this decision made after seeing the data? If so, please report the original analysis as well.

We have included the BETTER regressor again, and we have re-run the analyses. We now report the results of such regression. We have also changed the methods section accordingly:

“We used a different mixed-effects binomial regression model to test whether value learning from the 3-star agent was modulated by contextual credibility. We focused this analysis on instances where the previous trial with the same bandit pair featured the 3-star agent. We regressed the variable REPEAT, which indicated whether the current trial repeated the choice from the previous trial featuring the same bandit-pair (repeated choice=1, non-repeated choice=0). We included the following regressors: FEEDBACK coding the valence of feedback in the previous trial with the same bandit pair (positive=0.5, negative=-0.5), CONTEXT2-star indicating whether the trial immediately preceding the previous trial with the same bandit pair (context trial) featured the 2-star agent (feedback from 2-star agent=1, otherwise=0), and CONTEXT3star indicating whether the trial immediately preceding the previous trial with the same bandit pair featured the 3-star agent. We also included a regressor (BETTER) coding whether the bandit chosen in the learning trial was the better -mostly rewarding- or the worse -mostly unrewarding- bandit within the pair. We included in this analysis only current trials where the context trial featured a different bandit pair. The model in Wilkinson’s notation was:

𝑅𝐸𝑃𝐸𝐴𝑇~ 𝐹𝐸𝐸𝐷𝐵𝐴𝐶𝐾 ∗ (𝐶𝑂𝑁𝑇𝐸𝑋𝑇_2-star + 𝐶𝑂𝑁𝑇𝐸𝑋𝑇_3-star) + 𝐵𝐸𝑇𝑇𝐸𝑅 + (1|𝑝𝑎𝑟𝑡𝑖𝑐𝑖𝑝𝑎𝑛𝑡) ( 13 )

In figure 4c, we independently calculate the repeat probability difference for the better (mostly rewarding) and worse (mostly non-rewarding) bandits and averaged across them. This calculation was done at the participants level, and finally averaged across participants.”

(m/s)/s= change in Velocity over time

For Jourdain, it allowed her to 1) pursue a career in higher education; 2) enrol for a doctorate in Paris 3) write a dissertation 4) be hired as Vice-head at St. Hughe

Media acts as government’s tool due to dependency on official information and shared elite values.

Media as Actors: Independent influencers shaping the foreign policy agenda through coverage. Criticism: Some argue media follow political consensus rather than create it.

People are consuming media is so many different ways, washing out traditional forms of media

Growth in radio stations, cable systems, and digital platforms (Facebook, Twitter, TikTok).

Decline of print newspapers; increased digital access.

symbolizes the rise of 24-hour news

How is it receiving a charge? Isn't the oil initially neutral? What about the blowing out through the atomizer allows it to receive a charge? Also, can we control the charge that the droplet receives?

what is the "kinetic energy of agitation?" I've never heard of that before - I assume it has something to do with mixing or moving particles (particularly in a gas) around, but I'm just curious what it actually is and why it's important

Why? Why was the fixation on the individual? It seems bizarre to isolate a study on the effects of mass media on individual cases rather that the equivalent audience size (mass)

Actually fascinating

In the United States, could this refer to the anti-trust laws?

Cross-connection

How can you use in practicum what you cannot define

I guess this makes sense when a field of study organically grows from the cross-section of several other studies

Internal and external logics - capitalist media systems v publicly funded create differing results

This is the multi-faceted approach that Teke was referring to

DR @ VK: Should we use R inline code for things that will change, like the model number, and centralize these?

Renewables in Energy Supply

Does it have higher potential because it received an electron from A or it received the electron BECAUSE it have higher potential?

The platform is not abolitionist but firmly anti-slavery expansion.

Balances states’ rights with strong national projects (railroad, tariffs, land distribution).

Appeals to a wide coalition: free soil settlers, industrial workers, farmers, and immigrants.

The West is central: as the future of freedom, industry, and settlement.

Shows Republicans using corruption as a political weapon.

Positions Republicans as pro-Union and anti-secession.

Strong defense of the party’s legitimacy.

preservation of union and constitution

map not final, hover over legend not interactive. Too many digits after the decimal in most countries. Population data seems wrong (use format XXX.X million)

can these be in bullet points?

eLife Assessment

This valuable study combined careful computational modeling, a large patient sample, and replication in an independent general population sample to provide a computational account of a difference in risk-taking between people who have attempted suicide and those who have not. It is proposed that this difference reflects a general change in the approach to risky (high-reward) options and a lower emotional response to certain rewards. Evidence for the specificity of the effect to suicide, however, is incomplete, which would require additional analyses.

Reviewer #1 (Public review):

Summary:

The authors use a gambling task with momentary mood ratings from Rutledge et al. and compare computational models of choice and mood to identify markers of decisional and affective impairments underlying risk-prone behavior in adolescents with suicidal thoughts and behaviors (STB). The results show that adolescents with STB show enhanced gambling behavior (choosing the gamble rather than the sure amount), and this is driven by a bias towards the largest possible win rather than insensitivity to possible losses. Moreover, this group shows a diminished effect of receiving a certain reward (in the non-gambling trials) on mood. The results were replicated in an undifferentiated online sample where participants were divided into groups with or without STB based on their self-report of suicidal ideation on one question in the Beck Depression Inventory self-report instrument. The authors suggest, therefore, that adolescents with decreased sensitivity to certain rewards may need to be monitored more closely for STB due to their increased propensity to take risky decisions aimed at (expected) gains (such as relief from an unbearable situation through suicide), regardless of the potential losses.

Strengths:

(1) The study uses a previously validated task design and replicates previously found results through well-explained model-free and model-based analyses.

(2) Sampling choice is optimal, with adolescents at high risk; an ideal cohort to target early preventative diagnoses and treatments for suicide.

(3) Replication of the results in an online cohort increases confidence in the findings.

(4) The models considered for comparison are thorough and well-motivated. The chosen models allow for teasing apart which decision and mood sensitivity parameters relate to risky decision-making across groups based on their hypotheses.

(5) Novel finding of mood (in)sensitivity to non-risky rewards and its relationship with risk behavior in STB.

Weaknesses:

(1) The sample size of 25 for the S- group was justified based on previous studies (lines 181-183); however, all three papers cited mention that their sample was low powered as a study limitation.

(2) Modeling in the mediation analysis focused on predicting risk behavior in this task from the model-derived bias for gains and suicidal symptom scores. However, the prediction of clinical interest is of suicidal behaviors from task parameters/behavior - as a psychiatrist or psychologist, I would want to use this task to potentially determine who is at higher risk of attempting suicide and therefore needs to be more closely watched rather than the other way around (predicting behavior in the task from their symptom profile). Unfortunately, the analyses presented do not show that this prediction can be made using the current task. I was left wondering: is there a correlation between beta_gain and STB? It is also important to test for the same relationships between task parameters and behavior in the healthy control group, or to clarify that the recommendations for potential clinical relevance of these findings apply exclusively to people with a diagnosis of depression or anxiety disorder. Indeed, in line 672, the authors claim their results provide "computational markers for general suicidal tendency among adolescents", but this was not shown here, as there were no models predicting STB within patient groups or across patients and healthy controls.

(3) The FDR correction for multiple comparisons mentioned briefly in lines 536-538 was not clear. Which analyses were included in the FDR correction? In particular, did the correlations between gambling rate and BSI-C/BSI-W survive such correction? Were there other correlations tested here (e.g., with the TAI score or ERQ-R and ERQ-S) that should be corrected for? Did the mediation model survive FDR correction? Was there a correction for other mediation models (e.g., with BSI-W as a predictor), or was this specific model hypothesized and pre-registered, and therefore no other models were considered? Did the differences in beta_gain across groups survive FDR when including comparisons of all other parameters across groups? Because the results were replicated in the online dataset, it is ok if they did not survive FDR in the patient dataset, but it is important to be clear about this in presenting the findings in the patient dataset.

(4) There is a lack of explicit mention when replication analyses differ from the analyses in the patient sample. For instance, the mediation model is different in the two samples: in the patient sample, it is only tested in S+ and S- groups, but not in healthy controls, and the model relates a dimensional measure of suicidal symptoms to gambling in the task, whereas in the online sample, the model includes all participants (including those who are presumably equivalent to healthy controls) and the predictor is a binary measure of S+ versus S- rather than the response to item 9 in the BDI. Indeed, some results did not replicate at all and this needs to be emphasized more as the lack of replication can be interpreted not only as "the link between mood sensitivity to CR and gambling behavior may be specifically observable in suicidal patients" (lines 582-585) - it may also be that this link is not truly there, and without a replication it needs to be interpreted with caution.

(5) In interpreting their results, the authors use terms such as "motivation" (line 594) or "risk attitude" (line 606) that are not clear. In particular, how was risk attitude operationalized in this task? Is a bias for risky rewards not indicative of risk attitude? I ask because the claim is that "we did not observe a difference in risk attitude per se between STB and controls". However, it seems that participants with STB chose the risky option more often, so why is there no difference in risk attitude between the groups?

Reviewer #2 (Public review):

Summary:

This article addresses a very pertinent question: what are the computational mechanisms underlying risky behaviour in patients who have attempted suicide? In particular, it is impressive how the authors find a broad behavioural effect whose mechanisms they can then explain and refine through computational modeling. This work is important because, currently, beyond previous suicide attempts, there has been a lack of predictive measures. This study is the first step towards that: understanding the cognition on a group level. This is before being able to include it in future predictive studies (based on the cross-sectional data, this study by itself cannot assess the predictive validity of the measure).

Strengths:

(1) Large sample size.

(2) Replication of their own findings.

(3) Well-controlled task with measures of behaviour and mood + precise and well-validated computational modeling.

Weaknesses:

I can't really see any major weakness, but I have a few questions:

(1) I can see from the parameter recovery that the parameters are very well identified. Is it surprising that this is the case, given how many parameters there are for 90 trials? Could the authors show cross-correlations? I.e., make a correlation matrix with all real parameters and all fitted parameters to show that not only the diagonal (i.e., same data is the scatter plots in S3) are high, but that the off-diagonals are low.

(2) Could the authors clarify the result in Figure 2B of a correlation between gambling rate and suicidal ideation score, is that a different result than they had before with the group main effect? I.e., is your analysis like this: gambling rate ~ suicide ideation + group assignment? (or a partial correlation)? I'm asking because BSI-C is also different between the groups. [same comment for later analyses, e.g. on approach parameter].

(3) The authors correlate the impact of certain rewards on mood with the % gambling variable. Could there not be a more direct analysis by including mood directly in the choice model?

(4) In the large online sample, you split all participants into S+ and S-. I would have imagined that instead, you would do analyses that control for other clinical traits. Or, for example, you have in the S- group only participants who also have high depression scores, but low suicide items.

Reviewer #3 (Public review):

This manuscript investigates computational mechanisms underlying increased risk-taking behavior in adolescent patients with suicidal thoughts and behaviors. Using a well-established gambling task that incorporates momentary mood ratings and previously established computational modeling approaches, the authors identify particular aspects of choice behavior (which they term approach bias) and mood responsivity (to certain rewards) that differ as a function of suicidality. The authors replicate their findings on both clinical and large-scale non-clinical samples.

The main problem, however, is that the results do not seem to support a specific conclusion with regard to suicidality. The S+ and S- groups differ substantially in the severity of symptoms, as can be seen by all symptom questionnaires and the baseline and mean mood, where S- is closer to HC than it is to S+. The main analyses control for illness duration and medication but not for symptom severity. The supplementary analysis in Figure S11 is insufficient as it mistakes the absence of evidence (i.e., p > 0.05) for evidence of absence. Therefore, the results do not adequately deconfound suicidality from general symptom severity.

The second main issue is that the relationship between an increased approach bias and decreased mood response to CR is conceptually unclear. In this respect, it would be natural to test whether mood responses influence subsequent gambling choices. This could be done either within the model by having mood moderate the approach bias or outside the model using model-agnostic analyses.

Additionally, there is a conceptual inconsistency between the choice and mood findings that partly results from the analytic strategy. The approach bias is implemented in choice as a categorical value-independent effect, whereas the mood responses always scale linearly with the magnitude of outcomes. One way to make the models more conceptually related would be to include a categorical value-independent mood response to choosing to gamble/not to gamble.

The manuscript requires editing to improve clarity and precision. The use of terms such as "mood" and "approach motivation" is often inaccurate or not sufficiently specific. There are also many grammatical errors throughout the text.

Claims of clinical relevance should be toned down, given that the findings are based on noisy parameter estimates whose clinical utility for the treatment of an individual patient is doubtful at best.

Author response:

We thank the reviewers for recognizing the strengths of our work, as well as for their thoughtful and constructive feedback. In this provisional response, we focus on the main concern raised—namely, the need for stronger evidence that the effect is specific to suicide. A full revision of the manuscript will follow, in which we will address this point in greater depth and respond carefully to all additional comments in a point-by-point manner.

More specifically, reviewer 3 points out that “The main analyses control for illness duration and medication but not for symptom severity. The supplementary analysis in Figure S11 is insufficient as it mistakes the absence of evidence (i.e., p > 0.05) for evidence of absence.”. This is indeed an important point that we address below.

(1) Correction for symptom severity.

To address the request for evidence on specificity to suicidality beyond general symptom severity, we performed separate linear regressions to explain in gambling behaviour, value-insensitive approach parameter (β_gain), and mood sensitivity to certain rewards (β_CR) with group as a predictor (1 for S⁺ group and 0 for S^- group) and scores for anxiety and depression as covariates. Results remained significant after controlling anxiety and depression (ps < 0.027).

Author response table 1.

Given high correlations among anxiety and depression questionnaires (rs > 0.753, ps < 0.001), we performed Principal Components Analysis (PCA) on the clinical questionnaire to extract the orthogonal components, where each component explained 86.95%, 7.09%, 3.27%, and 2.68% variance, respectively. We then performed linear regressions using these components as covariates to control for anxiety and depression. Our main results remained significant (ps < 0.027).

Author response table 2.

We believe that these analyses provide evidence that the main effects on gambling and on mood were specific to suicide.

(2) Evidence of absence of effect of symptom severity

Based on clinical interviews, we included patients with and without suicidality (S⁺ and S^- groups). However, in line with suicidal-related literature (e.g., Tsypes et al., 2024), S⁺ and S^- differed substantially in the severity of symptoms (see Table 1). Although we median-split patients by the scores of general symptoms (e.g., depression and anxiety) and verified no significant differences in these severities (Figure S11), the “absence of evidence” cannot provide insights of “evidence of absence”. We, therefore, additionally conducted Bayesian statistics in gambling behavior, value-insensitive approach parameter, and mood sensitivity to certain rewards. BF₀₁ is a Bayes factor comparing the null model (M₀) to the alternative model (M₁), where M₀ assumes no group difference. BF₀₁ > 1 indicates that evidence favors M₀. As can be seen below, most results supported null hypothesis, suggesting that general symptoms of anxiety and depression overall did not influence our main results.

Author response table 3.

Overall, we believe that these analyses provide compelling evidence for the specificity of the effect to suicide, above and beyond depression and anxiety.

paid membership

no clear membrane

long-term relationships

no tooling

source google docs

Sideways Verifiable Community

Specifications Document v 1.2 (active version)

First one to star the project

I remember Grace making the point that it is our duty to try out people's work in adjacent forrows

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Document de Briefing : "Savoir ou périr" et les défis de l'éducation en France

Source: Extraits de "Rentrée scolaire : savoir ou réussite, pourquoi l’école tourne à l’envers (avec Bernard Lahire)"

Ce document de briefing synthétise les thèmes principaux, les idées essentielles et les faits importants tirés de l'entretien avec le sociologue Bernard Lahire, en se concentrant sur son ouvrage "Savoir ou périr" et ses réflexions sur le système éducatif français.

1. Le Savoir comme Condition de Survie Collective

Bernard Lahire insiste sur une idée fondamentale : le savoir n'est pas une simple affaire culturelle ou académique, mais une condition intrinsèque à la survie collective de l'humanité.

Il souligne que depuis l'aube de l'humanité, la transmission des expériences et des connaissances a été vitale pour l'adaptation des nouveaux venus et le développement des sociétés.

Citation clé : "on se rend pas compte que le savoir depuis le début de l'expérience de l'humanité euh c'est une des conditions de la survie collective"

Exemple historique : Lahire cite l'échec d'une expédition écossaise en Antarctique en 1845, dont aucun membre n'a survécu faute de savoirs adaptés à l'environnement hostile, contrairement aux Inuits qui y prospéraient.

Application contemporaine : La crise du coronavirus a mis en lumière l'urgence de la recherche et du savoir. Les investissements dans la recherche sur les coronavirus 10-15 ans auparavant, qui avaient été coupés, auraient pu accélérer la réponse.

"la recherche est directement euh concernée par les processus d'adaptation et que si on n'a pas ces savoirs et ben on est mal parti collectivement en fait".

Conséquence : L'oubli de cette vérité fondamentale nous rend "hors sol" et vulnérables aux défis futurs.

2. Le Système Scolaire "Tourne à l'Envers" : L'Obsession de l'Évaluation

Malgré l'importance vitale du savoir, Lahire dénonce un paradoxe français (et plus largement institutionnel) : l'école, censée être un lieu d'apprentissage, est devenue une institution "pilotée par l'évaluation", ce qui la fait "tourner à l'envers".

Dérive institutionnelle : Les institutions, créées avec un objectif précis, finissent souvent par dévier de leur mission initiale. L'école en est un exemple où l'évaluation a pris le pas sur l'apprentissage.

Bâchotage et surcharge des programmes : Lahire critique le "bâchotage" et la "surcharge des programmes", une problématique déjà soulevée par Marc Bloch en 1943. "on remplace le goût de la connaissance par le goût du succès".

Témoignages de grands scientifiques : Il s'appuie sur les expériences de personnalités comme Einstein, qui était "dégoûté de la physique" à force d'ingurgiter des choses par cœur, ou Grothendieck, qui critiquait ses collègues "trop dociles" et manquant d'ambition intellectuelle profonde.

La peur de la faute : Une spécificité française est la "peur de la faute", qui inhibe l'apprentissage des langues étrangères et contredit l'esprit scientifique, où l'erreur est une étape vers la découverte.

"on a tous peur de la faute je sais pas où on l'a attrapé mais évidemment que c'est à l'école que ça s'est passé".

Effets négatifs de la compétition et du stress : La peur et la compétition sont contre-productives pour l'apprentissage et la recherche.

Lahire témoigne de sa propre "boule au ventre" pendant sa scolarité et cite Laurent Lafforgue, lauréat de la médaille Fields, qui n'a presque rien publié pendant 10 ans, soulignant l'importance de laisser du temps aux chercheurs sans pression évaluative excessive.

La nécessité du retour, pas uniquement de l'évaluation : Les élèves ont besoin de retours, d'encouragements et de guidance (comme des tuteurs pour une plante), mais pas d'une évaluation constante et stressante.

3. Les Inégalités Sociales et la Reproduction : "Les enfants ne vivent pas dans le même monde"

Au-delà des problèmes pédagogiques, Lahire met en lumière l'impact profond des inégalités sociales et de la reproduction sociale sur les parcours scolaires, en s'appuyant sur son ouvrage "Enfance de classe".

Différences d'expériences dès le plus jeune âge : L'idée que "les enfants vivent au même moment dans la même société mais pas dans le même monde" illustre que, dès 5-6 ans, des enfants de milieux différents ont déjà des passés, des interactions et des horizons de possibles radicalement distincts.

"l'horizon n'est pas du tout le même les possibilités ne sont pas les mêmes".

Le mythe du "quand on veut on peut" : Lahire réfute fermement cette idée, la qualifiant de "régression scientifique".

Il souligne le "poids très très lourd des déterminismes sociaux d'origine".

Altricialité secondaire et dépendance aux adultes : La longue période de dépendance des enfants vis-à-vis des adultes (altricialité secondaire) a des conséquences majeures.

Les caractéristiques des parents (capitaux culturels, intérêt pour la pédagogie) influencent fortement la capacité des enfants à s'adapter à l'école.

Le rêve républicain de l'égalité : L'égalité n'est pas une réalité, mais un "horizon".

Les sociétés sont inégalitaires, mais l'État et les collectivités ont la responsabilité d'infléchir ces processus en offrant des opportunités culturelles et éducatives à ceux qui en sont le plus éloignés.

L'importance de l'ouverture culturelle : Les activités culturelles (théâtre, musées) sont cruciales pour "donner une chance" aux enfants de milieux défavorisés de s'approprier ces codes et de lutter contre l'autocensure. Sans cela, de nombreux élèves se projettent vers des "études courtes" faute de "background culturel".

4. Le Parcours Personnel de Bernard Lahire et la Critique Politique

Lahire, lui-même issu d'un "milieu ouvrier", a souffert du système scolaire mais a réussi grâce à un ensemble de facteurs (soutien familial, enseignants, chance), réfutant l'idée de sa seule "agentivité".

Réussite non individuelle : Sa réussite est le produit de "toutes les relations que [j'ai] eues avec toutes ces personnes et ces institutions".

Critique de la politique à court terme : Lahire exprime sa "tristesse" et son "dégoût" face à une politique perçue comme "décevante", "hors sol" et focalisée sur des querelles partisanes, plutôt que sur les défis à long terme (comme les enjeux climatiques ou éducatifs) qui nécessitent une vision sur "10000 ans".

Critique des décideurs ignorants des réalités éducatives : Il déplore la nomination de ministres de l'Éducation qui "connaissent très mal leur dossier", citant l'exemple d'Élisabeth Borne affirmant que le projet professionnel devait s'exprimer dès la maternelle.

5. Conséquences Budgétaires et Menaces sur l'Éducation

La situation est aggravée par les contraintes budgétaires, qui menacent directement les initiatives visant à lutter contre les inégalités.

Impact des coupes budgétaires : Les plans d'économie prévus pourraient entraîner une baisse des dotations pour les départements, impactant directement les collèges REP et les activités culturelles essentielles pour ces élèves. "il y a peut-être des activités culturelles qui vont devoir être annulées notamment pour louer un car".

En résumé, Bernard Lahire alerte sur un système éducatif qui a perdu de vue l'essence du savoir, obsédé par l'évaluation et incapable de compenser efficacement les inégalités sociales profondes, le tout aggravé par des décisions politiques court-termistes et un manque de compréhension des enjeux éducatifs.

eLife Assessment

This study presents a valuable finding on the molecular mechanisms that govern GABAergic inhibitory synapse function. The authors propose that Endophilin A1 serves as a novel regulator of GABAergic synapses by acting as a component of the inhibitory postsynaptic density. The findings are convincing and likely to interest a broad audience of scientists focusing on inhibitory synaptic transmission, the excitation-inhibition balance, and its disruption in disorders such as epilepsy.

Reviewer #1 (Public review):

Summary:

In the present study, Chen et al. investigate the role of Endophilin A1 in regulating GABAergic synapse formation and function. To this end, the authors use constitutive or conditional knockout of Endophilin A1 (EEN1) to assess the consequences on GABAergic synapse composition and function, as well as the outcome for PTZ-induced seizure susceptibility. The authors show that EEN1 KO mice show a higher susceptibility to PTZ-induced seizures, accompanied by a reduction in the GABAergic synaptic scaffolding protein gephyrin as well as specific GABAAR subunits and eIPSCs. The authors then investigate the underlying mechanisms, demonstrating that Endophilin A1 binds directly to gephyrin and GABAAR subunits, and identifying the subdomains of Endophilin A1 that contribute to this effect. Overall, the authors state that their study places Endophilin A1 as a new regulator of GABAergic synapse function.

Strengths:

Overall, the topic of this manuscript is very timely, since there has been substantial recent interest in describing the mechanisms governing inhibitory synaptic transmission at GABAergic synapses. The study will therefore be of interest to a wide audience of neuroscientists studying synaptic transmission and its role in disease. The manuscript is well written and contains a substantial quantity of data. In the revised version of the manuscript, the authors have increased the number of samples analyzed and have significantly improved the statistical analysis, thereby substantially strengthening the conclusions of their study.

Reviewer #2 (Public review):

Summary:

The function of neural circuits relies heavily on the balance of excitatory and inhibitory inputs. Particularly, inhibitory inputs are understudied when compared to their excitatory counterparts due to the diversity of inhibitory neurons, their synaptic molecular heterogeneity, and their elusive signature. Thus, insights into these aspects of inhibitory inputs can inform us largely on the functions of neural circuits and the brain.

Endophilin A1, an endocytic protein heavily expressed in neurons, has been implicated in numerous pre- and postsynaptic functions, however largely at excitatory synapses. Thus, whether this crucial protein plays any role in inhibitory synapse, and whether this regulates functions at the synaptic, circuit, or brain level remains to be determined.

The three remaining concerns are:

(1) The use of one-way ANOVA is not well justified.

(2) The use of superplots to show culture to culture variability would make it more transparent.

(3) Change EEN1 in Figure 8B to EndoA1.

Comments on revised version:

The authors addressed the concerns adequately.

Reviewer #3 (Public review):

Chen et al. identify endophilin A1 as a novel component of the inhibitory postsynaptic scaffold. Their data show impaired evoked inhibitory synaptic transmission in CA1 neurons of mice lacking endophilin A1, and an increased susceptibility to seizures. Endophilin can interact with the postsynaptic scaffold protein gephyrin and promotes assembly of the inhibitory postsynaptic element. Endophilin A1 is known to play a role in presynaptic terminals and in dendritic spines, but a role for endophilin A1 at inhibitory postsynaptic densities has not yet been described, providing a valuable addition to the field.

To investigate the role of endophilin A1 at inhibitory postsynapses, the authors used a broad array of experimental approaches, including tests of seizure susceptibility, electrophysiology, biochemistry, neuronal culture and image analysis. The authors have addressed the remaining concerns in their revision. Taken together, their results expand the synaptic role of endophilin-A1 to include the inhibitory post synaptic element.

Author response:

The following is the authors’ response to the previous reviews

Reviewer #2 (Recommendations for the authors):

Comments on revised version:

The authors addressed the concerns adequately. The three remaining concerns are:

(1) The use of one-way ANOVA is not well justified.

The statement about statistical test in “Statistical analysis” section is as follows in the revised manuscript, “Data sets were tested for normality and direct comparisons between two groups were made using two-tailed Student’s t test (t test, for normally distributed data) as indicated. To evaluate statistical significance of three or more groups of samples, one-way ANOVA analysis with a Tukey test was used or repeated measures ANOVA analysis with a Tukey test was used in behavior assays. Statistical parameters are reported in the figures and the corresponding legends”.

We used a one-way ANOVA for the data about one categorical independent variable and one quantitative dependent variable. The independent variable should have at least three different groups or categories. And we conducted repeated measures ANOVA analysis for the data about behavioral tests according to the suggestion by Reviewer #1 (Point 18) in revised manuscript.

(2) The use of superplots to show culture to culture variability would make it more transparent.

Thanks for the nice suggestion. While superplots could more transparently show culture to culture variability, it is difficult to add more colors or even shades to the scatterplots in the current form, which have already been color coded for multiple groups of samples. The scatterplots we used effectively illustrate the variability across all collected data and do not affect the conclusions of our study. Therefore, we prefer not to change the way of data presentation in the revised manuscript.

(3) Change EEN1 in Figure 8B to EndoA1.

Thanks a lot for the sharp eye. Corrected.

Reviewer #3 (Recommendations for the authors):

Specific comments:

The authors have made a substantial effort to improve their manuscript. A number of issues, related to numbers of observations mentioned by the reviewers, are clarified in the revised manuscript. The authors have also clarified some of the other questions from the reviewers. The long list of issues brought up by the reviewers and the many corrections needed still raise questions about data quality in this manuscript.

In response to my comments (Point 2), the added experiment with PSD95.FingR and GPN.FingR in cultured neurons (Fig. S5A-D) is a good addition; the in vivo data using FingRs in Figure S3 look less convincing however. In response to my Point 5, the authors have added a cell-free binding assay (Figure 5I). This is a useful addition, but to convincingly make the point of interaction between Gephyrin and EndoA1, more rigorous biophysical quantitation of binding is needed. The legend in Figure 5I states that 4 independent experiments were performed, but the graph only shows 3 dots. This needs to be corrected.

We sincerely appreciate your comments and apologize for any concerns raised. As suggested (Point 2), we made many efforts to visualize endogenous postsynaptic proteins using recombinant probes. However, due to much lower expression of GPN.FingR compared with PSD95.FingR in P21 brain slices following viral infection (Figure S3), we were unable to obtain better imaging results. To strengthen our data and conclusions, we additionally performed experiments with PSD95.FingR and GPN.FingR in cultured neurons (Fig. S5A-D) in the revised manuscript.

Regarding the biophysical quantification of gephyrin–endophilin A1 binding, we do not have the equipment for this type of experiment (surface plasmon resonance or isothermal titration calorimetry). Instead, we performed a pull-down assay as an alternative to confirm their interaction (Figure 5I). We also apologize for the error in the number of independent experiments stated in the figure legend and have corrected it in the revised manuscript.

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