I extend my appreciation to the authors for their receptive approach to the suggestions provided. Overall, the authors have made substantial improvements to the paper, resulting in a notably enhanced manuscript.

Here are several observations I made while reading the revision of this manuscript:

1. Introduction Clarity:

The introduction section contains several areas that could benefit from further clarity. It would be advisable to take out any reference to cognitive processes, as the primary focus appears to be on evaluating effectiveness rather than delving into cognitive explanations.

Specific points of concern include:

Page 2, paragraph 1: The statement, "Interestingly, recent evidence indicates that the practice of tasks involving the execution or inhibition of motor responses to food cues modulates their self-reported value, and their consumption," could be nuanced to indicate that the evidence suggests these practices can modulate these variables. In general, it is best to avoid making strong claims or clearly outline evidence supporting such claims in the event that there would be strong enough evidence.

Page 2, paragraph 2: “The repeated inhibition of motor response to unhealthy cues is thought to reduce their reward value to solve the conflict between the task demand for response withholding and their tendency to respond to palatable cues”. This sentence is very complex and it is not well explained (what is this "reward value" or this "tendency"). It would also be crucial to specify the source of these theoretical explanations as there are many theoretical explanations of observed effects. It might be better if the authors omit this sentence and instead of talking about these cognitive explanations simply explain the procedure and the findings more. The same holds for the next paragraph on the cue-approach-task.

The fourth paragraph is relevant as it goes into evidence of effectiveness. However, the next paragraph again goes into the cognitive processes (making some strong claims without presenting evidence and without explaining the cognitive constructs well). Consider omitting paragraph 4 as this would streamline the introduction and allow it to flow more smoothly into the next paragraph, which is well-written and clear.

Page 3: There is again a strong claim, this time the claim is that adherence to a restrictive diet is valuable due to it being easier to report and less biased. This claim requires substantiation with references or additional context or should be omitted.

2. Sampling Plan and Effect Size:

The section regarding the sampling plan raises questions about the choice of stringent cutoff values for effect sizes. For instance, the authors note: "any smaller effect than r =.4 will not be interpreted as relevant even if significant.” This seems very arbitrary. Why would there be such an important difference between  an effect of r=0.40 versus r =0.39. It's important to consider that researchers are increasingly avoiding strong cut-off points and instead reporting all values clearly (every piece of evidence is relevant), allowing readers to assess the findings in a nuanced manner.

Authors note that “For H2 and H3, which only consider the experimental group, the smallest effect size of interest was estimated to be small (r = 0.4) based on clinical subjectivity”. I’m not sure what they mean with clinical subjectivity. Additionally, it's worth noting that "r = 0.4" is generally considered a moderate to large effect size, rather than a small one, which should be accurately reflected.

3. Demand Compliance Measure:

I also still wonder why the authors did not include a demand compliance measure. The authors note in their response to the suggestion to include this measure: “Concerning the demand compliance question, the experimental group should not have a larger response bias than the control group. Contrasting experimental vs. control should thus isolate any effect of this potential bias.” I’m not sure if the authors have data to support this claim. It seems there is contrasting evidence that, in the experimental group, participants are often much more likely to figure out the purpose of the training and are more likely to become demand aware and give demand compliant answers (and sometimes reactant answers as well). 

The authors have replied to all my comments in a satisfactory manner. There remains, however, one point to be clarified, as I keep thinking about the personalized item set: what happens if a participant reports drinking less than eight of the drinks at a value above 0? Will a random selection of zero-value items be included in the training? I might be worrying about this too much as I don’t have experience studying sugary drinks consumption, so maybe the authors could clarify this point. Relatedly, will the study be advertised as relating to the reduction of sugary drinks consumption? That, of course, would lead to a selective sample in which consumption is probably rather common.

Apart from this, I have no further points and wish the authors best of luck with their study.

Review for Stage 1 RR: 

“Sugary drinks devaluation with executive control training helps to resist to their consumption”

Sampling plan

If 50 participants are needed in the experimental group for H2 and H3 why is the target sample size based on H1 which requires a smaller number of participants in each group (N= 36)? Also, I would be more inclined to use a d of 0.4 for the power analysis and not the chosen mean/sd differences that result in a Cohen’s d of 0.7, as in the rest of the manuscript you mention a d of 0.4 as your benchmark (smallest effect size of interest). In any case please make this clearer as reading this the first time I thought that the 7-day difference resulted in a d of 0.4. If you apply this change, your total sample size would be 216. A greater sample size may also allow for more power for H2 and H3 analyses (under 50 participants in the experimental group - which will further be reduced if you apply data exclusions as per my comment for the Pre-post explicit liking reduction section).

Recruitment and screening

As an inclusion criterion, willingness to follow a restrictive diet is important but it is also worth recording participants’ baseline consumption behaviour. Are you including everyone from people who rarely drink sugary drinks to people who drink more than a few sodas a day? In this section it is important to also add any methodological details or at least point to where the reader can access them (what are the exact questions for your screening- e.g. how do you define ‘healthy’ individuals in this context). 

Training tasks

I understand that the tasks have been used in previous studies but for this Registered Report I think you should not omit the methodological details and specific parameters of the tasks being administered (contingencies, time limits, number of trials, feedback element etc.). They are central to the study and should be presented as part of the Stage 1 proposal for further evaluation - even if the app cannot be changed at this time. The video for the app demonstration was really helpful - you could add a figure with screenshots from the game in the main text for convenience as well. 

Questionnaires

Please add a reference to supplementary material or an online repository where the full questionnaires can be found. In the text  you can add more details about the 10 items being included in the health questionnaire - what are you measuring with regards to participants’ health?  

Analysis plan

In this section  you need to specify all the analyses that will be run and treated as ‘confirmatory’ with details so you can move the paragraphs from the Statistical contrasts section here. For Bayesian analyses, what priors will you be using for the t-test and correlations? Also, while BFs can be very informative in the case of inconclusive results it would be preferable in my opinion to report them for all results irrespective of significance.  Also, although it may seem obvious please state on which statistics you will base your conclusions on (e.g. frequentist but BFs reported in a supplementary manner?). 

Data exclusions

Could you add details here about potential missing data and related exclusions with regards to your questionnaires? For example, what if participants don’t complete the weekly questionnaires, or if information is missing (e.g. exact dates of first consumption etc.)?

Given that reaction times from the analogue scales are recorded I presume that you can also have access to training performance data. While technically a day of training can be counted as successful if completed, I believe you should mention whether potential exclusions can apply to adherence. For example, does training proceed if you miss the reaction time window (if there is one, not currently known based on the details presented) or if participants simply skip trials and not interact with the game? 

Since the proportion of successful inhibitions in such training tasks may be a moderator of training effects (see meta-analysis by Jones et al. 2016), it is worth considering a performance benchmark for data exclusions - e.g. if one day of training is completed but participants fail to stop for more than half of the trials. As this may be a conservative criterion for data exclusions given the sample size you propose, it would be interesting to add training performance as a secondary outcome or consider certain exploratory analyses at Stage 2 to look at learning effects and inhibition success.

Statistical contrasts

Please state why have you chosen this criterion for your effect interpretation - i.e. why is a min d of 0.4 required to consider the result ‘relevant’ - I have found this confusing as mentioned in the Sampling plan. You mention that the result will only be relevant if the difference is at least 7 days or more of successful dieting, but in your power analysis this corresponds to a Cohen's d of 0.7 and yet in the text a Cohen’s d ≥ 0.4 is treated as relevant. 

Baseline reported consumption

If I understood this correctly, will you inspect the data, run the analyses and if for H1 you get a Cohen’s d greater than 0.4 you will exclude participants and report the results with the reduced sample size? For other data exclusions that do not require statistical analyses I assume that recruitment will continue until the sample size target is met, but for this exclusion criterion please add more details regarding the sampling plan - that is, how your sample size may be affected given that the target is based on an a priori power analysis. 

Pre-post explicit liking reduction

Please add a justification for this in a narrative format - e.g. for H2 you only want to run the correlations if a devaluation effect is observed (defined by your chosen threshold) - this should be clear in your hypotheses as well. It may be good to present results without all the effect-related exclusions in the supplementary material as well for comparison.

Review for “Sugary drinks devaluation with executive control training helps to resist to their consumption”

In the Stage 1 report “Sugary drinks devaluation with executive control training helps to resist to their consumption”, the authors lay out a randomized controlled trial that tests an app-based cognitive control training against an active, “sham-training” control group in its effectiveness to reduce evaluations and intake of sugar-sweetened beverages. Further, the authors aim to investigate the relation between devaluation and consumption effects as well as a dose-response effect between the amount of conducted training and consumption. The planned study is generally well-designed and tackles worthwhile questions in the field. I have some thoughts and suggestions that I hope would improve the study and its possible interpretations. Please note that this is the first time I am reviewing a Stage 1 report (which I’m quite excited about!), so please bear with me for any possible “breach of protocol”.

I was somewhat unclear about one of the proposed intervention tasks. The description of the ABM task in the introduction did, in my view, not fit an attentional bias modification. Looking at the video of the task in the OSF folder, the ABM task looks more like a mix between Approach-Avoidance Task,  GNG, and Cue approach task, which might actually work quite well, see van Alebeek, Veling, and Blechert (2023) (https://www.sciencedirect.com/science/article/pii/S0950329323000150). In past papers, the same authors have also termed this "Cue approach training". Why do the authors frame this as an attention modification paradigm here? I fail to see how it modifies attentional biases as it requires attention allocation to both approach and withhold items.

The authors include an active “sham-training” control condition (which I think is great) to control for confounding factors of expectations and cue exposure. This is surely a good idea but in addition, the authors could also include a measure of expectations (for example as we have done in an ongoing study of our own group: https://bmjopen.bmj.com/content/13/4/e070443.abstract). If expectations play a crucial role (and there is evidence that suggests that they might), we should then see an effect of expectations across both groups in the study. I see that this is a tangent to the current study’s goals but might still be interesting to consider.

I must admit that I never fully grasped what exactly the dependent variable for H1 is. Is it the number of days until the first consumption of trained drinks? Or the total number of trained drinks consumed during the follow-up period? I was thinking that the best outcome measure would be the amount of drink consumed: arguably, this is easier to report than foods because of fixed common serving sizes. Such a consumption measure would be much more sensitive to change than cruder measures.

Regarding H2: will this relation be calculated across groups? One might argue that we would only expect this effect in the intervention group because changes in the control group should be rather random. If you only use data from the intervention group, the sample size calculation does not add up because you would need 50 participants in the intervention group alone.

Regarding H3: to really speak of a dose-response effect, one would need to assign dosage experimentally, as done in Moore, White, Finalyson, and King (2022) (https://www.sciencedirect.com/science/article/pii/S0195666322002720?casa_token=N-C479gEscQAAAAA:wAz8DeDD_lzReFYBdfACTmcNnfIXdlc_7q_x5PunfGXmcB-j7slBgnh0QfF40afP0RTKdUuCgQ). With the current design, we would probably mainly see an effect of motivation on both training use and consumption. We discussed this in some detail in our paper after having been told off by a reviewer for using the term “dose-response relationship” (see Aulbach et al., 2021; https://www.sciencedirect.com/science/article/pii/S0195666321002221). Maybe this could be taken into account by adding a measure of motivation and controlling for it in the analysis but it still does not solve the problem of self-selection. Relatedly: will the analysis for H3 be conducted across groups? If yes, adding group as a moderator in a regression could show whether this “descriptive dose-response effect” differs between groups. That (especially when combined with expectancies) would be very interesting: if more training produces larger effects but only in the intervention group while expectations are similar between groups that would be quite strong evidence for the intervention.
Another aspect that limits this analysis is that the distribution is truncated at 7 and 14: there will be no participant with less than 7 or more than 14 sessions which severely limits interpretability of any found (or non-significant) effect.

Specific methods points:

-        What is the rationale for the age range of included participants?

-        20 minutes of intervention per day seems like a lot. What kind of dropout rates do you expect, especially given that you want to exclude anyone with less than seven sessions?

-        Will excluded participants be replaced or will the analysis be conducted with what you have after exclusions? If it is the latter: how will that affect statistical power at different exclusion rates?

-        Participants receive 8 sugary drinks for reduction. That seems like a lot of different drinks! I would consider lowering this number, as otherwise drinks will need to be included that are not drunk very often in the first place.

-        Relatedly, the consumption frequency question has a very subjective scale. Why not ask e.g. “On how many days during the last month have you drank this?” Otherwise, participants will scale the responses to their own standards: For person A, "often" might mean once a week, for person B it might mean several portions a day. 

-        I’m not sure if the liking measure is ideal to measure what is of key interest. With the current wording, it seems very context-dependent: I might like cola on a hot afternoon but imagining drinking it in the morning, I would not like it. From the introduction I read that the main interest is relatively stable preferences. If you measure a very variable momentary preference, you will get a lot of noise in your measure and might not measure so much what you care about.

In the analysis plan section, there is mention of “deltas” – I assume those are pre-post changes? Please clarify.

Regarding the compensatory strategies: I would find it interesting to see if the intervention group engaged more in those because it would suggest that the training works for the specific trained foods but does not generalize to similar items.

The authors write that a pre-post reduction of explicit liking is necessary for investigating H2. I do not think this is necessary: you would just correlate one distribution with another (liking – consumption) and it should be irrelevant where on the scale this correlation occurs/where these distributions are on the scale.  

In summary, I think that this study will produce very interesting evidence on the effects of mobile cognitive bias modification. I hope that the authors find my comments and suggestions helpful to further improve the study. I’m aware I referred to some of my own and my colleagues’ papers which is somewhat frowned upon in peer review. By no means do I insist they be cited in any publications, I only included those because I know those best and found them helpful pointers for the issues at hand.

Thank you for giving me the opportunity for this stage 1 review and possibly contributing to making this study even better.

In this registered report, the authors aim to investigate the impact of a combination of Go/No Go training and approach bias training on participants' consumption of their favorite sugary drinks. The study addresses an important and relevant topic, as the exploration of online training methods to improve unhealthy consumption patterns holds practical and theoretical significance. The authors are commendable for their commitment to good scientific practices by conducting this study as a registered report.

However, while reading the paper, I identified several areas where the authors could enhance the quality of their work. Primarily, the introduction falls short of the expected standards. It contains inaccuracies and lacks clarity regarding the constructs under investigation. It is crucial for the authors to be more precise when describing the behavior of interest, clearly distinguishing between observed behavior and the explanation of behavior in terms of mental processes. For instance, in the first sentence of the abstract there are already several inaccuracies: “Food executive control training has been shown to reduce the perceived value of palatable food items”. The authors mention a reduction in the perceived value of palatable food items, but since the participants' perception is not directly probed, it would be more accurate to refer to it as self-reported value. Furthermore, instead of using the term "executive control training," which implies training of the mental construct 'cognitive control,' a construct that cannot be directly observed, it would be better to consistently refer to the specific tasks employed, such as the go/no go training task and the attention bias modification task (and please make a note there as well that this task does not directly modify attentional bias, it merely targets this bias). I recommend that the authors critically review all the constructs discussed in the paper, ensuring accurate definitions and clear differentiation between behavioral effects and mental constructs.

Similarly, it is essential to avoid making inaccurate claims. For example in the second paragraph of the introduction, the authors state that conventional reflective approaches to reduce overconsumption behaviors usually fail because they target conscious processes, while (palatable) food consumption is largely driven by environmental cues. However, this represents only one explanation of findings and it should not be presented as if it is a truism. Additionally, in the next sentence, the authors claim that recent evidence indicates automatic motivational processes driving unhealthy overconsumption can be modulated by executive control training (ECT), with ECT robustly reducing the perceived value of targeted cues in the eating domain. These claims are not accurate and the sentences would better be discussed in reversed order. First, highlight evidence that specific types of training can reduce self-reported value. Then indicate that this reduction has been explained as potentially targeting automatic motivational processes driving unhealthy consumption (while noting other explanations as well). It is crucial to avoid oversimplifying the literature. In this sense, it is also worth noting that training effects are often limited, and there is little evidence supporting real-life effects of cognitive bias modification, except perhaps in the context of alcohol approach bias modification for alcoholic patients. It is essential to address this omission and discuss relevant work in the field.

Moving on to more minor issues within the paper:

-          The explanation of the sample size rationale lacks clarity, as the authors consistently fail to state the effect of interest for the t-test as Cohen's d. Additionally, it is unclear why only an effect of 7 days would be of interest, considering that finding such an effect appears highly unlikely. Moreover, with 36 participants per group, the sample size seems relatively small, which raises concerns about the informativeness of the results. Further explanation is needed to address these concerns adequately.

-          It would be beneficial to report Bayesian factors for significant results in addition to other statistical measures.

-          The paper states that adherence to a restrictive diet constitutes a robust and valuable dependent variable to assess the real-world effect of food ECT, as it is not biased by memory or the relationship with the experimenter. It would be helpful to explain the basis for this claim. Why would there not be a bias by “memory”. Isn’t there always a bias by a broad cognitive construct like memory? Additionally, it is important to note that experimenter demand still presents a possible explanation of any effect that may be observed. Including a demand compliance question at the end could provide more information about the possibility of participants in the experimental group conforming to the hypothesis and falsely indicating that they did not consume the sugary drink.

-          More background information is required to understand the rationale behind combining Go/No Go (GNG) and Attentional Bias Modification (ABM) training. The authors should provide a clearer explanation and reference their previous studies that employed this combination. It is crucial to highlight the added value of this research compared to their prior work.

-          The statement, "This contrast will allow us to control for the confounding factors of cue exposure and of expectations developed by the participants on the effects of the intervention," raises questions about expectations as a confound. The authors should clarify why expectations would not drive the effects as in fact, I think expectation may always drive any behavior effect. Additionally, it is evident that the control group does not control for expectations. 100% and 50% contingencies are typically noticed very well by participants (and in fact this awareness seems crucial for effects) and lead to different inferences (including causal inferences or predictions). 

-          H3) should be rephrased. The current phrasing suggests that the more participants train, the larger the effect of the intervention will be on their dieting behavior. However, if an effect is found, it does not necessarily imply that the intervention caused it. An alternative explanation could be that participants who train more are more motivated to stop drinking sugary drinks and thus exhibit reduced consumption.

-          Including the compensatory strategy in an ANOVA to determine its role in explaining the observed effects would be beneficial and should be considered.

By addressing these concerns and incorporating the suggested improvements, the authors can significantly enhance the quality and clarity of their paper, making it a valuable contribution to the research community.