In the Stage 2 ms the authors present the results of the study, following the preregistered protocol in every detail and clarifying the few occasions in which they have departed from the initial plan and why. The interpretation of the results does not go beyond what the preregistered analyses permit. Therefore, in my humble opinion, the paper could be accepted essentially as is. I only have a small number of recommendations that the authors might want to consider, although they shouldn’t feel obliged to include them in the final version of the manuscript.

I have the feeling that the authors fail to acknowledge the added value of pre-registration in their study. In the general discussion, they point out that based on previous research they expected gamification to have a greater impact. But how many of those previous studies were pre-registered and followed a registered report format? Plenty of research shows that RRs are far less biased and non-registered studies. Is it possible that previous research on gamification suffers from bias and therefore the reported effect sizes are inflated to an unknown extent? Even in the literature on response inhibition training, there is some evidence that, once corrected for publication bias, the average power could be substantially lower than .50, suggesting that the actual effect sizes are lower than anticipated by researchers in their power analyses (see https://onlinelibrary.wiley.com/doi/10.1111/obr.13338).

The effect of the manipulation on weight loss is analyzed, but no descriptive information is provided, possibly because this analysis was not pre-registered. But this information can be useful in many different ways (e.g., for future meta-analyses). I’d encourage the authors to report the descriptives of weight loss either in a table or a figure.

In the analysis of RQ4 it is perhaps worth noting that the SESOI entered in the power analysis was relatively large. The conclusion that the effects of both manipulation are identical relies on the assumption that effect sizes below d = 0.46 are too small to matter.

Figured 4 is not referenced in the main text.

From the previous round of review

• The authors have done a good job of replying to my comments. My only remaining thought is that, while I agree with the authors that measures of implicit associations are often difficult to change and can be frustrating, I would still recommend noting that they were not directly assessed in the discussion section of the manuscript when this comes around. It would be an interesting direction for future research. This might be particularly relevant where discussing that participants might not be aware of the n-go associations they learned and thus have not reported differences on self-reported measures.
• The authors have now dropped the bayesian statistics which is fine. But I beleive there was also mention of lmer in the original version? Was this also dropped?
• Minor comment but the tables are a little messy and not formatted per APA or similar.
• Violin plots add very little for me, as they seem very consistant with the numerical resutls. Consider moving these to a supplement to keep the manuscript streamlined.
• How meeting parametric assumptions, was this tested formally using shapro wilk or similar? or just by inspection of figures? Either is fine with me but I think it warrents mentioning. 
• I would like to see more on the argument for single vs. multiple gamified elements to highlight why this research is needed in the discussion (e.g., it is briefly touched on page 29). For me, if multiple gamified elements typically produce big effects, but single ones here only produce small effects, it leaves a big open question about how the multiple gamified elements stack. Is it a cumultative or interactive effect etc. A larger scale study with more combinations of gamified effects would be something very interesting to suggest for future research.