Author response:
The following is the authors’ response to the original reviews
eLife Assessment
This study provides a valuable contribution to understanding how negative affect influences food-choice decision making in bulimia nervosa, using a mechanistic approach with a drift diffusion model (DDM) to examine the weighting of tastiness and healthiness attributes. The solid evidence is supported by a robust crossover design and rigorous statistical methods, although concerns about low trial counts, possible overfitting, and the absence of temporally aligned binge-eating measures limit the strength of causal claims. Addressing modeling transparency, sample size limitations, and the specificity of mood induction effects, would enhance the study's impact and generalizability to broader populations.
We thank the Editor and Reviewers for their summary of the strengths of our study, and for their thoughtful review and feedback on our manuscript. We apologize for the confusion in how we described the multiple steps performed to ensure that the hierarchical model reported in the main text was the best fit for the data but was not overfitted. Regarding “model transparency,” as described in our response to Reviewer 1 below, we have now more clearly explained (with references) that the use of hierarchical estimation procedures allows for information sharing across participants, which improves the reliability and stability of parameter estimates—even when the number of trials per individual is small. We have clarified for the less familiar reader how our Bayesian model selection criterion penalizes models with more parameters (e.g., more complex models).
Details about model diagnostics, recoverability, and posterior predictive checks are all provided in the Supplementary Materials. We have clarified how these steps ensure that the parameters we estimate are identifiable and interpretable, while confirming that the model can reproduce key patterns in the data, ultimately supporting the validity of the winning model. Additionally, we have provided all scripts for estimating the models by linking to our public Github repository. Furthermore, we have edited language throughout to eliminate any implication of causal claims and acknowledged the limitation of the small sample size. Given these efforts, we are concerned that the current wording about “modeling transparency” in the public eLife Assessment may inadvertently misrepresent the modeling practices in our paper. Would it be possible to revise or remove that particular phrase to better reflect the steps we have taken? We believe this would help avoid confusion for readers.
We have also taken additional steps to ensure that we have used “appropriate and validated methodology in line with current state-of-the-art," and we have added references to recent papers supporting our approaches.
All changes in the revised text are marked in blue.
Public Reviews:
Reviewer #1 (Public review):
Summary:
Using a computational modeling approach based on the drift diffusion model (DDM) introduced by Ratcliff and McKoon in 2008, the article by Shevlin and colleagues investigates whether there are differences between neutral and negative emotional states in:
(1) The timings of the integration in food choices of the perceived healthiness and tastiness of food options between individuals with bulimia nervosa (BN) and healthy participants.
(2) The weighting of the perceived healthiness and tastiness of these options.
Strengths:
By looking at the mechanistic part of the decision process, the approach has the potential to improve the understanding of pathological food choices. The article is based on secondary research data.
Weaknesses:
I have two major concerns and a major improvement point.
The major concerns deal with the reliability of the results of the DDM (first two sections of the Results, pages 6 and 7), which are central to the manuscript, and the consistency of the results with regards to the identification of mechanisms related to binge eating in BN patients (i.e. last section of the results, page 7).
(1) Ratcliff and McKoon in 2008 used tasks involving around 1000 trials per participant. The Chen et al. experiment the authors refer to involves around 400 trials per participant. On the other hand, Shevlin and colleagues ask each participant to make two sets of 42 choices with two times fewer participants than in the Chen et al. experiment. Shevlin and colleagues also fit a DDM with additional parameters (e.g. a drift rate that varies according to subjective rating of the options) as compared to the initial version of Ratcliff and McKoon. With regards to the number of parameters estimated in the DDM within each group of participants and each emotional condition, the 5- to 10-fold ratio in the number of trials between the Shevlin and colleagues' experiment and the experiments they refer to (Ratcliff and McKoon, 2008; Chen et al. 2022) raises serious concerns about a potential overfitting of the data by the DDM. This point is not highlighted in the Discussion. Robustness and sensitivity analyses are critical in this case.
We thank the Reviewer for their thoughtful critique. We agree that a limited number of trials can impede reliable estimation, which we acknowledge in the Discussion section. However, we used a hierarchical estimation approach which leverages group information to constrain individual-level estimates. This use of group-level parameters to inform individual-level estimates reduces overfitting and noise that can arise when trial counts are low, and the regularization inherent in hierarchical fitting prevents extreme parameter estimates that could arise from noisy or limited data (Rouder & Lu, 2005). As a result, hierarchical estimation has been repeatedly shown to work well in settings with low trial counts, including as few as 40 trials per condition (Lerche et al., 2017; Ratcliff & Childers, 2015; Wiecki et al., 2013). In addition, previous applications of the time-varying DDM to food choice task data has included experiments with as few as 60 trials per condition (Maier et al., 2020). We have added references to these more recent approaches and specifically note their advantages for the modeling of tasks with fewer trials. Finally, our successful parameter recovery described in the Supplementary Materials supports the robustness of the estimation procedure and the reliability of our results.
The authors compare different DDMs to show that the DDM they used to report statistical results in the main text is the best according to the WAIC criterion. This may be viewed as a robustness analysis. However, the other DDM models (i.e. M0, M1, M2 in the supplementary materials) they used to make the comparison have fewer parameters to estimate than the one they used in the main text. Fits are usually expected to follow the rule that the more there are parameters to estimate in a model, the better it fits the data. Additionally, a quick plot of the data in supplementary table S12 (i.e. WAIC as a function of the number of parameters varying by food type in the model - i.e. 0 for M0, 2 for M1, 1 for M2 and 3 for M3) suggests that models M1 and potentially M2 may be also suitable: there is a break in the improvement of WAIC between model M0 and the three other models. I would thus suggest checking how the results reported in the main text differ when using models M1 and M2 instead of M3 (for the taste and health weights when comparing M3 with M1, for τS when comparing M3 with M2). If the differences are important, the results currently reported in the main text are not very reliable.
We thank the Reviewer for highlighting that it would be helpful to explicitly note that we specifically selected WAIC as one of two methods to assess model fit because it penalizes for model complexity. We now explicitly state that, in addition to being more robust than other metrics like AIC or BIC when comparing hierarchical Bayesian models like those in the current study, model fit metrics like WAIC penalize for model complexity based on the number of parameters (Watanabe, 2010). Therefore, more complex models (i.e., those with more parameters) do not automatically have lower WAIC. Additionally, we now more clearly note that our second method to assess model fit, posterior predictive checks, demonstrate that only model M3 can reproduce key behavioral patterns present in the empirical data. As described in the Supplementary Materials, M1 and M2 miss key patterns in the data. In summary, we used best practices to assess model fit and reliability (Wilson & Collins, 2019): results from the WAIC comparison (which penalizes models with more parameters) and results from posterior predictive checks align in showing that M3 provided the best fit to our data. We have added a sentence to the manuscript to state this explicitly.
(2) The second main concern deals with the association reported between the DDM parameters and binge eating episodes (i.e. last paragraph of the results section, page 7). The authors claim that the DDM parameters "predict" binge eating episodes (in the Abstract among other places) while the binge eating frequency does not seem to have been collected prospectively. Besides this methodological issue, the interpretation of this association is exaggerated: during the task, BN patients did not make binge-related food choices in the negative emotional state. Therefore, it is impossible to draw clear conclusions about binge eating, as other explanations seem equally plausible. For example, the results the authors report with the DDM may be a marker of a strategy of the patients to cope with food tastiness in order to make restrictive-like food choices. A comparison of the authors' results with restrictive AN patients would be of interest. Moreover, correlating results of a nearly instantaneous behavior (i.e. a couple of minutes to perform the task with the 42 food choices) with an observation made over several months (i.e. binge eating frequency collected over three months) is questionable: the negative emotional state of patients varies across the day without systematically leading patients to engage in a binge eating episode in such states.
I would suggest in such an experiment to collect the binge craving elicited by each food and the overall binge craving of patients immediately before and after the task. Correlating the DDM results with these ratings would provide more compelling results. Without these data, I would suggest removing the last paragraph of the Results.
We thank the Reviewer for these interesting and important suggestions, and we agree that claims about causal connections between our decision parameters and symptom severity metrics would be inappropriate. Per the Reviewer’s suggestions, we have eliminated the use of the word “predict” to describe the tested association with symptom metrics. We also agree that more time-locked associations with craving ratings and near-instantaneous behavior would be useful, and we have added this as an important direction for future research in the discussion. However, associating task-based behavior with validated self-report measures that assess symptom severity over long periods of time that precede the task visit (e.g., over the past 2 weeks in depression, over the past month in eating disorders) is common practice in computational psychiatry, psychiatric neuroimaging, and clinical cognitive neuroscience (Hauser et al., 2022; Huys et al., 2021; Wise et al., 2023), and this approach has been used several times specifically with food choice tasks (Dalton et al., 2020; Steinglass et al., 2015). We have revised the language throughout the manuscript to clarify: the results suggest that individuals whose task behavior is more reactive to negative affect tend to be the most symptomatic, but the results do not allow us to determine whether this reactivity causes the symptoms.
In response to this Reviewer’s important point about negative affect not always producing loss-of-control eating in individuals with BN, we now explicitly note that while several studies employing ecological momentary assessments (EMA) have repeatedly shown that increases in negative affect significantly increase the likelihood of subsequent loss-of-control eating (Alpers & Tuschen-Caffier, 2001; Berg et al., 2013; Haedt-Matt & Keel, 2011; Hilbert & Tuschen-Caffier, 2007; Smyth et al., 2007), not all loss-of-control eating occurs in the context of negative affect. We further note that future studies should integrate food choice task data pre and post-affect inductions with measures capturing the specific frequency of loss of control eating episodes that occur during states of high negative affect.
(3) My major improvement point is to tone down as much as possible any claim of a link with binge eating across the entire manuscript and to focus more on the restrictive behavior of BN patients in between binge eating episodes (see my second major concern about the methods). Additionally, since this article is a secondary research paper and since some of the authors have already used the task with AN patients, if possible I would run the same analyses with AN patients to test whether there are differences between AN (provided they were of the restrictive subtype) and BN.
We appreciate the Reviewer’s very helpful suggestions. We have adjusted our language linking loss-of-control eating frequency with decision parameters, and we have added sentences focusing on the implications for the restrictive behavior of patients with BN between binge eating episodes. In the Supplementary Materials, we have added an analysis of the restraint subscale of the EDE-Q and confirmed no relationship with parameters of interest. While we agree additional analyses with AN patients would be of interest, this is outside the scope of the paper. Our team have collected data from individuals with AN using this task, but not with any affect induction or measure of affect. Therefore, we have added this important direction for future research to the discussion.
Reviewer #2 (Public review):
Summary:
Binge eating is often preceded by heightened negative affect, but the specific processes underlying this link are not well understood. The purpose of this manuscript was to examine whether affect state (neutral or negative mood) impacts food choice decision-making processes that may increase the likelihood of binge eating in individuals with bulimia nervosa (BN). The researchers used a randomized crossover design in women with BN (n=25) and controls (n=21), in which participants underwent a negative or neutral mood induction prior to completing a food-choice task. The researchers found that despite no differences in food choices in the negative and neutral conditions, women with BN demonstrated a stronger bias toward considering the 'tastiness' before the 'healthiness' of the food after the negative mood induction.
Strengths:
The topic is important and clinically relevant and methods are sound. The use of computational modeling to understand nuances in decision-making processes and how that might relate to eating disorder symptom severity is a strength of the study.
Weaknesses:
The sample size was relatively small and may have been underpowered to find differences in outcomes (i.e., food choice behaviors). Participants were all women with BN, which limits the generalizability of findings to the larger population of individuals who engage in binge eating. It is likely that the negative affect manipulation was weak and may not have been potent enough to change behavior. Moreover, it is unclear how long the negative affect persisted during the actual task. It is possible that any increases in negative affect would have dissipated by the time participants were engaged in the decision-making task.
We thank the Reviewer for their comments on the strengths of the paper, and for highlighting these important considerations regarding the sample demographics and the negative affect induction. As in the original paper that focused only on ultimate food choice behaviors, we now specifically acknowledge that the study was only powered to detect small to medium group differences in the effect of negative emotion on these final choice behaviors.
Regarding the sample demographics, we agree that the study’s inclusion of only female participants is a limitation. Although the original decision for this sampling strategy was informed by data suggesting that bulimia nervosa is roughly six times more prevalent among females than males (Udo & Grilo, 2018), we now note in the discussion that our female-only sample limits the generalizability of the findings.
We also agree with the Reviewer’s noted limitations of the negative mood induction, and based on the reviewer’s suggestions, we have expanded our original description of these limitations in the Discussion. Specifically, we now note that although the task was completed immediately after the affect induction, the study did not include intermittent mood assessments throughout the choice task, so it is unclear how long the negative affect persisted during the actual task.
Reviewer #3 (Public review):
Summary:
The study uses the food choice task, a well-established method in eating disorder research, particularly in anorexia nervosa. However, it introduces a novel analytical approach - the diffusion decision model - to deconstruct food choices and assess the influence of negative affect on how and when tastiness and healthiness are considered in decision-making among individuals with bulimia nervosa and healthy controls.
Strengths:
The introduction provides a comprehensive review of the literature, and the study design appears robust. It incorporates separate sessions for neutral and negative affect conditions and counterbalances tastiness and healthiness ratings. The statistical methods are rigorous, employing multiple testing corrections.
A key finding - that negative affect induction biases individuals with bulimia nervosa toward prioritizing tastiness over healthiness - offers an intriguing perspective on how negative affect may drive binge eating behaviors.
Weaknesses:
A notable limitation is the absence of a sample size calculation, which, combined with the relatively small sample, may have contributed to null findings. Additionally, while the affect induction method is validated, it is less effective than alternatives such as image or film-based stimuli (Dana et al., 2020), potentially influencing the results.
We agree that the limited sample size and specific affect induction method may have contributed to the null model-agnostic behavioral findings. Based on this Reviewer’s and Reviewer 2’s comments, we have added these factors to our acknowledgements of limitations in the discussion.
Another concern is the lack of clarity regarding which specific negative emotions were elicited. This is crucial, as research suggests that certain emotions, such as guilt, are more strongly linked to binge eating than others. Furthermore, recent studies indicate that negative affect can lead to both restriction and binge eating, depending on factors like negative urgency and craving (Leenaerts et al., 2023; Wonderlich et al., 2024). The study does not address this, though it could explain why, despite the observed bias toward tastiness, negative affect did not significantly impact food choices.
We thank the Reviewer for raising these important points and possibilities. In the Supplementary Materials, we have added an additional analysis of the specific POMS subscales that comprise the total negative affect calculation that was reported in the original paper (Gianini et al., 2019). We also report total negative affect scores from the POMS in the main text. Ultimately, we found that, across both groups, the negative affect induction increased responses related to anger, confusion, depression, and tension while reducing vigor.
We agree with the Reviewer that factors like negative urgency and cravings are relevant here. The study did not collect any measures of craving, and in response to Reviewer 1 and this Reviewer, we now note in the discussion that replication studies including momentary craving assessments will be important. While we do not have any measurements of cravings, we did measure negative urgency. The original paper (Gianini et al., 2019) did not find that negative urgency was related to restrictive food choices. We have now repeated those analyses, and we also were unable to find any meaningful patterns related to negative urgency. Nonetheless, we have added an analysis of negative urgency scores and decision parameters to the Supplementary Materials.
Recommendations for the authors:
Reviewer #1 (Recommendations for the authors):
Please improve the description of the computational methods: the fit of the DDM, the difference between the models used in the DDM, and the difference between the DDM model and the models used in the linear mixed models (the word "model" is at the end confusing as it may refer either to the DDM or to the statistical analysis of the DDM parameters).
We thank the Reviewer for highlighting the unclear language. We have updated the main text to clarify when the term “model” refers to the DDM itself versus the regression models assessing DDM parameters. As described above, we have clarified that both tests of model fit (WAIC and posterior predictive checks) suggest that Model 3 was the best fit to the data. We have also clarified the differences between the tested models in the Supplementary Materials.
Please avoid reporting estimates of main effects in statistical models when an interaction is included: the estimates of the main effects may be heavily biased by the interaction term (this can be checked by re-running the model without the interaction term).
We sincerely appreciate the Reviewer’s comment regarding the interpretation of main effects in the presence of significant interaction terms. In the revised manuscript, we no longer discuss significant main effects and instead focus on interpreting the interaction terms.
Additionally, to help unpack interaction effects, we now include exploratory simple effects analyses in the supplementary materials. Simple effects analyses allow us to examine the effects of one independent variable at specific values of other independent variables (Aiken et al., 1991; Brambor et al., 2006; Jaccard & Turrisi, 2003; Winer et al., 1991).
Supplementary tables S5 and S6 are excessive: there is no third-level interaction (supplementary tables S3 and S4) to justify a split between BN and healthy participants. Please perform rather a descending regression. Accordingly, the results reported in the second paragraph of page 7 should be entirely rewritten.
We agree with the Reviewer’s suggestion that these tables are unnecessary. We have updated them to include details about simple effects analyses described above. We have revised the main text to reflect these changes.
The words such as "predictive" indicating a causality link is used in several places in the manuscript including the supplementary materials while the experimental design does not allow such claims. This should be rephrased.
We agree with the Reviewer that the term “predicted” in the main text improperly suggested a causal relationship between symptom severity and DDM parameters that our methods cannot evaluate. We have updated the main text with more appropriate language. However, our use of the term “predicted” in the Supplementary Materials refers to predicting the probability of a choice based on trial-level features which is standard use of the term in the computational cognitive modeling literature (Piray et al., 2019; Wilson & Collins, 2019; Zhang et al., 2020).
The word "evaluated" appears twice in line 42 of the supplementary materials. Same with "in" at line 50.
Thank you very much for highlighting this. We have removed the repeated words.
Reviewer #2 (Recommendations for the authors):
(1) I think it would be helpful if the authors noted in the Methods how long the food-choice task took. Prior research has suggested that in-lab mood inductions are very short-lasting (e.g., max 7 minutes) and it is likely that the task itself may have impacted the mood states of participants. Expanding on this in the Discussion/limitations seems important.
The Reviewer raises an important point regarding the duration of our affect manipulation. Since we did not measure mood during or after the Food Choice Task, we cannot determine how long these effects persisted. We have added this limitation to the discussion section, noting that the absence of continuous affect measures following mood induction is a widespread limitation in the field.
(2) Personally, I was a bit confused about what data the researchers were using to extrapolate information on whether or not participants were considering healthiness or tastiness. How was this operationalized? Is this an assumption being made based on how quickly someone chose a low-fat vs. high-fat food?
We thank this Reviewer for highlighting that our models’ complexity warrants a more thorough explanation.
Since we collected tastiness and healthiness attribute ratings during the first phase of the Food Choice Task, we can use those values to determine how these attribute values influence decision-making. Independently, foods were classified as low-fat or high-fat based on their objective properties (i.e., the percentage of calories from fat). However, the primary information we used to compute model parameters were participants’ attribute ratings, choices, and response times.
In these models, the drift rate parameter captures the speed and direction of evidence accumulation. As the unsigned magnitude of the drift rate increases, the decision-maker is making up their mind more quickly. Once the evidence accumulates to a response boundary, the option associated with that boundary is selected. A positive drift rate means they are moving toward choosing one option (i.e., upper boundary), and a negative drift rate means they are moving toward choosing the other (i.e., lower boundary). In these decisions, decision-makers often consider multiple attributes, such as perceived healthiness and tastiness. Each of these attributes can influence the evidence accumulation process with different strengths, or weights.
In addition, decision-makers do not consider all attributes at the same time. Inspired by earlier work on multi-attribute decision-making (Maier et al., 2020; Sullivan & Huettel, 2021), our modeling approach computes a parameter (i.e., relative attribute onset) which captures the time delay between when each attribute starts influencing the evidence accumulation process. This parameter gives us a way to estimate when decision-makers are considering different attributes, and tells us how much influence each attribute has, because if the attribute starts late, it has less time to influence the decision. These models use a piecewise drift rate function to describe how evidence changes over time within a trial: sometimes the decision maker only considers taste, sometimes only health, and other times both. Importantly, models with a relative attribute onset parameter can produce key behavioral patterns observed in mouse-tracking studies that models without this parameter are unable to replicate (Maier et al., 2020).
In summary, the computational model describes decision-makers’ behaviors (what they would choose, and how fast they would choose) using different potential values of the drift weights and relative start time parameters. We then used Bayesian estimation methods to compare the model's predictions to the actual data. By examining how reaction times and choices change depending on the attribute values of the presented options, the model allows us to infer when each attribute is considered, and how strongly it influences the final choice.
We have clarified this in the main text.
Reviewer #3 (Recommendations for the authors):
I wonder whether there were any measures concerning negative affect before and after the mood induction? This would make it clearer whether there was a significant change before and after. If different emotions were assessed, which emotion showed the strongest change?
We thank the Reviewer for flagging this point. We realize that the main text did not make it clear that mood was assessed before and after the mood induction using the POMS (McNair et al., 1989). While these analyses were conducted and the results were reported in the original manuscript (Gianini et al., 2019), we now report them in the main text for completeness. Additionally, we added more details about how specific emotions changed by analyzing the subscales of the POMS in the Supplementary Materials. As mentioned above, we found that, across both groups, the negative affect induction increased responses related to anger, confusion, depression, and tension while reducing vigor.
Thank you again for your consideration and for the reviewers’ comments and suggestions. We believe their incorporation has significantly strengthened the paper. In addition, thank you for the opportunity to publish our work in eLife. We look forward to hearing your response.
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