Negative affect influences the computations underlying food choice in bulimia nervosa

Reviewer #1 (Public review):

Summary:

Using a computational modeling approach based on the Drift and 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 in 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 potential to improve the understanding of pathological food choices.

Weaknesses:

I thank the authors for revising their manuscript.

I still notice that the authors did not go through their manuscript to look for wordings refering to a prediction interpretation of their results while I already highlighted the inappropriateness of this wording in my two first rounds of reviews: e.g. there is still "we used zero-inflated negative binomial models to predict the three-month frequency" and I can find other statements like this. The design of their study does not allow such claims.

The authors answered my major concern regarding the experimental induction towards a negative or a neutral state before running the food decision task. My concern is: BN patients already seemed to be already in a high negative state before undergoing the neutral induction, while these patients are in a lower negative state before undergoing the negative induction. It is therefore not surprising that patients seem to report a similar level of negative state after the two inductions (according to the figure of the authors' previous article). Of note is that the additional analysis the authors ran within the BN group only provides a significant result: this result shows that there has been an induction but does not rule out that patients were in the exact same magnitude of negative state to perform the task as the figure in their previously published article suggests it. The major issue is to show that:

(1) As compared to the neutral induction, there has been a higher variation in negative state after as compared to before the negative induction.

(2) The magnitude of the negative state after the negative induction is higher than the magnitude of the negative state after the neutral induction.

The first point shows that the induction worked. The second point shows that the participants are in two distinct states. Without showing the second point, it may be possible that one induction increases the negative state of participants to the same level as the one of the second induction that has not increased anything.

Within this context, how is it possible to associate, in patients, a difference in the DDM between the two sessions to a negative state (which is one of the main focus of the article) rather than to another parameter that has not been captured? A similar situation would be in an experiment studying the consequence of stress, a stressfull induction over relaxed participants attending the lab has high chances to raise the level of stress of those participants to the same level as the one that the same participants would experience after a neutral induction when these participants attend the lab with an already high level of stress. In that case, would it be approrpiate to claim that a difference at a task performed after the induction would be related to stress while the participants would be at the same level of stress when performing the task despite the fact that the induction worked ?

In the experiment performed by the authors, the additional analysis to perform would be a paired sample t-test (or the appropriate non-parametric test) to check whether the magnitude of negative state of BN patients was different between the negative and neutral conditions after the induction only. If not, associating the difference at the DDM with negative states in BN is highly misleading.

I read carefully the authors' answer related to mixed models: they claim that mixed models take into account correlations within their repeated data. The specification of the structure of the covariance matrix allows to control only partly for that. I notice that the authors did not specify the structure of that matrix: the article they refer to to justify the appropriatness of their analyses is not adapted. The specification of the structure of the covariance matrix needs to address, in a mixed model, the difference in handling 4 repeated data per participants that cannot be paired as compared to 4 repeated data that can be paired (two per session with one before and one after the neutral or negative priming sessions, if I count right). Of note is that a covariance structure that is left free of constraint for the fit of the model does not capture appropriately the pairing of the data: it has all chances to capture the covariance in a different way. And a covariance structure that has constraints has more chances to lead to a model that cannot be estimated because of an absence of convergence of the algorithms.

By the way, a single two-sample t-test (or a Mann-Whitney test if appropriate), and not a set of multiple paired-sample t-test as the authors suggest, would answer the goal of the authors to test for what they call the three-way interaction in their comment. This test would be performed between the two groups of participants (BN/controls) with the computation for each participant separately: (assessment after neutral induction-assessment before neutral induction)-(assessment after negative induction-assessment before negative induction). This analysis answers points 1, 2 and 4 they raise together with my point of controlling for the paired data. I would have agreed with their choice of a mixed model if they had an unbalanced dataset within each participant.

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 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:

Sample size was relatively small, and participants were all women with BN, which limits 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. These limitations are adequately noted in the discussion.

Author response:

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 the interpretation of group differences across neutral and negative conditions limit the interpretability of the results.

We are grateful for this improved assessment. Below, we provide detailed responses that we believe address the noted concerns about interpreting group differences across conditions. If these clarifications resolve the interpretability concerns, we would be grateful if the editors would consider updating the eLife assessment accordingly.

Public Reviews:

Reviewer #1 (Public review):

Summary:

Using a computational modeling approach based on the Drift and 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 in 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 potential to improve the understanding of pathological food choices.

Weaknesses:

I thank the author for reviewing their manuscript.

However, I still have major concerns.

The authors say that they removed any causal claims in their revised version of the manuscript. The sentence before the last one of the abstract still says "bias for high-fat foods predicted more frequent subjective binge episodes over three months". This is a causal claim that I already highlighted in my previous review, specifically for that sentence (see my second sentence of my major point 2 of my previous review).

We appreciate the Reviewer's continued attention to causal language. We acknowledge that our use of the term 'predicted', though intended to refer to statistical prediction in a regression model, could be misinterpreted as implying causation. We have therefore revised this sentence to read: 'bias for high-fat foods was associated with more frequent subjective binge episodes over three months’.

I also noticed that a comment that I added was not sent to the authors. In this comment I was highlighting that in Figure 2 of Galibri et al., I was uncertain about a difference between neutral and negative inductions of the average negative rating after the induction in the BN group (i.e. comparing the negative rating after negative induction in BN to the negative rating after neutral induction in BN). Figure 2 of Galibri et al. looks to me that:

(1) The BN participants were more negative before the induction when they came to the neutral session than when they came to the negative session.

(2) The BN participants looked almost negatively similar (taking into account the error bars reported) after the induction in both sessions

These observations are of high importance because they may support the fact that BN patients were likely in a similar negative state to run the food decision task in both conditions (negative and neutral). Therefore, the lack of difference in food choices in BN patients is unsurprising and nothing could be concluded from the DDM analyses. Moreover, the strong negative ratings of BN patients in the neutral condition as compared to healthy participants together with almost similar negative ratings after the two inductions contradict the authors' last sentence of their abstract.

I appreciate that the authors reproduced an analysis of their initial paper regarding the negative ratings (i.e. Table S1). It partly answers my aforementioned point but does not address the fact that BN may have been in a similar negative state in both conditions (neutral and negative) when running the food decision task: if BN patients were similarly negative after both induction (neutral and negative), nothing can be concluded from their differences in their results obtained from the DDM. As the authors put it, "not all loss-ofcontrol eating occurs in the context of negative state", I add that far from all negative states lead to a loss-of-control eating in BN patients. This grounds all my aforementioned remarks and my remarks of my first review.

A solution for that is to run a paired t-test in BN patients only comparing the score after the induction in the two conditions (neutral and negative) reported in Figure 2 of their initial article.

We appreciate the reviewer’s concern. We understand how the visual representation in Figure 2, which displays between-subject error bars, might suggest similar post-induction affect levels. However, the within-subject paired comparison (which appropriately accounts for individual differences in baseline affect) reveals a significant difference, which we detail below.

While BN participants did report higher baseline negative affect than the HC group prior to the mood inductions, this does not negate the effectiveness of the manipulation. The critical comparison is the within-subject change from pre- to post-induction (detailed below) which shows that negative affect was significantly higher after the negative induction than the neutral induction.

As we reported in the Supplementary Information (Table S1), our initial analyses of self-reported affect ratings used a linear mixed-effects model with group (HC = 0, BN = 1), condition (Neutral = 0, Negative = 1), and time (pre-induction = 0, post-induction = 1) as fixed effects, including all interactions, and random intercepts for participants. This approach accounts for individual differences in baseline affect.

However, to address the reviewer's concerns, we conducted two simple effects analyses using estimated marginal means. As the reviewer suggested, we directly compared post-induction affect between conditions within the BN group (described in the second analysis below). In the first analysis, we examined the diagnosis × time interaction within each condition separately. In the Negative condition, individuals with BN demonstrated a substantial increase in negative affect from pre- to post-induction (mean difference = 20.36, t = 4.84, p < 0.0001, Cohen’s d = 0.97). In the second analysis, we examined the condition × time interaction within each group separately. Among the BN group, we found that reported affect was significantly higher following the negative mood induction than after the neutral affect induction (mean difference = -17.40, t = -4.13, p = 0.0003, Cohen’s d = 0.83). This difference in post-induction negative affect between conditions within the BN group represents a meaningful and statistically robust difference in affective states. These within-group effects confirm that the negative mood induction was (1) effective in the BN group and (2) produced significantly greater negative affect than the neutral mood induction.

These findings confirm that participants completed the food decision task under meaningfully different affective states, supporting the interpretability of the subsequent DDM analyses. We now report these analyses in the Supplementary Information.

I appreciate the analysis that the authors added with the restrictive subscale of the EDE-Q.

That this analysis does not show any association with the parameters of interest does not show that there is a difference in the link between self reported restrictions and self reported binges. Only such a difference would allow us to claim that the results the authors report may be related to binges.

We thank the reviewer for raising this important point about specificity. To address this concern, we examined the correlation between self-reported binge frequency (both subjective binge episodes and objective binge episodes over the past three months) and EDE-Q Restraint subscale in our BN sample.

The correlation between these measures were modest and non-significant (subjective binge frequency: Spearman’s p = 0.21, p = 0.306; objective binge frequency: Spearman’s p = 0.05, p = 0.806), indicating that both binge frequency measures and dietary restraint were relatively independent dimensions of eating pathology in our sample. This dissociation supports the specificity of our findings: the fact that our DDM parameters were associated with binge frequency but not with dietary restraint suggests that the affect-induced changes in decisionmaking we observed are specifically related to binge-eating behavior rather than reflecting a correlate of dietary restraint. We now report this analysis in the Supplementary Information.

I appreciate the wording of the answer of the authors to my third point: "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". This sentence is crystal clear and sums very well the limits of the associations the authors report with binge eating frequency. However, I do not see this sentence in the manuscript. I think the manuscript would benefit substantially from adding it.

We thank the reviewer for the suggestion. We have added the following sentences that convey this information to the end of the third paragraph of the discussion:

“These results suggest that individuals whose task behavior is more reactive to negative affect tend to be the most symptomatic. However, our correlational design does not allow us to determine whether this reactivity causes the symptoms.”

Statistical analyses:

If I understood well the mixed models performed, analyses of supplementary tables S1 and S27 to S32 are considering all measures as independent which means that the considered score of each condition (neutral vs negative) and each time (before vs after induction) which have been rated by the same participants are independent. Such type of analyses does not take into account the potential correlation between the 4 scores of a given participant. As a consequence, results may lead to false positives that a linear mixed model does not address. The appropriate analysis would be to run adapted statistical tests pairing the data without running any mixed model.

We appreciate the reviewer's attention to the statistical approach. However, we respectfully note that mixed-effects models do account for within-subject correlations, contrary to the reviewer’s interpretation.

The linear mixed-effects model we employed explicitly accounts for the correlation among repeated measures from the same participant through the random intercept term. This random effect structure models the non-independence of observations within participants, allowing for correlated errors within individuals while assuming independence between individuals. This is a standard and appropriate approach for analyzing repeated-measures data (Bates et al., 2015).

The mixed-effects model is, in fact, more appropriate than separate paired t-tests for our design because it:

(1) Simultaneously models all fixed effects (group, condition, time) and their interactions in a single unified framework;

(2) Properly partitions variance into within-subject and between-subject components;

(3) Provides greater statistical power and more precise estimates by using all available data simultaneously; and

(4) Allows for direct testing of three-way interactions that cannot be assessed through pairwise comparisons alone.

Paired tests (e.g., t-tests), as the reviewer suggests, would require multiple separate analyses and would not allow us to test our primary hypotheses about group × condition × time interactions. The mixed-effects approach provides a more comprehensive and statistically rigorous analysis of our repeated-measures design. To clarify this even further in the manuscript, we have added the following in our methods when describing our model, “participant-level random intercepts were included to account for within-subject correlations across repeated measurements.”

Notes:

It is not because specific methods like correlating self reported measures over long periods with almost instantaneous behaviors (like tasks) have been used extensively in studies that these methods are adapted to answer a given scientific question. Measures aggregated over long periods miss the variations in instantaneous behaviors over these periods.

We acknowledge the reviewer’s concern about the temporal mismatch between our session-level task measures and the 3-month aggregated symptom reports. This is a valid limitation of crosssectional designs, and we agree that examining how task performance fluctuates in relation to real-time symptom variation would provide richer insights into the potential dynamics of these relationships.

We agree that we cannot capture how daily changes in task performance relate to momentary symptom occurrence. In response to previous rounds of helpful reviews, we added this limitation to the Discussion section, noting that future research employing ecological momentary assessment (EMA) or daily diary methods could examine whether the decision-making processes we identified also fluctuate in relation to real-time symptom occurrence.

We note that our finding that affect-induced changes in decision-making parameters were associated with subjective binge frequency suggests that this laboratory-measured reactivity may reflect a stable individual difference that manifests across contexts and time periods. While our current study provides initial evidence that individual differences in affect-related decisionmaking are associated with symptom severity, we acknowledge that longitudinal designs with repeated assessments would strengthen causal and temporal inferences.

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 decisionmaking 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 the 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:

Sample size was relatively small, and participants were all women with BN, which limits 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. These limitations are adequately noted in the discussion.

We are grateful to Reviewer #2 for their careful and supportive review of our manuscript. We appreciate their recognition that computational modeling can reveal nuanced alterations in decision-making processes that may not be apparent in overt behavioral choices. Their balanced assessment of both the strengths and limitations of our work has been helpful in contextualizing our findings appropriately. We have carefully considered their comments regarding sample size and the potential limitations of our mood induction procedure, both of which we discuss in detail in the manuscript's limitations section.

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 are grateful to Reviewer #3 for their thoughtful evaluation of our work. We appreciate their recognition that the diffusion decision model provides a novel analytical lens for understanding how negative affect influences the dynamics of food-related decision-making in bulimia nervosa. Their balanced assessment of both the methodological strengths of our design (counterbalancing, rigorous statistical corrections) and its limitations (sample size, mood induction efficacy) has been valuable in ensuring we appropriately contextualize our findings and their implications. Specifically, we have taken their comments regarding sample size and the relative efficacy of different mood induction methods seriously, and we address these important methodological considerations in our discussion of the study's limitations.

Recommendations for the authors:

Reviewer #2 (Recommendations for the authors):

The authors have addressed my previous comments, and I do not have any additional suggestions for improvement.

We thank the reviewer for their time, effort, and insightful feedback.

Reviewer #3 (Recommendations for the authors):

The authors have adequately addressed my feedback. I have no further comments.

We thank the reviewer for their time, effort, and insightful feedback.