How Emotions Influence Cognitive Control: A Within-Subject Investigation

Round 1

Reviewer 1 Report

Comments and Suggestions for Authors

The study compares the effects of negative emotion on three components of cognitive control—response inhibition (Go/No-Go), updating (2-back), and shifting (set switching). The within-subject design and cross-task comparison are commendable and potentially informative. However, several issues remain:

 

The manuscript states: “However, the precise mechanisms through which negative emotions influence cognition remain unclear, particularly regarding how negative emotions capture attention and interfere with or support specific cognitive functions.” This does not specify what exactly is unclear. The authors should delineate, in concrete terms, which mechanisms are under debate and why. Moreover, they should clarify the theoretical status of attentional capture and cognitive functions in major emotion theories (e.g., value of each construct, hypothesized links, and testable predictions), and explain why these are the focal issues for the present study.

 

The introduction notes that “methodological heterogeneity” in prior work hinders identification of common mechanisms sensitive to emotion. Yet the present study still employs multiple paradigms for different constructs (Go/No-Go, 2-back, set switching). This design does not, by itself, resolve heterogeneity; it reproduces it across tasks. The authors should justify why this choice advances beyond the stated limitation, or consider an integrated paradigm that manipulates inhibition/updating/shifting within a unified task structure.

 

The introduction should focus more tightly on known problems and controversies. Concretely:Paragraph 1: Directly establish the relationship between emotion and cognitive control (rather than beginning broadly with “cognition”).Paragraphs 2–4: Summarize prior findings for emotion effects on inhibition, updating, and shifting, respectively, highlighting contradictions and potential resolutions.Paragraph 5: State the current study’s aims, methods, and hypotheses succinctly.

 

Why was the sample drawn from the French Air Force Academy (with notable gender imbalance)? Did the authors assess and control trait factors that modulate emotional reactivity (e.g., anxiety, depression, trauma history), as well as sleep/medication status? These variables may moderate emotion–control interactions. Please report screening instruments and/or include them as covariates.

 

Although task order was randomized, did the authors test the Task Order × Emotion interaction? Given trial-level induction, emotional states may linger across tasks or blocks, causing cross-task contamination. Please analyze or rule out such carryover.

 

IAPS valence/arousal ratings are largely normative. Were within-subject ratings or physiological indices (e.g., EDA, HRV) collected as manipulation checks? If not, how do the authors ensure that each participant was effectively “negativized” at the trial level?

 

Task stimuli were overlaid on the emotional images. This can alter low-level visual features and perceptual load. Was a control implemented in which the emotional image is presented and then masked before the task stimulus (no spatial overlap), to rule out low-level perceptual confounds?

 

The current approach relies on within-subject ANOVAs and percent “normalized differences.” I strongly recommend hierarchical mixed-effects modeling (trial-level GLMM/LMM) with participants and items (images/trial IDs) as random effects, and trial-level covariates (previous-trial emotion, switch status, target position, etc.). This avoids aggregation bias and improves inferential reliability.

 

With three tasks × multiple measures (RT/accuracy) × multiple contrasts, how was familywise error controlled (e.g., Holm–Bonferroni or an omnibus test within a hierarchical framework)? Please report standardized effect sizes and confidence intervals, not only p-values.

 

The results highlight a single moderate correlation—“A significant moderate positive correlation emerged between the emotions effect in the 2-back task and the Set-Switching task”—and then generalize to “These findings support the hypothesis of a general reduction in control efficiency under negative emotions …” and “both updating and shifting rely on a common executive operation.” This inference is not warranted, particularly given that the two tasks show different impact patterns (updating: selective impairment on Non-Match; switching: global accuracy increase in errors). From a construct-validity standpoint, this pattern is more consistent with different mechanisms perturbed in different ways by emotion, rather than a single shared component being uniformly engaged.

 

A schematic of the experimental procedure should be added, and the results should be presented as figures rather than tables to make them more intuitive. Please include a flowchart of the experimental procedure, and present the results as figures instead of tables for greater clarity and intuitiveness.

Author Response

1. The introduction should focus more tightly on known problems and controversies. Concretely: Paragraph 1: Directly establish the relationship between emotion and cognitive control (rather than beginning broadly with “cognition”). Paragraphs 2–4: Summarize prior findings for emotion effects on inhibition, updating, and shifting, respectively, highlighting contradictions and potential resolutions. Paragraph 5: State the current study’s aims, methods, and hypotheses succinctly.” 

 The manuscript states: “However, the precise mechanisms through which negative emotions influence cognition remain unclear, particularly regarding how negative emotions capture attention and interfere with or support specific cognitive functions.” This does not specify what exactly is unclear. The authors should delineate, in concrete terms, which mechanisms are under debate and why. Moreover, they should clarify the theoretical status of attentional capture and cognitive functions in major emotion theories (e.g., value of each construct, hypothesized links, and testable predictions) and explain why these are the focal issues for the present study.” 

 We thank the reviewer for these two complementary and constructive comments. We address them together, as they both concern the structure and theoretical focus of the introduction. 

First, we acknowledge that the initial version of the introduction may have developed at excessive length both the general relationship between emotion and cognition, and the subsequent discussion of how emotions influence each component of cognitive control. In response, we have rewritten this section to provide a more concise and targeted overview of the link between emotion and cognitive control (P.2-3, l. 89-106), highlighting only the principal findings and the limitations that directly motivate our study. We nevertheless retained a brief theoretical grounding on the broader emotion–cognition relationship, as the hypotheses tested in the present work derive from these foundational accounts, and because this study aimed to advance fundamental knowledge on how emotions shape attentional resources.  

Second, in response to the comment regarding the lack of clarity on unresolved mechanisms, we have refined the theoretical section to specify which mechanisms remain debated (p.2, l. 36; p.2, l. 42-51). We now explicitly describe how major accounts differ with respect to attentional capture by emotional stimuli, whether through intrusive emotional thoughts, automatic prioritization, transient freezing of control processes, or competition for limited attentional resources, and identify which aspects of these mechanisms remain theoretically or empirically unclear. 

Then, following the reviewer’s recommendation, we have restructured the introduction to align with the requested progression: a) establishing the relationship between emotion and cognitive control, b) summarizing prior findings for inhibition, updating, and shifting in separate, focused paragraphs that emphasize inconsistencies in the literature and possible explanations, and c) presenting the aims, methodological approach, and hypotheses of the study in a concise final paragraph. Together, these revisions strengthen the theoretical coherence of the manuscript and clarify the specific questions that the present study seeks to address. 

 

2. The introduction notes that “methodological heterogeneity” in prior work hinders identification of common mechanisms sensitive to emotion. Yet the present study still employs multiple paradigms for different constructs (Go/No-Go, 2-back, set switching). This design does not, by itself, resolve heterogeneity; it reproduces it across tasks. The authors should justify why this choice advances beyond the stated limitation, or consider an integrated paradigm that manipulates inhibition/updating/shifting within a unified task structure. 

 

We fully agree that methodological heterogeneity across paradigms is a major limitation in existing literature. Our intention in the present study was not to eliminate heterogeneity across tasks, but rather to control it by examining inhibition, updating, and shifting within the same individuals, using prototypical and well-validated tasks for each construct. This approach allowed us to compare emotional effects across executive components, in order to investigate whether individuals who show sensitivity to emotions in a specific task also exhibit this sensitivity in other tasks. We have therefore revised the discussion to clarify that the added value of the present study does not lie in eliminating heterogeneity, but rather in controlling inter-individual variability by assessing how emotions influence inhibition, updating and shifting within the same participant (p.13, l. 551-554). 

 We agree that integrated paradigms offer a promising direction for future research, and this is therefore a point we have acknowledged in the limitations and perspectives of our study, by outlining how future works should combine both isolated and integrated paradigms to better delineate shared emotion–control mechanisms (p.13, l.536-541).  

 

3. Why was the sample drawn from the French Air Force Academy (with notable gender imbalance)? Did the authors assess and control trait factors that modulate emotional reactivity (e.g., anxiety, depression, trauma history), as well as sleep/medication status? These variables may moderate emotion–control interactions. Please report screening instruments and/or include them as covariates. 

  

Our sample included one-third of female participants, which is comparable to the gender ratios typically reported in studies on emotion–cognition interactions. Importantly, prior research has not documented systematic gender differences in the direction or reliability of emotional effects on executive control, suggesting that the observed gender distribution is unlikely to bias our findings.  

Moreover, the reviewer is absolutely right to point out that covariables such as anxiety trait, medication or lack of sleep could interfere with our study. In our study, all participants were screened in accordance with the requirements of the Comité de protection des personnes Sud-Est IV, which mandated the exclusion of individuals with a history anxiety disorder, current medication, sleep-related difficulties, or any condition likely to affect emotional responsiveness. In addition, a subset of participants completed the State–Trait Anxiety Inventory (STAI-Y). This screening was used to verify the absence of extreme anxiety levels within the cohort. No atypical or clinically elevated scores were observed, and exploratory analyses revealed no meaningful association between STAI scores and behavioral performance. For this reason, and because the STAI was not administered to all participants, we did not include anxiety as a covariate in the main analyses. 

 4. Although task order was randomized, did the authors test the Task Order × Emotion interaction? Given trial-level induction, emotional states may linger across tasks or blocks, causing cross-task contamination. Please analyze or rule out such carryover. 

 Thanks to the reviewer's recommendations, we explicitly tested the Task Order × Emotion interaction to assess potential carryover or cross-task contamination effects. These analyses revealed no significant interaction, indicating that task order did not modulate the impact of emotional condition on performance. 

We agree that in certain experimental designs, particularly those relying on block-level or session-level emotional inductions, emotional states may persist and lead to carryover effects across tasks or blocks. However, as clarified in our response to comment 5, the goal of the present study was not to induce a sustained emotional state, but rather to elicit transient, trial-specific attentional capture by emotional stimuli. For this reason, emotional conditions were randomized at the trial level, to reduce systematic spillover across trials and tasks. 

 

5. IAPS valence/arousal ratings are largely normative. Were within-subject ratings or physiological indices (e.g., EDA, HRV) collected as manipulation checks? If not, how do the authors ensure that each participant was effectively “negativized” at the trial level? 

 Emotional induction at a trial-level has been used in several studies investigating the influence of emotions on cognition (e.g., Melani et al., 2025; Melani et al., 2024; Fabre & Lemaire, 2019), indicating that random induction at the trial level could have an influence on behavioral outcomes. Beyond these findings, trial-level induction is widely employed in research targeting transient emotional influences on attention and cognitive control (e.g., Kalanthroff et al., 2013). This methodology is specifically recommended when the goal is to capture rapid fluctuations in attentional allocation and interference resolution (Okon-Singer et al., 2015; Pessoa, 2009). Many studies showed that presenting emotional IAPS pictures immediately before a cognitive target reliably modulates performance, even in the absence of block-level mood induction. 

 

We also acknowledge that the term emotional induction may imply the creation of a sustained affective state. However, this is not the purpose of the present experiment. Our objective was not to induce a long-lasting emotional state but rather to trigger a transient attentional capture by emotional stimuli. Trial-level presentation is therefore not only adequate for our research question but methodologically optimal for capturing the transient attentional disruptions that are central to hypothesis of emotion-cognition interactions.  

  

6.Task stimuli were overlaid on the emotional images. This can alter low-level visual features and perceptual load. Was a control implemented in which the emotional image is presented and then masked before the task stimulus (no spatial overlap), to rule out low-level perceptual confounds? 

 We thank the reviewer for raising this important point. We agree that overlaying task stimuli on emotional images can, in principle, modify low-level visual properties and perceptual load, and that this constitutes a potential source of confound. 

In the present study, we did not include a control condition in which the emotional picture was presented and then masked before the onset of the task stimulus with no spatial overlap. According to previous studies (Melani et al., 2024; Melani et al., 2024; Fabre & Lemaire, 2019) we acknowledge that the absence of a non-overlapping control condition prevents us from fully ruling out contributions of low-level perceptual differences. 

 To mitigate these concerns, we a) used negative and neutral pictures that were matched as closely as possible in terms of general visual complexity and b) kept the position, size, and contrast of the task stimuli constant across emotional conditions. We have now clarified this limitation in the Discussion (p.13, l. 555-559) and toned down our claims accordingly, emphasizing that the present results reflect the combined influence of emotional context and potential perceptual differences. 

  7. The current approach relies on within-subject ANOVAs and percent “normalized differences.” I strongly recommend hierarchical mixed-effects modeling (trial-level GLMM/LMM) with participants and items (images/trial IDs) as random effects, and trial-level covariates (previous-trial emotion, switch status, target position, etc.). This avoids aggregation bias and improves inferential reliability. 

 

We agree that trial-level mixed-effects models constitute a powerful tool, particularly when the aim is to capture fine-grained fluctuations in performance across individual trials or to model item-level variance. In the present study, however, our primary objective was different: we sought to compare how negative emotion modulates the three core components of cognitive control within the same participants, using tasks adapted from well-established paradigms. Our primary aim was therefore to evaluate condition-level effects (Emotion, Trial Type, and their interaction) within each task, in order to characterize whether the emotional manipulation influences inhibition, updating, and shifting in the same or different ways. 

This approach closely follows the analytical logic adopted in the majority of studies on trial-level emotional interference in executive control (e.g., Albert et al., 2010; Kalanthroff et al., 2013; Grissmann et al., 2017). Such work typically relies on factorial ANOVAs to assess whether emotional conditions produce systematic differences in mean performance across executive processes. In our case, ANOVAs also served to confirm that each task produced the effects expected in the literature (e.g., switch cost, faster RTs on false alarms, slower RTs on non-match), which was necessary before carrying out cross-task comparisons. 

 Following the reviewer recommendations, we implemented LMM and GLMM including random intercepts for participants and IAPS, as well as trial-level covariates such as previous-trial emotion and block. All models converged without numerical issues. 

However, these models revealed no significant fixed effects of emotion, even in cases where the ANOVA detected reliable differences. This pattern is attributable to several structural features of our data. Indeed, our tasks, especially the Go/No-Go task, include trial types with inherently low error rates (Go trials), restricting the dispersion the mixed-effects models require to detect fixed effects. Our data also presented limited interindividual variability in emotional manipulation, due to trial-level induction, participants respond similarly across repetitions, reducing the random-participant variance component. We therefore believe that the absence of significant effects in the LMM/GLMM models does not indicate that the emotional manipulation failed, but rather reflects the statistical properties of the tasks themselves, which offer limited item-level or trial-level variability for hierarchical estimation. 

 

We recognize however the conceptual value of hierarchical mixed-effects models, particularly for future work aiming to model trial-level fluctuations in emotional processing. We plan to integrate such analysis in a future EEG study. Therefore, we have carefully revised the manuscript to adopt a more cautious and conservative interpretive tone. While the ANOVAs reveal mean differences consistent with our hypotheses, suggesting that negative emotion selectively disrupts certain components of cognitive control, we avoid overstating the robustness of these effects.  

 

8. With three tasks × multiple measures (RT/accuracy) × multiple contrasts, how was familywise error controlled (e.g., Holm–Bonferroni or an omnibus test within a hierarchical framework)? Please report standardized effect sizes and confidence intervals, not only p-values. 

 

Familywise error was controlled through a hierarchical testing framework: post hoc comparisons were only conducted when the corresponding omnibus ANOVA effect (main effect or interaction) reached significance. For all significant interactions, we reported Holm–Bonferroni–corrected post hoc tests, which provide robust control of the familywise error rate while maintaining greater power than classical Bonferroni correction (p.7, l.263, p.7, l.288). Standardized effect sizes (partial η²) were already included in the initial submission; we now additionally report 95% confidence intervals for all relevant means and contrasts. These intervals are presented in Supplementary Table A2, as recommended, to avoid overloading the main text. 

 9. The results highlight a single moderate correlation—“A significant moderate positive correlation emerged between the emotions effect in the 2-back task and the Set-Switching task”—and then generalize to “These findings support the hypothesis of a general reduction in control efficiency under negative emotions …” and “both updating and shifting rely on a common executive operation.” This inference is not warranted, particularly given that the two tasks show different impact patterns (updating: selective impairment on Non-Match; switching: global accuracy increase in errors). From a construct-validity standpoint, this pattern is more consistent with different mechanisms perturbed in different ways by emotion, rather than a single shared component being uniformly engaged. 

  

We thank the reviewer for this thoughtful and important comment. We agree that our initial wording may have overstated the implications of the observed correlation. Specifically, the presence of a single moderate correlation between emotion-related effects in the 2-back and Set-Switching tasks does not warrant the conclusion that a single, uniformly engaged executive component underlies both effects. 

 We acknowledge that the two tasks exhibited distinct patterns of emotional modulation: negative emotions selectively impaired performance on Non-Match trials in the 2-back task, whereas they produced a more global increase in error rates in the Set-Switching task. From a construct-validity perspective, this dissociation indeed suggests that different control mechanisms are modulated in different ways by emotional context, rather than reflecting a unitary executive deficit. 

 

In the revised manuscript, we have therefore tempered our interpretation and clarified that the observed correlation should not be taken as evidence for a single shared executive process. Instead, we propose that updating and shifting may rely on partially overlapping control operations, such as goal maintenance, interference resolution, or the suppression of irrelevant representations, that are differentially recruited depending on task demands. Negative emotions may thus disrupt a common pool of attentional or control resources, while the behavioral manifestation of this disruption varies across tasks. 

We have revised the Discussion accordingly to emphasize the process-specific nature of emotional effects, and to frame the cross-task correlation as reflecting shared vulnerability to emotional interference, rather than a uniform reduction in executive control efficiency. 

 

10. A schematic of the experimental procedure should be added, and the results should be presented as figures rather than tables to make them more intuitive. Please include a flowchart of the experimental procedure, and present the results as figures instead of tables for greater clarity and intuitiveness. 

 

In the revised manuscript, we have added a flowchart of the experimental procedure (p.6) to provide a clear overview of the task structure and trial sequence. In addition, the main behavioral results are now presented as a figure (p.8) to complete the table, to improve the clarity and the intuitiveness of the study.

Reviewer 2 Report

Comments and Suggestions for Authors

I appreciate the opportunity to review this manuscript examining how negative emotion influences cognitive control across inhibition, updating, and shifting. I enjoyed reading this paper. The question is important and aligns well with long-standing debates about how affective states interact with executive function. The use of within-subject design is refreshing, useful and important to the field. I have several comments to improve the manuscript further:

1. The authors state that no prior work has examined effects across three EF components in the same sample. While the exact combination may indeed be novel, the field does include multi-task emotion–EF studies. The novelty claim would be more credible if framed more narrowly and precisely.

2. The paper acknowledges that negative stimuli tend to have stronger cognitive effects, yet elsewhere emphasizes arousal. If valence and arousal motivate different predictions, the introduction should make this conceptual separation clear.

3. Although the predicted effects are listed, they do not always follow directly from the literature summarized. Strengthening the link between specific prior findings and each hypothesis would improve the logic of the introduction.

4. The justification for power analysis relies on an unusually large effect size (η²ₚ = .30) and an unconventional α = .10. A more conservative and conventional power analysis is needed.

5. The study assumes that negative IAPS images reliably induced negative emotional states, but no participant-level affect ratings or physiological measures were collected. Without direct evidence that participants actually experienced negative emotion, interpretations of “emotion effects” remain tentative.

6. I might have missed this but the text notes that images were “matched,” yet Table A1 shows expected differences in valence and arousal. It would help to specify what exactly was matched (e.g., distribution across trial types). More detail about content controls (e.g., presence of mutilation images vs. neutral objects) would also be useful.

7. I would like to encourage the authors to discuss more directly on how their within-subject design differs from what is typically done in the previous literature. Many studies use block-level or session-level emotion inductions, often counterbalanced or temporally separated, to ensure a stable emotional state and reduce spillover or habituation. In contrast, the present study intermixes negative and neutral trials on a trial-by-trial basis, with no washout period. This methodological difference may inadvertently weaken the emotion induction and increase emotional blending across adjacent trials. It would be helpful for the authors to discuss how this design choice aligns with or departs from prior work and whether it might partly account for the pattern of results. For example, see this paper from the same journal: The effect of state gratitude on cognitive flexibility: A within-subject experimental approach. (2020). Brain Sciences, 10(7), 413.

8. Some statements imply broad or robust impairments from negative emotion across EF components. Given the small, selective sample and mixed effect patterns, a more measured tone would be better.

Author Response

1. The authors state that no prior work has examined effects across three EF components in the same sample. While the exact combination may indeed be novel, the field does include multi-task emotion–EF studies. The novelty claim would be more credible if framed more narrowly and precisely. 

We agree that the broader literature does include studies examining emotional influences across multiple executive functions using multi-task designs. Our intention was not to suggest that multi-task emotion–EF approaches are entirely absent from the field. 

We have therefore revised the manuscript to narrow and clarify the novelty claim (p.2, l.69). Specifically, we now emphasize that, to our knowledge, no prior study has examined the three core components of cognitive control within the same group of participants, using a within-subject design that allows direct cross-task comparison. This refined framing more accurately situates the present work relative to existing multi-task studies while highlighting its specific contribution. 

 2. The paper acknowledges that negative stimuli tend to have stronger cognitive effects, yet elsewhere emphasizes arousal. If valence and arousal motivate different predictions, the introduction should make this conceptual separation clear. 

 We agree that the distinction between valence-related effects and arousal-related effects was not sufficiently explicit in the original version of the introduction. This lack of clarity partly reflects a broader limitation in the existing literature, where valence and arousal are often intertwined both theoretically and methodologically, making their independent contributions difficult to disentangle. 

In the revised manuscript, we clarified this point by explicitly acknowledging that the respective roles of valence and arousal in modulating cognitive control remain debated and are not always cleanly separated in prior work. Importantly, we emphasize that our study deliberately focused on negative emotional stimuli, as converging evidence suggests that negative emotions exert particularly strong effects on attention and cognitive processing (p.3, l. 111-116). We hope that these few changes will improve the clarity of our study.  

  3. Although the predicted effects are listed, they do not always follow directly from the literature summarized. Strengthening the link between specific prior findings and each hypothesis would improve the logic of the introduction. 

 

We thank the reviewer for this valuable comment. We agree that, in the initial version, the predicted effects were not always explicitly and directly linked to the literature summarized in the introduction. In line with the suggestions from Reviewer 1, we revised and shortened the introduction, providing a clearer and more focused synthesis of prior findings regarding emotional influences on each component of cognitive control. By reorganizing this section and summarizing the key empirical results for inhibition, updating, and shifting, the theoretical rationale underlying each hypothesis is now clearer.  

4. The justification for power analysis relies on an unusually large effect size (η²ₚ = .30) and an unconventional α = .10. A more conservative and conventional power analysis is needed. 

 In line with the reviewer’s suggestion, we conducted an additional, more conventional power analysis using GPower for a repeated-measures ANOVA with one within-subject factor (4 levels), assuming α = .05, power = .80, and a medium effect size (η²ₚ = .06; f = 0.25). Under these assumptions, the required sample size is approximately 24–30 participants. This is comparable to the sample size used in the present study, indicating that our design had adequate statistical power to detect effects of this magnitude. 

 5. The study assumes that negative IAPS images reliably induced negative emotional states, but no participant-level affect ratings or physiological measures were collected. Without direct evidence that participants actually experienced negative emotion, interpretations of “emotion effects” remain tentative. 

We agree that the absence of participant-level affect ratings or physiological measures limits conclusions about the induction of a sustained emotional state. However, the present study does not assume that negative IAPS images elicited a robust or long-lasting emotional state at the participant level. Instead, our interpretation of “emotion effects” refers to the ability of emotional stimuli to transiently capture attentional resources. Trial-level emotional induction has been widely used to investigate transient emotional influences on cognition and cognitive control (e.g., Fabre & Lemaire, 2019; Melani et al., 2024, 2025; Kalanthroff et al., 2013) and is specifically recommended when the goal is to capture rapid fluctuations in attentional allocation and interference resolution (Okon-Singer et al., 2015; Pessoa, 2009). 

Accordingly, the present manipulation was designed not to induce a sustained emotional state, but to elicit momentary attentional capture by negative emotional stimuli. Numerous studies have shown that presenting emotional IAPS images immediately before a cognitive target reliably modulates behavioral performance through such transient attentional competition, even without block-level mood induction or explicit affect ratings. We have revised the manuscript to clarify this conceptual distinction and to explicitly frame our findings as reflecting attentional capture by emotional stimuli, rather than the induction of a stable emotional state (p.3, l. 116-118).  

 6. I might have missed this but the text notes that images were “matched,” yet Table A1 shows expected differences in valence and arousal. It would help to specify what exactly was matched (e.g., distribution across trial types). More detail about content controls (e.g., presence of mutilation images vs. neutral objects) would also be useful. 

We thank the reviewer for this clarification request. By “matched,” we did not intend to imply that negative and neutral images were equated in valence or arousal, which would not be conceptually appropriate. Rather, images were matched in terms of their distribution across the experimental design, such that the number and proportion of negative and neutral images were balanced across tasks and trial types. This procedure ensured the absence of systematic biases (e.g., a higher concentration of highly negative images in a specific task or trial type). 

As shown in Table A1, negative and neutral images differed in normative valence and arousal ratings, as expected given their emotional category. We have clarified this point in the Methods section and added further details regarding image distribution and content (p.6, l. 170-176).  

7.  I would like to encourage the authors to discuss more directly on how their within-subject design differs from what is typically done in the previous literature. Many studies use block-level or session-level emotion inductions, often counterbalanced or temporally separated, to ensure a stable emotional state and reduce spillover or habituation. In contrast, the present study intermixes negative and neutral trials on a trial-by-trial basis, with no washout period. This methodological difference may inadvertently weaken the emotion induction and increase emotional blending across adjacent trials. It would be helpful for the authors to discuss how this design choice aligns with or departs from prior work and whether it might partly account for the pattern of results. For example, see this paper from the same journal: The effect of state gratitude on cognitive flexibility: A within-subject experimental approach. (2020). Brain Sciences, 10(7), 413. 

 We fully agree that many previous studies have relied on block-level or session-level emotion inductions (e.g., Hartanto et al., 2020; see p. 4, l. 129), which are particularly well suited for eliciting relatively stable affective states while minimizing potential spillover or habituation effects (e.g., through counterbalanced blocks or the inclusion of washout periods). In contrast, our design deliberately intermixed negative and neutral trials on a trial-by-trial basis, without washout periods. The goal of the present study was not to induce a sustained emotional state, but to examine how brief emotional stimuli transiently capture attentional resources and interfere with ongoing executive control processes. Trial-level emotional manipulations have been widely used in studies targeting rapid fluctuations in attentional allocation and cognition (e.g., Melani et al., 2024; Melani et al., 2024; Fabre & Lemaire, 2019). This approach is explicitly recommended when the focus is on momentary competition between emotional and task-related processing, rather than on enduring affective states (Pessoa, 2009; Okon-Singer et al., 2015). 

 We acknowledge, as the reviewer notes, that trial-by-trial intermixing may reduce the likelihood of inducing a stable emotional state and may allow some degree of emotional blending across adjacent trials. However, this potential limitation is also inherent to the mechanism we aimed to study. From this perspective, the absence of washout periods is not a design flaw but a feature that preserves ecological validity and enables the investigation of rapid, transient emotional interference under conditions of fluctuating affective context. 

 Importantly, we have clarified throughout the revised manuscript that the term “emotion effects” in our study refers to the capacity of emotional stimuli to momentarily recruit attentional resources, rather than to the induction of a prolonged emotional state. We have also deepened our choice to use such a design (p.3, l. 122). 

 Finally, we agree that different induction formats may engage partially distinct mechanisms, and we now emphasize that our findings should be interpreted within the specific context of transient, trial-level emotional interference rather than generalized mood effects. This clarification helps situate the present study more precisely within the broader literature on emotion–cognition interactions. 

 8. Some statements imply broad or robust impairments from negative emotion across EF components. Given the small, selective sample and mixed effect patterns, a more measured tone would be better. 

We agree that some formulations in the Discussion may have conveyed an overly broad interpretation of the effects of negative emotions across executive function components, particularly given the selective nature of the sample and the heterogeneous pattern of results across tasks and dependent measures. 

Beyond refining our interpretation toward partially overlapping mechanisms, according to the comments of the reviewer 1, we have therefore revised the manuscript to adopt a more measured and cautious tone (p. 9, l. 351; p. 11, l. 453; p. 12, l. 509). The revised text now consistently reflects that emotional effects varied across tasks, trial types, and performance measures, and should not be interpreted as uniform impairments across executive functions. 

Round 2

Reviewer 1 Report

Comments and Suggestions for Authors

The revised manuscript is satisfactory and is hereby accepted for publication.

Reviewer 2 Report

Comments and Suggestions for Authors

The authors have addressed all of my comments thoughtfully. I agree that the manuscript has improved substantially and will make a valuable contribution to the literature.