Review Reports - Psychological Distress and Quality of Life in a Community-Based Sample of Adults with Atopic Dermatitis: A Cross-Sectional Exploratory Study

Round 1

Reviewer 1 Report

Comments and Suggestions for Authors

The manuscript addresses a clinically relevant topic: the psychosocial burden of Atopic Dermatitis (AD) in adults. The study aims to correlate psychological distress (anxiety/depression) with Quality of Life (QoL) domains. While the premise is sound and the tools used (HADS, WHOQOL-BREF) are validated, the study suffers from significant methodological limitations regarding sample size, statistical rigor, and the measurement of disease severity. These weaknesses must be addressed to ensure the validity of the conclusions.

Major Weaknesses & Critiques
Small Sample Size and Statistical Power

Observation: The study recruited only 47 participants. The authors state that the sample size was calculated based on an effect size of 0.39 to achieve 80% power.
Critique: While N=47 may be sufficient for simple bivariate correlations, it is likely insufficient for the multivariate regression analyses performed later in the study. Standard statistical guidelines often suggest 10–15 participants per predictor variable to avoid overfitting. The regression models included multiple independent variables (e.g., depression, stress, allergy, sleep), suggesting that the model is over-parameterized and that the results may lack stability.
Suggestion: The authors should either recruit more participants to robustly support multivariate regression or simplify their statistical analysis to bivariate associations. If retaining the current sample, the limitations section must explicitly state that the regression results are exploratory and likely underpowered.

Lack of Objective Disease Severity Measures

Observation: The study relies on self-reported "frequency of AD episodes" and subjective triggers (weather, stress).
Critique: There is a complete absence of validated, objective clinical measures of AD severity, such as SCORAD (SCORing Atopic Dermatitis) or EASI (Eczema Area and Severity Index). Furthermore, patient-reported severity measures specific to eczema, such as the Patient-Oriented Eczema Measure (POEM), are missing. Without controlling for clinical severity, it is difficult to determine if high anxiety/depression scores are driven by severe active disease or by psychological factors independent of skin status.
Suggestion: If clinical grading cannot be added retrospectively, the authors must acknowledge this as a major limitation. They should discuss how "perceived" severity (self-report) differs from clinical severity and how this impacts their findings.

Causal Language in a Cross-Sectional Design

Observation: The manuscript frequently uses the term "predicted" or "predictors." For example, "Depression... predicted poorer self-perceived QoL" and "Anxiety significantly predicted depression.
Critique: The study design is cross-sectional8888. Statistical "prediction" in regression does not imply temporal causality. Using such language can be misleading, implying that depression causes poor QoL, whereas the relationship is likely bidirectional (as admitted in the Discussion).
Suggestion: Replace "predicted" and "predictors" with "associated with" or "correlated with" throughout the Abstract, Results, and Discussion to accurately reflect the study design.

Sampling Bias

Observation: Recruitment was done via "convenience and snowball sampling".
Critique: This method introduces selection bias. Participants recruited through snowball sampling may share similar traits (e.g., socioeconomic status, treatment access) or be more active in support groups, potentially inflating distress scores compared to the general AD population.
Suggestion: This bias should be clearly articulated in the limitations section. The term "Community-Based" in the title is slightly misleading, given the non-random sampling; "Cross-Sectional Study" might be more appropriate.

Specific Suggestions for Rigor

Methodology & Data Reporting

Clarify "Episodes": The variable "Eczema episode (per year)" is used, but "episode" is not defined. Is it a flare requiring corticosteroids? A self-perceived worsening? A clear operational definition is needed.
Medication Control: The methodology mentions collecting data on "current treatments", but this data does not appear to be used in the analysis. The impact of systemic vs. topical treatments on QoL is significant. This data should be reported in Table 1 and, if possible, controlled for in the analysis.
Check Section Numbering: There is an inconsistency in numbering. Section 2.2.1 is followed immediately by 2.1.2. Please standardize the outline.

Results & Tables

Reporting Precision: In Table 1, "AD-perceving factors" contains a typo; it should be "AD-perceiving".
Detailed Regression Tables: The text mentions "Detailed regression coefficients... are provided in Table S2". Ensure these tables include Confidence Intervals (95% CI). Given the small sample size, wide CIs would further indicate the uncertainty of the estimates.

Discussion

Overreaching Implications: The conclusion states, "Strategies should be developed to tackle not only physical burden but also psychological distress". While true, the study did not test any strategies. The authors should link their recommendations more closely to their specific findings—e.g., "High correlations between sleep and Environmental QoL suggest sleep hygiene may be a specific target for intervention."
Comparison to Norms: It would be rigorous to compare the HADS scores (Mean 7.91 and 6.28) against local Hong Kong population norms, not just theoretical cut-offs. This would contextualize whether the AD population is truly more distressed than the general public.

Final Recommendation

The study provides preliminary evidence of the psychological burden of AD in this specific cohort. However, the sample size is a critical limitation that reduces the robustness of the multivariate analysis.

Decision: Major Revisions.

Author Response

Major Weaknesses & Critiques
Small Sample Size and Statistical Power

Observation: The study recruited only 47 participants. The authors state that the sample size was calculated based on an effect size of 0.39 to achieve 80% power.
Critique: While N=47 may be sufficient for simple bivariate correlations, it is likely insufficient for the multivariate regression analyses performed later in the study. Standard statistical guidelines often suggest 10–15 participants per predictor variable to avoid overfitting. The regression models included multiple independent variables (e.g., depression, stress, allergy, sleep), suggesting that the model is over-parameterized and that the results may lack stability.
Suggestion: The authors should either recruit more participants to robustly support multivariate regression or simplify their statistical analysis to bivariate associations. If retaining the current sample, the limitations section must explicitly state that the regression results are exploratory and likely underpowered.

Reply: Thank you for raising this important methodological point. We agree that our sample size of 47 limits the robustness of the multivariate regression analyses. As suggested, we will address this limitation explicitly in the revised manuscript, stating that these results are exploratory and require validation in larger cohorts.

Lack of Objective Disease Severity Measures

Observation: The study relies on self-reported "frequency of AD episodes" and subjective triggers (weather, stress).
Critique: There is a complete absence of validated, objective clinical measures of AD severity, such as SCORAD (SCORing Atopic Dermatitis) or EASI (Eczema Area and Severity Index). Furthermore, patient-reported severity measures specific to eczema, such as the Patient-Oriented Eczema Measure (POEM), are missing. Without controlling for clinical severity, it is difficult to determine if high anxiety/depression scores are driven by severe active disease or by psychological factors independent of skin status.
Suggestion: If clinical grading cannot be added retrospectively, the authors must acknowledge this as a major limitation. They should discuss how "perceived" severity (self-report) differs from clinical severity and how this impacts their findings.

Reply: We thank you for your crucial and valid comments. We made revision in Limitation section to mention that the absence of using objective clinical severity measures such as SCORAD or EASI, is a significant limitation.

Causal Language in a Cross-Sectional Design

Observation: The manuscript frequently uses the term "predicted" or "predictors." For example, "Depression... predicted poorer self-perceived QoL" and "Anxiety significantly predicted depression.
Critique: The study design is cross-sectional8888. Statistical "prediction" in regression does not imply temporal causality. Using such language can be misleading, implying that depression causes poor QoL, whereas the relationship is likely bidirectional (as admitted in the Discussion).
Suggestion: Replace "predicted" and "predictors" with "associated with" or "correlated with" throughout the Abstract, Results, and Discussion to accurately reflect the study design.

Reply:

We thank the reviewer for this important observation. Regarding inappropriate use of causal terminology for a cross-sectional analysis, we replaced terms like "predicted," "predictors," and "prediction" with more accurate terms such as "associated with," "correlated with," and "correlates" throughout the relevant sections.

Sampling Bias

Observation: Recruitment was done via "convenience and snowball sampling".
Critique: This method introduces selection bias. Participants recruited through snowball sampling may share similar traits (e.g., socioeconomic status, treatment access) or be more active in support groups, potentially inflating distress scores compared to the general AD population.
Suggestion: This bias should be clearly articulated in the limitations section. The term "Community-Based" in the title is slightly misleading, given the non-random sampling; "Cross-Sectional Study" might be more appropriate.

Reply: We have revised the manuscript accordingly. Regarding the comment for sampling bias, we acknowledge the potential for selection bias due to our convenience and snowball sampling methods. We have added a clear statement in the Limitations section of the Discussion to articulate this bias and clarify the interpretation of the term "Community-Based." For the comment Clarify "Episodes"

Regarding the limit representativeness of our sample by using convenience/snowball sampling, we added a clear statement about this potential bias in the revised Limitations paragraph of the Discussion.

Specific Suggestions for Rigor

Methodology & Data Reporting

Clarify "Episodes": The variable "Eczema episode (per year)" is used, but "episode" is not defined. Is it a flare requiring corticosteroids? A self-perceived worsening? A clear operational definition is needed.

Reply: We thank the reviewer for their thoughtful and constructive feedback. The reviewer is correct that the term "episode" was not operationally defined, which could lead to variability in participant interpretation. We have added a clear operational definition of "atopic dermatitis episode" in the Methods section under 2.3.1. Demographics to ensure clarity and consistency in reporting. The term is now defined as "a self-perceived significant worsening of skin symptoms, such as increased itching, redness, or rash, that would typically prompt a change in daily management or the use of rescue medication.

Medication Control: The methodology mentions collecting data on "current treatments", but this data does not appear to be used in the analysis. The impact of systemic vs. topical treatments on QoL is significant. This data should be reported in Table 1 and, if possible, controlled for in the analysis.

Reply: We thank the reviewer for this insightful comment. The impact of treatment type (systemic versus topical) on quality of life (QoL) is indeed an important factor that we did not fully explore in our initial analysis. In response, we have now included the data on "current treatments" in Table 1 (Demographic Characteristics and AD-Perceiving Factors).

Please note that treatment information was available for only 14 out of 47 participants. The treatments have been categorized into groups such as Topical Only, Steroids, and Systemic and Topical. Due to the limited sample size and the distribution of treatment types, further analysis controlling for treatment may not reliably reflect the QoL within this population.

We have also added a statement to the Limitations section of the Discussion to transparently acknowledge this limitation and to suggest that examining the impact of treatment type warrants further investigation in future research.

Check Section Numbering: There is an inconsistency in numbering. Section 2.2.1 is followed immediately by 2.1.2. Please standardize the outline.

Reply: We thank for your comment. The numbering has been fixed.

Results & Tables

Reporting Precision: In Table 1, "AD-perceving factors" contains a typo; it should be "AD-perceiving".

Reply: We thank you for your comment. The typo has been revised.

Detailed Regression Tables: The text mentions "Detailed regression coefficients... are provided in Table S2". Ensure these tables include Confidence Intervals (95% CI). Given the small sample size, wide CIs would further indicate the uncertainty of the estimates.

Reply: Thank you for valuable and important comments. Table S2 has been revised accordingly. Because some results of 95% CIs are relatively wide, further information has been added in the Results and limitation sections.

Discussion

Overreaching Implications: The conclusion states, "Strategies should be developed to tackle not only physical burden but also psychological distress". While true, the study did not test any strategies. The authors should link their recommendations more closely to their specific findings—e.g., "High correlations between sleep and Environmental QoL suggest sleep hygiene may be a specific target for intervention."

Reply: We thank the reviewer for this valuable feedback. We agree that our original statement was too broad and not sufficiently grounded in our specific results. In response, we have revised the Highlights and Discussion sections to explicitly connect our recommendations to key empirical findings, for example, highlighting the strong association between sleep disturbances and lower environmental QoL, which suggests that sleep hygiene may be a specific target for intervention.

Comparison to Norms: It would be rigorous to compare the HADS scores (Mean 7.91 and 6.28) against local Hong Kong population norms, not just theoretical cut-offs. This would contextualize whether the AD population is truly more distressed than the general public.

Reply: We thank the reviewer for this valuable suggestion, which would indeed provide more meaningful context for interpreting the absolute levels of distress in our cohort. In response, we have incorporated a brief comparison of our HADS scores to available local Hong Kong population norms into the Results section (3.2. Anxiety, depression, and QoL). Additionally, we have qualified and contextualized our interpretation in the Discussion to better reflect how our cohort’s distress levels compare to the general population.

Final Recommendation

Reply: We thank the reviewer for acknowledging the contribution of our study and for raising a crucial point regarding sample size. We fully agree that the modest sample size (n=47) is a significant limitation, particularly for the multivariate analyses. We have also strengthened the Limitations section in the Discussion to explicitly address the impact of sample size on the robustness and generalizability of our findings.

Reviewer 2 Report

Comments and Suggestions for Authors

In the abstract, the main area for improvement relates to conceptual and methodological precision. Given the cross-sectional nature of the study, any language suggesting causality should be avoided. The use of terms such as “predictors” may lead readers to infer causal relationships that the study design does not allow, and it would therefore be more appropriate to refer to “associated factors.” In addition, the abstract highlights the role of stress and sleep quality; however, these variables are not clearly operationalized in the methods through specific and validated instruments, which compromises the internal consistency of the manuscript. It would be important to clarify that these are self-reported variables or, alternatively, to reduce the emphasis placed on them in the abstract. The small sample size, although justified by a statistical power calculation, should also be contextualized as a limitation, reinforcing the exploratory nature of the study.

In the introduction, despite being well grounded and supported by current and relevant literature, there is some redundancy in the description of the psychosocial impact of atopic dermatitis, which makes this section overly long. Greater synthesis would improve the flow of the text. Furthermore, the scientific gap that the study aims to address is not fully explicit. Although it is stated that few studies examine predictors of quality of life, it would be important to clarify how this study differs from previous research, for example by emphasizing the community-based context, the focus on an Asian population, or on young adults. The objectives are clearly defined but could be accompanied by guiding hypotheses, even if exploratory, to strengthen the logical coherence between the literature review and the empirical analysis. Finally, the somewhat interchangeable use of the terms “psychological distress,” “stress,” “anxiety,” and “depression” may generate conceptual ambiguity, making a clearer and more consistent definition of psychological constructs throughout the text desirable.

With regard to the methods, although the cross-sectional design and the use of validated instruments are appropriate for the study objectives, there are important limitations that should be better justified or explicitly acknowledged. Convenience and snowball sampling limit sample representativeness and the generalizability of the findings, and this should be more clearly stated. The exclusion of participants with diagnosed mental health conditions is particularly problematic, given that the study specifically examines anxiety and depression, and may lead to an underestimation of the psychological impact of atopic dermatitis; this decision requires stronger justification or a more critical discussion of its implications. In addition, no standardized instruments were used to assess atopic dermatitis severity, which weakens the interpretation of associations between physical symptoms and quality of life. Variables such as stress, sleep, and environmental factors are treated as predictors in the statistical analyses but are not clearly described in terms of their operationalization, raising concerns about the validity of the findings. From a statistical perspective, the number of multivariate analyses conducted appears high relative to the sample size, increasing the risk of unstable models and spurious results. A more parsimonious analytical approach and a clearer description of procedures used to verify statistical assumptions, such as multicollinearity, would be advisable. Finally, inconsistent use of verb tenses should be corrected, replacing future tense with past tense in accordance with scientific writing conventions.

Regarding the results, their presentation is generally clear, well structured, and aligned with the study objectives. The description of the sociodemographic and clinical characteristics of the sample is appropriate and provides adequate context for interpreting the findings. The bivariate analyses are correctly reported, including correlation coefficients and p-values, which facilitates interpretation. However, the scope and complexity of the multivariate analyses raise some concerns. The high number of regression models relative to the small sample size increases the risk of statistical instability and overfitting. Moreover, although many results are statistically significant, it is not always clear whether the magnitude of the effects is clinically meaningful, an aspect that could be explored further. Some redundancy is also evident between the results presented in the text and those shown in the tables, and the narrative could be more concise and focused on the most relevant findings. Finally, the continued use of the term “predictors” in the results section may again suggest causal interpretations and should be replaced with “associated variables.”

The discussion is one of the strongest sections of the manuscript, offering a comprehensive and well-contextualized interpretation of the findings in light of the existing literature. The authors demonstrate strong theoretical understanding and successfully integrate the results within a conceptual framework that views atopic dermatitis as a chronic condition with multidimensional impact. The discussion of the bidirectional relationship between physical symptoms, psychological distress, and quality of life is particularly well developed. Nevertheless, in some instances, the discussion tends to overextend the findings, approaching causal interpretations that are not supported by the cross-sectional design. Additionally, some explanatory arguments rely on variables that were not objectively or systematically measured, such as stress and disease severity, which weakens the robustness of the interpretations. Although study limitations are acknowledged, they could be discussed more critically, particularly with respect to sampling bias, the exclusion of individuals with mental health conditions, and the statistical limitations associated with the number of regression analyses performed. Despite these issues, the discussion presents relevant and coherent clinical implications and convincingly argues for the need for integrated care approaches.

The conclusion is clear, well structured, and consistent with the reported results. It appropriately summarizes the main findings without introducing new information and reinforces the clinical relevance of the study by highlighting the psychological burden and reduced quality of life experienced by individuals with atopic dermatitis. The identification of potentially modifiable factors is pertinent and well aligned with practical implications for healthcare professionals. However, the conclusion would benefit from a more cautious tone, avoiding overgeneralization given the sample size and sampling strategy. It would also be desirable to explicitly emphasize the exploratory nature of the study and the need for confirmation of the findings in larger samples and longitudinal study designs.

Author Response

In the abstract, the main area for improvement relates to conceptual and methodological precision. Given the cross-sectional nature of the study, any language suggesting causality should be avoided.

Reply: We thank the reviewer for their continued attention to detail. We agree that maintaining precise, non-causal language in the Abstract is crucial. We have reviewed the Abstract and made the necessary correction to ensure all language is associative, not predictive. We have revised the relevant sentence in the Abstract's Results section to correctly reflect the cross-sectional design

The use of terms such as “predictors” may lead readers to infer causal relationships that the study design does not allow, and it would therefore be more appropriate to refer to “associated factors.”

Reply: We thank the reviewer for this important methodological clarification. The reviewer is correct that "stress" and "inadequate sleep" were not assessed with validated instruments. These variables emerged from participants’ open-ended self-reporting of factors they perceived to be associated with their AD exacerbations. We made revisions in Abstract (conclusion), Methods, and Discussion Sections.

In addition, the abstract highlights the role of stress and sleep quality; however, these variables are not clearly operationalized in the methods through specific and validated instruments, which compromises the internal consistency of the manuscript. It would be important to clarify that these are self-reported variables or, alternatively, to reduce the emphasis placed on them in the abstract.

Reply: We thank the reviewer for this constructive feedback regarding the flow of the Introduction. We agree that greater synthesis would enhance readability. We have revised the Introduction to streamline the description of the psychosocial impact of AD. We have consolidated overlapping points, removed redundant phrasing, and synthesized the literature to create a more concise and fluid narrative while preserving all key concepts and supporting citations.

The small sample size, although justified by a statistical power calculation, should also be contextualized as a limitation, reinforcing the exploratory nature of the study.

Reply: We thank the reviewer for this constructive feedback regarding the flow of the Introduction. We agree that greater synthesis would enhance readability.
We have revised the Introduction to streamline the description of the psychosocial impact of AD. We have consolidated overlapping points, removed redundant phrasing, and synthesized the literature to create a more concise and fluid narrative while preserving all key concepts and supporting citations.

Furthermore, the scientific gap that the study aims to address is not fully explicit. Although it is stated that few studies examine predictors of quality of life, it would be important to clarify how this study differs from previous research, for example by emphasizing the community-based context, the focus on an Asian population, or on young adults.

Reply: We thank the reviewer for this insightful suggestion. The reviewer is correct that we could more clearly articulate the unique contribution of our study. We have revised the final paragraph of the Introduction to explicitly state the scientific gaps our study addresses. We now specify that our research focuses on a community-based, non-clinical sample of predominantly young adults in an Asian setting (Hong Kong), areas where targeted research has been limited. This revision clarifies how our study differs from and builds upon previous research, providing a clearer justification for our aims.

The objectives are clearly defined but could be accompanied by guiding hypotheses, even if exploratory, to strengthen the logical coherence between the literature review and the empirical analysis.

Reply: We thank the reviewer for this valuable suggestion to enhance the methodological rigor and logical flow of our manuscript. We have added a set of guiding, exploratory hypotheses at the end of the Introduction, following the statement of our research aims. These hypotheses (H1–H3) are directly derived from the literature reviewed and explicitly link the known psychosocial burden of AD to our specific empirical questions regarding anxiety, depression, and QoL in our community-based sample.

Finally, the somewhat interchangeable use of the terms “psychological distress,” “stress,” “anxiety,” and “depression” may generate conceptual ambiguity, making a clearer and more consistent definition of psychological constructs throughout the text desirable.

Reply: We sincerely thank the reviewer for this critical observation, which significantly improves the conceptual clarity of our manuscript. The reviewer is absolutely correct that our terminology required greater precision. We have carefully revised the manuscript to establish and apply clear, consistent definitions for the key psychological constructs: psychological stress, anxiety and depression, and stress.

Reply: We thank the reviewer for reinforcing this crucial point. We agree that the limitations of our sampling method deserve explicit and unambiguous acknowledgment. We have substantially strengthened the statement regarding sampling limitations in the Discussion section. The revised text now explicitly identifies non-representative sampling as a "primary methodological limitation," clearly describes the risk of selection bias, directly states the constraint on generalizability, and clarifies that our findings reflect a specific community-engaged cohort. This provides a much clearer and more forthright acknowledgment of this limitation as requested.

The exclusion of participants with diagnosed mental health conditions is particularly problematic, given that the study specifically examines anxiety and depression, and may lead to an underestimation of the psychological impact of atopic dermatitis; this decision requires stronger justification or a more critical discussion of its implications.

Reply: We thank the reviewer for this critically important observation. The reviewer is absolutely correct that excluding individuals with diagnosed mental health conditions is a consequential methodological choice that requires clear justification and a thorough discussion of its implications. We made revisions in Abstract (conclusion), Methods, and Discussion Sections.

In addition, no standardized instruments were used to assess atopic dermatitis severity, which weakens the interpretation of associations between physical symptoms and quality of life.

Reply: We thank the reviewer for reinforcing this critical methodological point. We fully agree that the lack of a standardized AD severity measure is a major limitation that constrains the interpretation of our findings, particularly regarding the link between physical symptoms and QoL. We have strengthened the corresponding statement in the Limitations section of the Discussion. The revised text now explicitly states that this absence "fundamentally weakens the interpretation of the physical symptom-QoL relationship" and clarifies the core interpretative problem: we cannot discern whether the associations are mediated by objective disease severity or by subjective perception and distress.

Variables such as stress, sleep, and environmental factors are treated as predictors in the statistical analyses but are not clearly described in terms of their operationalization, raising concerns about the validity of the findings. From a statistical perspective, the number of multivariate analyses conducted appears high relative to the sample size, increasing the risk of unstable models and spurious results.

Reply: We thank the reviewer for these two essential methodological critiques, which greatly improve the rigor and transparency of our manuscript. We made revisions on 2.3.1 Methods section, 2.5 and Limitations Sections.

A more parsimonious analytical approach and a clearer description of procedures used to verify statistical assumptions, such as multicollinearity, would be advisable.

Reply: We thank the reviewer for this important point regarding measurement clarity. We have revised the manuscript to provide a precise description of how these variables were operationalized. In the Methods section (2.3.1 Demographics), we now explicitly state that variables like 'stress' and 'inadequate sleep' were derived from categorizing participant responses to an open-ended question about perceived AD-associated factors. We clarify that these are patient-identified, perceived contributors captured through qualitative reporting, not scores from validated clinical scales. This description accurately reflects the origin and nature of these variables, addressing the concern about their operationalization and appropriate interpretation.

Finally, inconsistent use of verb tenses should be corrected, replacing future tense with past tense in accordance with scientific writing conventions.

Reply: We thank the reviewer for noting this important detail regarding scientific writing style. We have carefully reviewed the manuscript and corrected inconsistent verb tenses. Specifically, we have changed all instances of the future tense in the Methods and Results sections (e.g., "will be used") to the past tense (e.g., "was used") to accurately reflect that the study procedures and analyses have been completed.

Reply: Thank you for your valuable feedback. We appreciate your positive assessment of the clarity, structure, and contextualization of our results. We acknowledge your concern regarding the number of multivariate regression models relative to our sample size, which may pose risks of statistical instability and overfitting. To address this, we have revised our manuscript to clearly state in the Methods and Results sections that these analyses are exploratory and should be interpreted with caution due to the sample size limitations. We also emphasize in the Discussion that the findings from these models are preliminary and require validation in larger, more representative samples.

Moreover, although many results are statistically significant, it is not always clear whether the magnitude of the effects is clinically meaningful, an aspect that could be explored further. Some redundancy is also evident between the results presented in the text and those shown in the tables, and the narrative could be more concise and focused on the most relevant findings.

Reply: Thank you for your insightful feedback. We appreciate your emphasis on the importance of distinguishing between statistical significance and clinical relevance. In response, we have revised the manuscript to streamline the Results section to reduce redundancy between the text and tables, focusing the narrative on the most salient and impactful findings and to make the description more concise and targeted, highlighting key results that are both statistically significant and clinically relevant.

Finally, the continued use of the term “predictors” in the results section may again suggest causal interpretations and should be replaced with “associated variables.”

Reply: We thank the reviewer for their careful attention to detail. We agree that consistent, non-causal language is essential. We have reviewed Section 3.4 (Results) and replaced any remaining instances of the term "predictors" with appropriate associative language, such as "factors associated with" or "correlates." We have ensured that the language in this section is now fully consistent with the corrected section heading and the cross-sectional nature of our study.

Reply: Thank you for your encouraging comments regarding the strengths of our discussion section. We appreciate your recognition of our comprehensive interpretation and integration of the findings within the conceptual framework of AD as a multidimensional, chronic condition.

We also acknowledge your valuable point regarding the potential overextension of causal implications. In our revised discussion, we have taken care to clarify that the cross-sectional design limits our ability to infer causal relationships. We have adjusted the language to emphasize that our findings demonstrate associations rather than causation. Specifically, we now highlight that modifiable factors such as sleep quality, stress, and disease activity are linked to mental health and QoL outcomes, but causal inferences require longitudinal or interventional studies for confirmation.

Additionally, some explanatory arguments rely on variables that were not objectively or systematically measured, such as stress and disease severity, which weakens the robustness of the interpretations.

Reply: We thank the reviewer for this important clarification, which ensures our interpretations are precisely aligned with our measurement methods. We have reviewed the Discussion section and identified where interpretations relied on variables measured with limited rigor (self-reported stress, self-reported episode frequency). We have qualified these explanatory arguments by explicitly referring to the nature of measurement (e.g., "self-reported perceptions of stress," "self-reported episode frequency") and by acknowledging that our interpretations are based on patient-identified factors rather than objective clinical assessments.

Although study limitations are acknowledged, they could be discussed more critically, particularly with respect to sampling bias, the exclusion of individuals with mental health conditions, and the statistical limitations associated with the number of regression analyses performed. Despite these issues, the discussion presents relevant and coherent clinical implications and convincingly argues for the need for integrated care approaches.

Reply: We thank the reviewer for this critical feedback. We agree that our original limitations section was not sufficiently focused or critical in its discussion of these core methodological issues. We have thoroughly rewritten the Limitations section in the Discussion to provide a more logical, concise, and critically engaged synthesis.

Reply: We thank the reviewer for this crucial final suggestion to ensure our conclusions are appropriately measured. We have revised the Conclusion section to adopt a more cautious and qualified tone throughout.

Round 2

Reviewer 1 Report

Comments and Suggestions for Authors

The manuscript tackles a clinically meaningful question: how anxiety/depression relate to multidimensional quality of life in adults with atopic dermatitis, and the use of HADS and WHOQOL-BREF is appropriate for a preliminary community sample. However, despite improvements in tone (replacing causal language) and an expanded limitations section, the current version still contains multiple internal inconsistencies and data-reporting errors that undermine confidence in the results as presented. Because several issues are not “minor polishing” but rather affect interpretability and reproducibility, my decision remains Major Revision.

The most immediate problem is the internal consistency of core reporting. The ethics approval information is inconsistent across the manuscript: the Methods section cites one ethics reference number, while the Institutional Review Board Statement later cites a different protocol code and date. This is a credibility issue because it concerns study governance and cannot be left ambiguous. Similarly, the Abbreviations list is incorrect (it conflates HADS and QoL), which signals insufficient technical proofreading in a paper that depends on precise measurement reporting. These are easy fixes, but leaving them uncorrected damages trust in the rest of the manuscript.

There are also clear numerical and labeling errors in Table 1 that must be corrected before publication. The treatment section contains at least one plainly wrong percentage (e.g., a category shown as “7” with “0.5%,” which is mathematically impossible in a sample where treatment data are available for 14 participants). In addition, the “Related factors” frequencies conflict with the narrative. Results: the text states that stress was identified by 12 participants (25.5%), but the table lists stress as 25 with 25.5%, which cannot both be true. These are not cosmetic typos; they change the descriptive epidemiology of your sample and can mislead readers about the proportion of people who reported stress, allergies, and sleep problems.

Methodologically, the authors correctly state that multivariable regression is exploratory with n=47, but the paper still leans too heavily on multivariable interpretations as if they were stable. Even with attempts to “minimize factors,” the regression section reports several models across multiple QoL domains plus anxiety and depression, which increases the risk of overfitting and selective significance in a small dataset. The added 95% CIs help, but the manuscript should go further: tighten the narrative so that regression findings are explicitly framed as hypothesis-generating and avoid presenting them as “key factors” with near-interventional implications.

A deeper problem is that parts of the regression interpretation are directionally inconsistent with the reported coefficients. In the self-perceived QoL model, stress and allergy are described as “adversely affecting” QoL, yet the B coefficients shown are positive, indicating that, as coded, those variables would be associated with higher, not lower, QoL. That contradiction strongly suggests either (a) coding direction is reversed and not described, (b) the narrative is incorrect, or (c) the sign was copied incorrectly. This must be reconciled because it directly affects the manuscript’s practical takeaway (e.g., whether stress is linked to worse QoL in this dataset). Until the authors resolve the sign/coding problem and ensure the text matches the tables, the regression results cannot be trusted.

The measurement description also needs tightening. The HADS section describes item responses as a “3-point Likert scale” while simultaneously stating scoring from 0 to 3, which implies four response options; the anchors provided (“never” to “always”) also read like generic placeholders rather than the scale’s actual item-dependent response formats. This doesn’t invalidate the data, but it is incorrect instrument reporting and invites reviewer skepticism. Likewise, the “episodes per year” definition is now clearer, which is good, but it remains a subjective severity proxy; without objective or validated patient-reported severity (e.g., POEM) or clinician severity (e.g., EASI/SCORAD), the paper still cannot separate psychological distress driven by active/severe disease from distress that is partly independent of disease activity. The limitations state this, but the Discussion should more explicitly caution that observed associations could be confounded by unmeasured severity.

Finally, the manuscript’s framing still overshoots the sampling reality. The study uses convenience and snowball sampling, excludes participants with diagnosed mental health conditions, and relies on a predominantly young, highly educated cohort. These choices narrow generalizability and likely bias estimates of distress and QoL in unknown directions. The revised text acknowledges bias, but the title and conclusion should be kept modest and clearly positioned as preliminary evidence in a specific community-connected cohort rather than implying broader population inference.

Decision: Major Revision

Author Response

We sincerely thank for your careful reading, insightful comments, and constructive suggestions, which have significantly helped us improve the manuscript 's accuracy, clarity, and methodological rigor. We are grateful for the reviewer's time and expertise. We have revised the manuscript accordingly, with all changes highlighted in yellow in the revised version. Our point-by-point responses to each comment are provided below.

The manuscript tackles a clinically meaningful question: how anxiety/depression relate to multidimensional quality of life in adults with atopic dermatitis, and the use of HADS and WHOQOL-BREF is appropriate for a preliminary community sample. However, despite improvements in tone (replacing causal language) and an expanded limitations section, the current version still contains multiple internal inconsistencies and data-reporting errors that undermine confidence in the results as presented. Because several issues are not “minor polishing” but rather affect interpretability and reproducibility, my decision remains Major Revision.

Response: We thank for acknowledging the improvements and the clinical relevance of our study. We have carefully addressed all the remaining issues concerning internal consistency and data reporting, as detailed in the responses below. We believe these revisions have strengthened the manuscript's credibility and clarity.

The most immediate problem is the internal consistency of core reporting. The ethics approval information is inconsistent across the manuscript: the Methods section cites one ethics reference number, while the Institutional Review Board Statement later cites a different protocol code and date. This is a credibility issue because it concerns study governance and cannot be left ambiguous. Similarly, the Abbreviations list is incorrect (it conflates HADS and QoL), which signals insufficient technical proofreading in a paper that depends on precise measurement reporting. These are easy fixes but leaving them uncorrected damages trust in the rest of the manuscript.

Response: We sincerely apologize for these oversights. We have now corrected these inconsistencies:

Ethics Approval: The ethics reference number has been standardized to REC2024220 in both the Methods section (Section 2.6) and the Institutional Review Board Statement.

Abbreviations List: The list has been corrected to accurately and separately define the key instruments:

- HADS: Hospital Anxiety and Depression Scale

- QoL: Quality of Life

- WHOQOL-BREF: World Health Organization Quality of Life - Brief Version

There are also clear numerical and labeling errors in Table 1 that must be corrected before publication. The treatment section contains at least one plainly wrong percentage (e.g., a category shown as “7” with “0.5%,” which is mathematically impossible in a sample where treatment data are available for 14 participants). In addition, the “Related factors” frequencies conflict with the narrative. Results: the text states that stress was identified by 12 participants (25.5%), but the table lists stress as 25 with 25.5%, which cannot both be true. These are not cosmetic typos; they change the descriptive epidemiology of your sample and can mislead readers about the proportion of people who reported stress, allergies, and sleep problems.

Response: We thank the reviewer for identifying these critical errors. We have meticulously reviewed and corrected Table 1:

Treatment Data: The percentage for "Steroids" has been corrected from 0.5% to 85.7%, accurately reflecting that 12 out of the 14 participants who provided treatment data reported using steroids during flares.
Related Factors: The frequency for "Stress" has been corrected from 25 to 12, which aligns with the narrative in the text reporting 12 participants (25.5%).
Labeling Error: The category "System and Tropical" has been corrected to "Systemic and Topical".

Methodologically, the authors correctly state that multivariable regression is exploratory with n=47, but the paper still leans too heavily on multivariable interpretations as if they were stable. Even with attempts to “minimize factors,” the regression section reports several models across multiple QoL domains plus anxiety and depression, which increases the risk of overfitting and selective significance in a small dataset. The added 95% CIs help, but the manuscript should go further: tighten the narrative so that regression findings are explicitly framed as hypothesis-generating and avoid presenting them as “key factors” with near-interventional implications.

Response: We agree with the reviewer's important methodological point. We have substantially revised the narrative around the multivariate analyses to emphasize their exploratory and hypothesis-generating nature, and to avoid overinterpretation.

In the introduction to Section 3.4, we now explicitly state: "These multivariate analyses are explicitly exploratory and hypothesis-generating; they should not be interpreted as identifying definitive causal 'key factors'."

In the conclusion of Section 3.4.7, we reinforce this: "It is important to note that these multivariate models… were considered strictly exploratory and hypothesis-generating."

A deeper problem is that parts of the regression interpretation are directionally inconsistent with the reported coefficients. In the self-perceived QoL model, stress and allergy are described as “adversely affecting” QoL, yet the B coefficients shown are positive, indicating that, as coded, those variables would be associated with higher, not lower, QoL. That contradiction strongly suggests either (a) coding direction is reversed and not described, (b) the narrative is incorrect, or (c) the sign was copied incorrectly. This must be reconciled because it directly affects the manuscript’s practical takeaway (e.g., whether stress is linked to worse QoL in this dataset). Until the authors resolve the sign/coding problem and ensure the text matches the tables, the regression results cannot be trusted.

Response: The reviewer is absolutely correct. We sincerely apologize for this error. The regression coefficient for 'stress' in the self-perceived QoL model was incorrectly described as positive. It has been corrected to show the proper negative association: "Self- perceived QoL was adversely affected by… stress (B = -0.538… p = 0.002)". This aligns with the interpretation that higher stress is associated with poorer self-perceived QoL.

The measurement description also needs tightening. The HADS section describes item responses as a “3-point Likert scale” while simultaneously stating scoring from 0 to 3, which implies four response options; the anchors provided (“never” to “always”) also read like generic placeholders rather than the scale’s actual item-dependent response formats. This doesn’t invalidate the data, but it is incorrect instrument reporting and invites reviewer skepticism. Likewise, the “episodes per year” definition is now clearer, which is good, but it remains a subjective severity proxy; without objective or validated patient-reported severity (e.g., POEM) or clinician severity (e.g., EASI/SCORAD), the paper still cannot separate psychological distress driven by active/severe disease from distress that is partly independent of disease activity. The limitations state this, but the Discussion should more explicitly caution that observed associations could be confounded by unmeasured severity.

Response: We thank the reviewer for pointing out these needed clarifications.

HADS Scale Description: We have corrected the description in Section 2.3.2 to accurately reflect a "4-point Likert scale (0–3)".

Unmeasured Severity Confounding: As suggested, we have added a stronger caution in the Discussion (Limitations section): "Consequently, the reported links between psychological distress, self-reported factors, and QoL may be confounded by unmeasured disease severity."

Finally, the manuscript’s framing still overshoots the sampling reality. The study uses convenience and snowball sampling, excludes participants with diagnosed mental health conditions, and relies on a predominantly young, highly educated cohort. These choices narrow generalizability and likely bias estimates of distress and QoL in unknown directions. The revised text acknowledges bias, but the title and conclusion should be kept modest and clearly positioned as preliminary evidence in a specific community-connected cohort rather than implying broader population inference.

Response: We agree and have tempered the framing of our study's implications to better reflect its methodological context.

Title: The title has been revised to: "Psychological Distress and Quality of Life in a Community-Based Sample of Adults with Atopic Dermatitis: A Cross-Sectional Exploratory Study".

Conclusion: The conclusion now explicitly states that findings are preliminary and context-specific: "…these findings should be interpreted as preliminary evidence specific to this group and require confirmation in larger, more representative cohorts using longitudinal designs."

Reviewer 2 Report

Comments and Suggestions for Authors

The revisions made by the authors to the manuscript render it suitable for publication.

Author Response

The revisions made by the authors to the manuscript render it suitable for publication.

Reply: Thank you very much for your valuable comments to improve our manuscript's quality for publication.