Review Reports - Beyond Screen Time and Emotion Regulation: Social Trust as a Structural Pathway to Perceived Well-Being—A Competing-Models Analysis Among Chinese Youth

Round 1

Reviewer 1 Report

Comments and Suggestions for Authors

Thank you for the opportunity to review Beyond Screen Time and Emotion Regulation: Social Trust as a Social Determinant of Digital Well-Being—Evidence from Competing Models Analysis among Chinese Young People.

Overall, the article makes an important contribution and advances understanding of the mechanisms underlying digital well-being from a novel perspective. However, there are several concerns that should be addressed prior to publication. Please see my comments below.

The title and manuscript use the phrase “young people.” A more accurate characterization would be late adolescents to adults.

Abstract

Line 11: “digital well-being policy” appears to be a misuse of the term; “interventions” may be more appropriate.
Line 18: The reported beta is −.03. Although statistically significant, this represents a small effect size.
Line 21: The sentence beginning “a competing directional specification...” should be simplified, as it is unclear which directional specification is being referenced.

Introduction / Early Sections

Lines 38–39: The term “monotonic” used to describe the relationship between screen time and well-being is overly technical and should be explained.
Lines 42–43: The manuscript overuses em dashes. The authors note the use of AI in writing, and this is a common feature of AI-generated text. In many instances, em dashes can be replaced with commas or semicolons. A full manuscript review is recommended.
Lines 58–59: The authors refer to contemporary well-being research but cite sources from 1989, 1998, and 2014. More recent references are needed.
Line 64: The phrase “…highly correlated with negative emotional” appears incomplete; a word is missing.
Lines 67–68: Arrows should be removed from the text.
Lines 95 and 97: There are spacing issues around full stops.
Line 109: The phrase “global trust infrastructure” is unclear and should be reconsidered.

Conceptualization and Methods

Line 162: Arnett (2000) defines emerging adulthood as spanning the late teens through the mid-20s (approximately ages 18–25), not through age 35. Therefore, defining adulthood as ages 16–35 is inaccurate. The authors should review the manuscript, starting with the title, to ensure consistent and accurate age definitions.
Line 167: The authors state that logically inconsistent or outlier responses were excluded. The criteria used to identify outliers should be specified (e.g., standard deviation thresholds).
Lines 170–173: The use of multiple imputation is mentioned, but it is unclear which variables contained missing data. Earlier, the authors state that entries with missing data on key variables were excluded, which appears inconsistent.
Lines 175–195: Screen time is operationalized as total internet usage across mobile devices and computers. This differs from Twenge et al. (2018), who conceptualize screen time as a composite that includes multiple dimensions such as social media use, smartphone use, texting, gaming, and general internet browsing. The current operationalization may include work-related internet use, which could contribute to differences from prior findings. The authors reference Twenge et al. in the introduction, so this discrepancy should be addressed.
Line 199: The term “contemporary” should be removed when describing well-being theory, as the cited sources are from 2001 and 2002.

Measurement Issues

Lines 217–225: Social trust is operationalized as trust in neighbors, local government officials, and doctors. This excludes key aspects of interpersonal trust, particularly friendships and close peer relationships, which are central to everyday social trust. The construct is skewed toward institutional trust, with limited representation of interpersonal trust. Additionally, combining trust in government officials, doctors, and neighbors into a single factor may be theoretically imprecise, as these forms of trust do not necessarily covary.
Lines 236–241: Home life is operationalized as time spent on daily chores and caregiving. The authors interpret higher values as indicating stronger family bonds and protective mental health effects. This assumption is highly questionable. It is disproportionately women who spend more time on household chores and caregiving responsibilities, and these are not inherently protective factors. A recent systematic review in The Lancet Public Health (Grangel et al., 2025) found that caregiving has a small to moderately negative effect on the mental health of adolescent and young carers, with variation by sex, ethnicity, care intensity, duration, and type of tasks. A large 2025 study in the Journal of Research on Adolescence (Armstrong-Carter et al.) involving over 49,000 students showed that caregiving adolescents reported significantly worse mental health outcomes—including higher anxiety, stress, depression, and suicidality—and lower academic performance compared to non-caregiving peers. Regarding household chores specifically, Molarius et al. (2025), using a Swedish sample, found that experiencing domestic work as burdensome explained 47% of the prevalence of depression in women, with no independent association observed in men.

The operationalization of these two key variables—social trust and home life—is highly problematic, and these shortcomings must be acknowledged not only in the limitations section but also in interpreting the study’s findings.

Borgmann is cited in the text but not included in the reference list.

Tables and Figures

Table 1: The categorization of age groups is problematic. Individuals aged 16–17 do not constitute early adolescence. Age groupings should be revised in line with established adolescence literature.
Table 4: Given the operationalization of home life, the reported positive correlation with negative emotion is not surprising.
Table 6: The item “I think it’s difficult o do anything” is missing a “t” in “to.”
Table 7: Home life is missing as a latent variable.
SEM figures: Standard SEM path diagram conventions are not followed. Observed variables should be represented as rectangles, latent variables as ovals, single-headed arrows for paths, and curved double-headed arrows for covariances. The figures should be revised accordingly.

Results

Line 351: The section heading refers to testing the “trust-first versus emotion-first pathway,” but the first model presented is the emotion-first pathway. The order should match the heading for clarity.
Line 352: The term “indirect association” is introduced immediately after discussing a direct association, without clear explanation. This section should be rewritten for clarity.
Line 370: The authors report that the social trust pathway shows the strongest mediation (87% stronger than the home life path). Given the concerns about construct operationalization, the robustness of this conclusion is difficult to assess.

Discussion
Overall, this section is well written, with a few issues noted below:

Line 448: The authors refer to “Chinese young adults,” but the sample is not limited to young adults.
Line 449: The term “digital health policy” is used again without clear definition or context.
Line 452: “Trust erosion” is introduced without prior discussion in the introduction or literature review. This concept should be established earlier.
Lines 507–511: The discussion links digital time use to reduced offline social activities (e.g., sports, community engagement, informal neighborhood interactions), but these variables were not measured within the social trust construct used in this study.

The authors do a good job acknowledging the limitations of their study.

Author Response

Comment 1 [Abstract, Line 11]:

“Digital well-being policy” appears to be a misuse of the term; “interventions” may be more appropriate.

Response 1:

Thank you for pointing this out. We agree with this comment. Therefore, we have replaced "policy" with "interventions".

Comment 2 [Abstract, Line 18]:

The reported beta is −.03. Although statistically significant, this represents a small effect size.

Response 2:

The reviewer's point is well taken. We have candidly acknowledged the modest absolute magnitude of all indirect effects in the Limitations section [Line 530–53]. We would nonetheless note, as context for interpreting the comparative claim, that the social trust pathway's indirect effect (β = −0.030) is approximately twice the magnitude of the home-life pathway (β = −0.011), suggesting that while effect sizes are uniformly small across the model, social trust operates as the relatively dominant mediating mechanism. [Line 18]

Comment 3 [Abstract, Line 21]:

The sentence beginning “a competing directional specification...” should be simplified, as it is unclear which directional specification is being referenced.

Response 3:

Agreed. In consultation with feedback from multiple reviewers, this passage has been removed entirely from the abstract.

Comment 4 [Introduction, Lines 38–39]:

The term “monotonic” used to describe the relationship between screen time and well-being is overly technical and should be explained.

Response 4:

We agree with the reviewer that the term 'monotonic' was overly technical in the original context. To enhance clarity for a broader audience, we have replaced it with a more descriptive explanation: 'This perspective presupposes a monotonic decline in well-being as screen time increases.' This revision ensures the relationship is easily understood without losing its conceptual precision [Lines 37–39].

Comment 5 [Introduction, Lines 42–43]:

The manuscript overuses em dashes. The authors note the use of AI in writing, and this is a common feature of AI-generated text. In many instances, em dashes can be replaced with commas or semicolons. A full manuscript review is recommended.

Response 5:

We thank the reviewer for this stylistic observation. We have addressed the excessive use of dashes throughout the manuscript. By incorporating participial phrases and logical conjunctions, we have restructured these sentences to enhance syntactic variety and improve the overall narrative flow [Line 42–43].

Comment 6 [Introduction, Lines 58–59]:

The authors refer to contemporary well-being research but cite sources from 1989, 1998, and 2014. More recent references are needed.

Response 6:

Agreed. The citation cluster at Lines 58–59 has been updated to include more recent empirical and theoretical work. Specifically, we now cite Lomas et al. (2023, 2025) and Pronk et al. (2025), whose social-ecological frameworks reflect the current direction of the field [Lines 58–59].

Comment 7 [Introduction, Line 64]:

The phrase “…highly correlated with negative emotional” appears incomplete; a word is missing.

Response 7:

Corrected. The phrase now reads "…highly correlated with negative emotions" [Line 64].

Comment 8 [Introduction, Lines 67–68]:

Arrows should be removed from the text.

Response 8:

Agreed. The sentence has been revised to read: "Research from the United States documents that screen use among youth contributes to emotional distress, mediated by decreased physical activity and impaired sleep quality." All notational arrows have been removed from the running text [Lines 67–69].

Comment 9 [Introduction, Lines 95 and 97]:

There are spacing issues around full stops.

Response 9:

Corrected at both locations [Lines 95 and 97].

Comment 10 [Introduction, Line 109]:

The phrase “global trust infrastructure” is unclear and should be reconsidered.

Response 10:

Agreed. This phrase has been replaced with the more precise "social connection and trust," which directly connects to the constructs examined in the study [Lines 111–112].

Comment 11 [Methods, Line 162]:

Arnett (2000) defines emerging adulthood as spanning the late teens through the mid-20s (approximately ages 18–25), not through age 35. Therefore, defining adulthood as ages 16–35 is inaccurate. The authors should review the manuscript, starting with the title, to ensure consistent and accurate age definitions.

Response 11:

The reviewer raises a valid and important definitional concern. Rather than stretching the developmental category of "emerging adulthood" beyond its established boundaries, we have standardised the manuscript-wide terminology to "youth," anchored to China's official CPC Central Committee (2017) definition of youth as ages 14–35. Our analytic sample covers ages 16–35, consistent with CFPS self-report data availability. The age of 16 is retained as the lower bound to fully leverage available self-report records; the sample distribution (91.4% of participants aged 18–35) is reported descriptively in the Methods section without conflating it with the developmental construct of emerging adulthood. All previously inconsistent uses of "young adults" have been harmonised [Lines 163–168].

Comment 12 [Methods, Line 167]:

The authors state that logically inconsistent or outlier responses were excluded. The criteria used to identify outliers should be specified (e.g., standard deviation thresholds).

Response 12:

Agreed. The exclusion criterion has been operationalised explicitly: observations were excluded where reported screen time exceeded 20 hours per day. Given physiological time constraints (sleep, nutrition, and basic daily functioning), values exceeding 20 hours represent biologically implausible responses that most likely reflect data-entry error rather than genuine behaviour. This threshold is now stated precisely in the Methods [Lines 171–172].

Comment 13 [Methods, Lines 170–173]:

The use of multiple imputation is mentioned, but it is unclear which variables contained missing data. Earlier, the authors state that entries with missing data on key variables were excluded, which appears inconsistent.

Response 13:

We agree with the comment regarding the handling of missing data. We have now provided comprehensive details on this procedure in the revised manuscript and Supplementary Table 1, which summarizes the missingness distribution for all key variables. To maintain data integrity and maximize statistical power, we have elaborated on the rationale for employing Multiple Imputation (MI). Furthermore, technical details of the MI procedure have been added to ensure the robustness of our statistical inferences. [Line 174-183]

We recognize that the original phrasing 'missing data on any key study variables' was overly restrictive and potentially misleading. In the revised manuscript, we have corrected this criterion to: 'simultaneous missingness on more than three of the five key study variables.' This refinement was implemented to better balance data integrity with sample representativeness.

Comment 14 [Methods, Lines 175–195]:

Screen time is operationalized as total internet usage across mobile devices and computers. This differs from Twenge et al. (2018), who conceptualize screen time as a composite that includes multiple dimensions such as social media use, smartphone use, texting, gaming, and general internet browsing. The current operationalization may include work-related internet use, which could contribute to differences from prior findings. The authors reference Twenge et al. in the introduction, so this discrepancy should be addressed.

Response 14:

This is a substantively important point. We have added explicit language in the Methods acknowledging that our operationalisation captures cumulative duration of mobile and computer use and does not distinguish by content type or purpose (recreational versus occupational). This differs from the multidimensional, content-differentiated measures used by Twenge et al. (2018). We cite Bell et al. (2015) and Santos et al. (2023) to contextualise the comparatively modest effect sizes observed in our study, consistent with broader evidence that the direct impact of aggregate internet use on well-being is typically small. This measurement limitation is also discussed in the Limitations section. Supporting data from the Pew Research Center (95% of youth use smartphones; 85% use computers for internet access) are cited to justify our operationalisation as ecologically representative of youth digital behaviour [Lines 189 and 518–519].

Comment 15 [Methods, Line 199]:

The term “contemporary” should be removed when describing well-being theory, as the cited sources are from 2001 and 2002.

Response 15:

"Contemporary" has been removed. The sentence now situates the theoretical framework within the tradition it represents, without overclaiming temporal currency for decade-old citations [Line 207].

Comment 16 [Measurement, Lines 217–225]:

Social trust is operationalized as trust in neighbors, local government officials, and doctors. This excludes key aspects of interpersonal trust, particularly friendships and close peer relationships, which are central to everyday social trust. The construct is skewed toward institutional trust, with limited representation of interpersonal trust. Additionally, combining trust in government officials, doctors, and neighbors into a single factor may be theoretically imprecise, as these forms of trust do not necessarily covary.

Response 16:

We thank the reviewer for this substantive concern, which goes to the heart of the study's construct validity. We address it on three levels: empirical, theoretical, and interpretive.

Empirically, EFA applied to the full six-item CFPS trust scale retained three items (trust in neighbours, local government officials, and doctors; Cronbach's α = 0.681; factor loadings in Table 5). We acknowledge that α = 0.681 falls at the lower boundary of conventional acceptability (Nunnally, 1978). In the context of secondary survey data this internal consistency value reflects the heterogeneity inherent in a composite that intentionally spans multiple trust domains rather than a unidimensional affective state, where item selection is constrained by the instrument rather than the construct. We have added this clarification to the Limitations section.

Theoretically, item retention was guided by Delhey and Newton's (2003) distinction between particularised and generalised trust. Trust in neighbours indexes proximate generalised trust; trust in local officials captures civic-institutional trust; trust in doctors captures professional-institutional trust routinely encountered in daily life [Lines 225–233]. That these three items co-load on a single factor is itself an empirical signal: in the post-COVID Chinese context, where state legitimacy and community cohesion co-varied under unified pandemic governance (Fang et al., 2023), generalised trust in proximate institutions may have a shared underlying structure that a single-factor solution appropriately captures.

Interpretively, we fully accept the reviewer's point that peer and friendship trust is absent from our operationalisation. This is a consequential limitation. The CFPS instrument does not include peer trust items, and we are therefore measuring an institutional-proximate form of social trust rather than the interpersonal peer trust most salient to youth well-being. We have now foregrounded this as the first substantive limitation, and qualified all discussion of the "social trust pathway" accordingly: our findings concern specifically the civic-institutional trust register, which may underestimate the full salience of the structural pathway in youth populations where peer trust is the dominant form [Line 522–528].

Comment 17 [Measurement, Lines 236–241]:

Home life is operationalized as time spent on daily chores and caregiving. The authors interpret higher values as indicating stronger family bonds and protective mental health effects. This assumption is highly questionable. It is disproportionately women who spend more time on household chores and caregiving responsibilities, and these are not inherently protective factors. A recent systematic review in The Lancet Public Health (Grangel et al., 2025) found that caregiving has a small to moderately negative effect on the mental health of adolescent and young carers, with variation by sex, ethnicity, care intensity, duration, and type of tasks. A large 2025 study in the Journal of Research on Adolescence (Armstrong-Carter et al.) involving over 49,000 students showed that caregiving adolescents reported significantly worse mental health outcomes—including higher anxiety, stress, depression, and suicidality—and lower academic performance compared to non-caregiving peers. Regarding household chores specifically, Molarius et al. (2025), using a Swedish sample, found that experiencing domestic work as burdensome explained 47% of the prevalence of depression in women, with no independent association observed in men.

Response 17:

We wish to go one step further than the revision described above, because the reviewer's concern raises a question that language revision alone cannot resolve: if the dominant evidence suggests that caregiving and domestic labour burden are associated with worse mental health outcomes in youth, what should we make of a positive zero-order association between home life time and negative emotion (Table 4) alongside a mediated pathway in which home life features as a route from screen time to well-being?

We have removed the phrase "Higher values indicate greater home life engagement" and any language suggesting a uniformly positive valence to this variable. The revised text characterises "home life" as an objective behavioural time-allocation indicator, capturing the proportion of waking hours devoted to domestic activities and caregiving. A higher value indicates only that more time is spent in the domestic sphere; it carries no inherent positive or protective implication [Lines 246–247].

To make the directional logic fully transparent: the SEM path from home life to well-being is negative (β = -0.016, p ＜0.001), indicating that greater time allocated to domestic and caregiving activities is associated with lower perceived well-being. This direction is consistent with the recent caregiving burden literature (Grangel et al., 2025; Armstrong-Carter et al., 2025). Despite being statistically significant, the path through family life shows a relatively limited explanatory power in the relationship between screen time and well-being. This modest indirect association suggests that while the displacement of family time indeed occurs, it is not the primary driver behind fluctuations in well-being. We have made this directional logic explicit in the Results section [Lines 370-372].

Comment 18 [Measurement]:

Response 18:

Agreed entirely. Measurement limitations for both constructs are now woven into the interpretation of the relevant results (Results section) and consolidated in an expanded Limitations paragraph. We are careful to frame findings as associative patterns that depend on the particular operationalisation employed, and to note that alternative measurement approaches — particularly for social trust, which would ideally include close peer relationships — might yield somewhat different effect estimates [Lines 521–528].

Comment 19 [Tables, Table 1]:

The categorization of age groups is problematic. Individuals aged 16–17 do not constitute early adolescence. Age groupings should be revised in line with established adolescence literature.

Response 19:

Agreed. The 16–17 group has been relabelled "late adolescence" and the 18–25 group as "emerging adulthood," consistent with standard developmental classifications (Arnett, 2000). These corrections have been applied in Tables 1 and 3 [Lines 268 and 278].

Comment 20 [Tables, Table 4]:

Given the operationalization of home life, the reported positive correlation with negative emotion is not surprising.

Response 20:

Thank you for pointing this out. Given the operationalization of the home life variable which captures the objective time young people allocate to family-oriented activities rather than their subjective experience. The observed positive association with negative emotion is theoretically interpretable and not unexpected.

Comment 21 [Tables, Table 6]:

The item “I think it’s difficult o do anything” is missing a “t” in “to.”

Response 21:

Corrected. The item now reads "I think it's difficult to do anything" [Line 307].

Comment 22 [Tables, Table 7]:

Home life is missing as a latent variable.

Response 22:

We would like to clarify that home life is specified in the model as an observed composite variable rather than a latent construct. It is therefore represented as a rectangle in the SEM path diagram (as an observed variable).

Comment 23 [Tables, SEM Figures]:

Standard SEM path diagram conventions are not followed. Observed variables should be represented as rectangles, latent variables as ovals, single-headed arrows for paths, and curved double-headed arrows for covariances. The figures should be revised accordingly.

Response 23:

Agreed. Both SEM path diagrams have been redrawn in accordance with LISREL/AMOS conventions.

Comment 24 [Results, Line 351]:

The section heading refers to testing the “trust-first versus emotion-first pathway,” but the first model presented is the emotion-first pathway. The order should match the heading for clarity.

Response 24:

The presentation order has been corrected. Trust-pathway findings are now reported first, consistent with the sequence implied by the heading and the theoretical priority given to the structural pathway throughout the paper [Line 351].

Comment 25 [Results, Line 352]:

The term “indirect association” is introduced immediately after discussing a direct association, without clear explanation. This section should be rewritten for clarity.

Response 25:

The transition has been rewritten. The revised text now introduces the distinction between direct and indirect pathways explicitly before reporting effect estimates, uses consistent terminology throughout, and includes a brief conceptual bridge that guides the reader from the direct-path finding to the mediated pathways [Lines 343–374].

Comment 26 [Results, Line 370]:

The authors report that the social trust pathway shows the strongest mediation (87% stronger than the home life path). Given the concerns about construct operationalization, the robustness of this conclusion is difficult to assess.

Response 26:

Agreed. We have revised the presentation of results to adopt more cautious language throughout [Line 369].

Comment 27 [Discussion, Line 448]:

The authors refer to “Chinese young adults,” but the sample is not limited to young adults.

Response 27:

Corrected. "Youth" is now used consistently throughout the manuscript in accordance with the terminological revision described in the Summary [passim].

Comment 28 [Discussion, Line 449]:

The term “digital health policy” is used again without clear definition or context.

Response 28:

"Digital health policy" has been replaced with "digital health interventions" [Line 414].

Comment 29 [Discussion, Line 452]:

“Trust erosion” is introduced without prior discussion in the introduction or literature review. This concept should be established earlier.

Response 29:

Thank you for this suggestion. We have incorporated a discussion of trust erosion into the introduction to better contextualize the theoretical background and strengthen the rationale for the study [Lines 91–95].

Comment 30 [Discussion, Lines 507–511]:

The discussion links digital time use to reduced offline social activities (e.g., sports, community engagement, informal neighborhood interactions), but these variables were not measured within the social trust construct used in this study.

Response 30:

The reviewer correctly identifies a slippage between the variables measured and the mechanisms invoked in the discussion. The text has been revised to read: "First, opportunity-cost displacement: time spent in digital environments reduces sustained neighbourhood interactions and participation in local civic life." This revision more explicitly connects the mechanism of opportunity cost displacement to the trust in neighbors within the social trust construct employed in this study, thereby strengthening the theoretical grounding of the discussion [Lines 495–496].

Reviewer 2 Report

Comments and Suggestions for Authors

The study is well-intentioned and designed. The workflow is also clear overall. Several key aspects need strong clarifications.

1. The concept of digital well-being. It is not accepted to use "digital well-being" to represent the link between digital use and well-being. If you insist, cite those who did this.

2. The title. "Social determinant of digital well-being" is doing two things wrong at once—"determinant" overclaims causation the design can't support, and "digital well-being" as a construct is underspecified. Borrowing the "social determinants of health" framing sounds authoritative, but it also invites scrutiny from that literature, which uses "determinant" in a very specific causal-structural sense. The paper probably can't survive that scrutiny.

3. The emotion pathway. The study examined the role of depressive emotion in channeling the relationship between digital use and well-being. Well-being was captured by subjective well-being and psychological well-being. In principle, emotion is a key component of, instead of an antecedent of subjective well-being. If you insist, try harder to persuade readers like me, who are also doing subjective well-being research.

4. Why the competing directional model analysis? Any justifications from prior research? It seems to me to be a distraction. After all, you have done much effort on elaborating on the direction from digital use to well-being, not vice versa.

5. It is especially curious to consider the direct path from digital use to well-being as negligible. The coefficient was 0.05, larger than any of the indirect pathways in magnitude. Sometimes, we do treat a coefficient as negligible for a combination of statistical significance and small value. In your case, the coefficient is marginally significant and comparatively large in value. Moreover, the direct pathway was positive, which is indeed interesting if you treat it as non-negligible.

6. Quite a few in-text citations cannot be found in the reference section.

Author Response

Comment 1:

The concept of digital well-being. It is not accepted to use "digital well-being" to represent the link between digital use and well-being. If you insist, cite those who did this.

Response 1:

The reviewer is correct, and the distinction is important. "Digital well-being" in the psychological and human-computer interaction literature refers to a specific subjective state — the experience of maintaining a sense of balance, control, and meaning within digital environments (Gui et al., 2017; Vanden Abeele, 2021) — rather than serving as a shorthand for any association between technology use and psychological outcomes. Using it in the latter sense overextends the construct.

Accordingly, we have replaced "digital well-being" throughout the manuscript with contextually precise alternatives: "well-being in digital contexts" where the focus is on psychological outcomes among digitally-engaged youth; "the screen time–well-being relationship" where the focus is on the empirical association; and "well-being" alone where no digital-specific framing is required. These changes are applied consistently from the title through to the discussion.

Comment 2:

The title. "Social determinant of digital well-being" is doing two things wrong at once—"determinant" overclaims causation the design can't support, and "digital well-being" as a construct is underspecified. Borrowing the "social determinants of health" framing sounds authoritative, but it also invites scrutiny from that literature, which uses "determinant" in a very specific causal-structural sense. The paper probably can't survive that scrutiny.

Response 2:

We agree unreservedly. Both problems have been corrected. The manuscript title has been revised to:

"Beyond Screen Time and Emotion Regulation: Social Trust as a Structural Pathway to Perceived Well-Being — A Competing Models Analysis Among Chinese Youth."

The word "pathway" accurately reflects the associative, mediational logic of a cross-sectional SEM design. The construct language is now precise. The "social determinants of health" framing has been entirely removed.

Comment 3:

The emotion pathway. The study examined the role of depressive emotion in channeling the relationship between digital use and well-being. Well-being was captured by subjective well-being and psychological well-being. In principle, emotion is a key component of, instead of an antecedent of subjective well-being. If you insist, try harder to persuade readers like me, who are also doing subjective well-being research.

Response 3:

The reviewer is entirely correct that within Diener's tripartite framework (1984), negative affect constitutes a core component of subjective well-being — measured canonically by instruments such as the PANAS. Modelling affect as an antecedent of SWB in that framework would indeed introduce circularity.

However, the negative emotions construct in our study is operationalised using items drawn from the Center for Epidemiologic Studies Depression Scale (CES-D; Radloff, 1977), not from an affect balance instrument. The CES-D items — "I felt down," "I felt it was difficult to do anything," "I felt lonely," "I felt sad," "I felt I could not go on" — capture a qualitatively distinct construct: depressive symptomatology characterised by helplessness, functional impairment, interpersonal withdrawal, and despair. These phenomenological features extend well beyond the transient negative mood states indexed by PANAS items (e.g., "hostile," "irritable," "upset").

This distinction is not merely conceptual. As reported in Table 8, the square root of the average variance extracted (AVE) for negative emotions exceeds its correlations with both well-being constructs, confirming adequate discriminant validity: in our data, negative emotions and well-being are empirically distinguishable rather than overlapping.

Furthermore, positioning CES-D-based depressive symptoms as a predictor or mediator of life satisfaction and psychological well-being has substantial precedent in the literature. He et al. (2026), Hu and Tan (2025), and Yang et al. (2022) have modelled depressive symptoms in precisely this mediating role without attracting the circularity concern the reviewer raises, because those studies, like ours, are not modelling negative affect as SWB is constituted but rather depressive symptomatology as a psychopathological process that precedes and constrains well-being evaluations.

Taken together, we believe that the conceptual distinction between CES-D-based depressive symptomatology and PANAS-type negative affect, the empirical evidence of discriminant validity in our data, and the established precedent in the literature collectively provide a sound basis for treating negative emotions as a mediator rather than a component of well-being in our model. We hope these clarifications adequately address the reviewer's concern, and we remain open to further suggestions.

Reference：

He, J., Hu, Y., Wu, X., Yin, J., Cai, J., & Jin, Z. (2026). Impact of life satisfaction on chronic diseases in aging populations: Exploring the mediating effects of depressive symptoms and frailty. Journal of Affective Disorders, 396, 120863. https://doi.org/https://doi.org/10.1016/j.jad.2025.120863

Hu, J., & Tan, C. (2025). The impact of internet use on the subjective well-being of older adults: The mediating role of mental health. PLoS One, 20(10), e0335985. https://doi.org/10.1371/journal.pone.0335985

Radloff, L. S. (1977). The CES-D Scale: A self-report depression scale for research in the general population. Applied Psychological Measurement, 1(3), 385-401. https://doi.org/10.1177/014662167700100306

Yang, Y., Cuffee, Y. L., Aumiller, B. B., Schmitz, K., Almeida, D. M., & Chinchilli, V. M. (2022). Serial Mediation Roles of Perceived Stress and Depressive Symptoms in the Association Between Sleep Quality and Life Satisfaction Among Middle-Aged American Adults. Front Psychol, 13, 822564. https://doi.org/10.3389/fpsyg.2022.822564

Comment 4:

Why the competing directional model analysis? Any justifications from prior research? It seems to me to be a distraction. After all, you have done much effort on elaborating on the direction from digital use to well-being, not vice versa.

Response 4:

One consequence of removing the reversed-directionality analysis warrants transparent acknowledgement: the phrase "Competing Models Analysis" in the revised title now refers exclusively to the comparison of two structural pathways (social trust versus negative emotions as mediating routes from screen time to well-being), rather than the original design which also compared opposing causal directions.

We accept this critique. In retrospect, the competing-directional-specification analysis added complexity without corresponding theoretical necessity, given that the paper's core contribution lies in comparing structural versus emotional pathway magnitudes within the screen-time-to-well-being direction. The directional analysis has been removed. The manuscript now focuses exclusively on the theory-driven pathway from digital engagement to well-being outcomes via social trust, negative emotions, and home life, which is where the theoretical and empirical weight of the paper resides.

Comment 5:

It is especially curious to consider the direct path from digital use to well-being as negligible. The coefficient was 0.05, larger than any of the indirect pathways in magnitude. Sometimes, we do treat a coefficient as negligible for a combination of statistical significance and small value. In your case, the coefficient is marginally significant and comparatively large in value. Moreover, the direct pathway was positive, which is indeed interesting if you treat it as non-negligible.

Response 5:

The reviewer's observation is analytically acute, and we have substantially revised our treatment of this finding. We agree that the original framing was indefensible, and we have corrected it in three ways.

First, we have removed all language characterising the direct path as "negligible." A standardised coefficient of β = 0.05 is not trivial, positive, statistically significant, and larger in absolute magnitude than any individual indirect association. To dismiss it as negligible was to suppress a substantively important result.

Second, we identify the pattern as a case of inconsistent mediation (MacKinnon et al., 2000; Tzelgov & Henik, 1991), defined by a positive direct effect co-existing with negative indirect effects, yielding a near-zero total bivariate association. Critically, this pattern is not theoretically post-hoc in the present study. We argue it is anticipated by the dual-pathway logic that motivates the paper: digital engagement may simultaneously erode indirect pathways while providing direct psychological gratification or compensatory connection. Uses-and-gratifications theory (Katz et al., 1973) and the compensatory internet use framework (Kardefelt-Winther, 2014) both provide prior theoretical warrant for a positive direct association.

Third, we note that it is precisely the suppression structure that makes pathway decomposition analytically necessary. If screen time's net effect on well-being were strongly positive or negative, a mediation analysis would quantify the mechanisms of that effect. When the total effect is near zero due to offsetting pathways, mediation analysis reveals a more important finding: screen time is not benign, but its harms and benefits partially cancel at the population level. This reframing has been incorporated into the Results [Lines 334–339].

Reference:

Kardefelt-Winther, D. (2014). A conceptual and methodological critique of internet addiction research: Towards a model of compensatory internet use. Computers in Human Behavior, 31, 351–354. https://doi.org/10.1016/j.chb.2013.10.059

Katz, E., Blumler, J. G., & Gurevitch, M. (1973). Uses and gratifications research. Public Opinion Quarterly, 37(4), 509–523. https://doi.org/10.1086/268109

MacKinnon, D. P., Krull, J. L., & Lockwood, C. M. (2000). Equivalence of the mediation, confounding and suppression effect. Prevention Science, 1(4), 173–181. https://doi.org/10.1023/A:1026595011371

Tzelgov, J., & Henik, A. (1991). Suppression situations in psychological research: Definitions, implications, and applications. Psychological Bulletin, 109(3), 524–536. https://doi.org/10.1037/0033-2909.109.3.524

Comment 6:

Quite a few in-text citations cannot be found in the reference section.

Response 6:

We apologise for this oversight. A systematic cross-check of all in-text citations against the reference list has been conducted. All missing entries have been restored and all entries have been verified for completeness and formatting accuracy against the journal's citation style. The reference list in the revised manuscript is internally consistent.

Reviewer 3 Report

Comments and Suggestions for Authors

Thank you for the opportunity to review this manuscript. This study addresses an important and timely topic with a potentially novel focus on social trust as a structural determinant of digital well-being. The use of a large national dataset and a competing pathway framework are notable strengths. However, substantial concerns related to conceptual framing, methodological rigor, causal overinterpretation, measurement validity, and writing clarity must be addressed before the manuscript can be considered for publication. Please see my comments below.

Background:

Line 39, the in-text citation "Chang, 2025," has a question mark. Was it a formatting error? If yes, then it needs to be removed.

Lines 108-117: Referring to China 2022 as a “natural experiment condition” is inappropriate given the cross-sectional observational design.

Lines 130-142: Claims such as “no prior study” and “directly tested” are overstated and should be softened.

Methods:

Lines 156-158: The exclusion of participants with missing key variables, ≥20% missing data, or “abnormal” responses lacks sufficient justification and may introduce selection bias. Please justify exclusion thresholds and discuss how these decisions may affect representativeness.

Lines 170-173: Multiple imputation is mentioned, but critical methodological details (e.g., imputation model variables, missingness assumptions, diagnostic checks) are missing. Provide comprehensive information on the imputation process.

Lines 176-179: Screen time is measured solely through the combined duration of mobile and computer use, without accounting for the type or purpose of digital engagement. Acknowledge limitations of this simplified measure more explicitly.

Results:

Lines 285-290: The near-zero correlation between screen time and well-being raises concerns about the practical significance of subsequent mediation pathways. I would recommend authors to be more cautious interpret indirect effects when total association is negligible.

Lines 299-306: Exclusion of certain trust items (e.g., parents, strangers) appears partially subjective and may influence construct validity. It will be nice to justify factor retention decisions.

Lines 352-356: Null findings for the emotional pathway are used to challenge broader literature too aggressively. I would recommend avoiding overstating contradictions with prior studies, particularly given the cross-sectional design.

Lines 369-373: Interpretation of pathway size comparisons may exaggerate practical significance despite relatively small indirect effects. Emphasize effect size magnitude more cautiously.

Lines 379-418: Sensitivity analyses are extensive but are interpreted with overly strong confirmatory language. So, consider framing sensitivity analyses as supportive rather than definitive.

Discussion:

Lines 447-457: The discussion repeatedly frames social trust as the “primary” mechanism despite cross-sectional data and relatively modest effect sizes. Please temper down the claims and present findings as associative rather than definitive.

Lines 458-467: Statements such as “first study” and “provides that answer” are overly absolute and likely overstated. I would recommend authors use more cautious scholarly language unless it is supported by systematic review evidence.

Lines 486-494: Cultural interpretations regarding Chinese digital ecosystems and trust mechanisms extend beyond directly measured data. Consider providing a clearly distinguished speculative contextual interpretation from empirical findings.

Lines 559-578: While limitations are acknowledged, they are not sufficiently emphasized relative to the manuscript’s strong conclusions. So, expand the limitations discussion, particularly regarding causality, measurement constraints, and residual confounding.

Author Response

Comment 1 [Background, Line 39]:

The in-text citation "Chang, 2025," has a question mark. Was it a formatting error? If yes, then it needs to be removed.

Response 1:

This was a formatting artefact. The rhetorical question has been replaced with a declarative statement: "Recent evidence suggests that the link between screen time and well-being may not be as straightforward as the dominant paradigm assumes (Chang, 2025)." The citation is now embedded in a properly constructed declarative sentence [Lines 38–39].

Comment 2 [Background, Lines 108–117]:

Referring to China 2022 as a “natural experiment condition” is inappropriate given the cross-sectional observational design.

Response 2:

The reviewer is correct. The "natural experiment" language has been removed and replaced with: China in 2022 offers a particularly informative test case. Due to the "dynamic ze-ro-COVID" policy, youth in China experienced prolonged social restrictions, which intensified the dispersion of trust (Fang et al., 2023), while the country maintained the world's highest rate of digital technology adoption (Montag et al., 2018). In this context, high digital penetration coupled with social restrictions allows for the examination of trust mechanisms [Line 113-118].

We take this opportunity to address an interpretive tension that cuts across Reviewer 3's methodological concerns and the paper's policy framing. We use the 2022 CFPS wave because it captures a moment of concentrated social restriction and accelerated digital adoption in China, conditions that amplify the dispersion in trust and screen time that our model requires for adequate statistical power.

Comment 3 [Background, Lines 130–142]:

Claims such as “no prior study” and “directly tested” are overstated and should be softened.

Response 3:

Agreed. Absolute novelty claims are rarely defensible and invite the kind of systematic-review challenge the reviewer anticipates. We have now refined the language to be more cautious and precise. The revised text clarifies that while existing literature has explored these themes, there is a scarcity of research that directly compares structural and emotional mechanisms within a single competing model [Lines 131–134].

Comment 4 [Methods, Lines 156–158]:

The exclusion of participants with missing key variables, ≥20% missing data, or “abnormal” responses lacks sufficient justification and may introduce selection bias. Please justify exclusion thresholds and discuss how these decisions may affect representativeness.

Response 4:

The reviewer's concern is well-founded. The original wording was insufficiently precise and the rationale for each threshold was absent. Three revised and explicitly justified exclusion criteria are now stated in the Methods [Lines 169–173]:

(1) Simultaneous missingness on more than three of the five focal constructs (screen time, social trust, negative emotions, perceived well-being, home life). Criterion rationale: when more than 60% of a respondent's key variable values are unobserved, multiple imputation generates estimates dominated by between-person prediction rather than the individual's own responses, attenuating associations and introducing noise rather than recovering signal.

(2) Total case-level missingness across all measured variables ≥ 20%. Criterion rationale: consistent with widely-used recommendations in survey research literature (Sterne et al., 2009), this threshold represents the upper boundary at which the Missing At Random (MAR) assumption underlying MICE remains plausibly defensible.

(3) Reported screen time > 20 hours per day. Criterion rationale: given physiological constraints on waking hours, daily screen use exceeding 20 hours is biologically implausible and almost certainly reflects data-entry error or careless responding.

Comment 5 [Methods, Lines 170–173]:

Multiple imputation is mentioned, but critical methodological details (e.g., imputation model variables, missingness assumptions, diagnostic checks) are missing. Provide comprehensive information on the imputation process.

Response 5:

Full technical details have been added to the Methods. We have now provided comprehensive details on missing data in the revised manuscript and Supplementary Table 1, which summarizes the missingness distribution for all key variables. [Lines 174–183].

Comment 6 [Methods, Lines 176–179]:

Screen time is measured solely through the combined duration of mobile and computer use, without accounting for the type or purpose of digital engagement. Acknowledge limitations of this simplified measure more explicitly.

Response 6:

An expanded acknowledgement of this limitation is now included in the Limitations section. The text notes that our screen time measure (total duration) does not distinguish passive consumption from active engagement, without accounting for the type or purpose of digital engagement [Lines 518–519].

Comment 7 [Results, Lines 285–290]:

The near-zero correlation between screen time and well-being raises concerns about the practical significance of subsequent mediation pathways. I would recommend authors to be more cautious interpret indirect effects when total association is negligible.

Response 7:

The reviewer's statistical caution is appropriate. We identify the pattern as a case of inconsistent mediation (MacKinnon et al., 2000; Tzelgov & Henik, 1991), defined by a positive direct effect co-existing with negative indirect effects, yielding a near-zero total bivariate association. Critically, this pattern is not theoretically post-hoc in the present study. We argue it is anticipated by the dual-pathway logic that motivates the paper: digital engagement may simultaneously erode indirect pathways while providing direct psychological gratification or compensatory connection. Uses-and-gratifications theory (Katz et al., 1973) and the compensatory internet use framework (Kardefelt-Winther, 2014) both provide prior theoretical warrant for a positive direct association.

In addition, we note that it is precisely the suppression structure that makes pathway decomposition analytically necessary. If screen time's net effect on well-being were strongly positive or negative, a mediation analysis would quantify the mechanisms of that effect. When the total effect is near zero due to offsetting pathways, mediation analysis reveals a more important finding: screen time is not benign, but its harms and benefits partially cancel at the population level. This reframing has been incorporated into the Results [Lines 334–339].

Reference:

Katz, E., Blumler, J. G., & Gurevitch, M. (1973). Uses and gratifications research. Public Opinion Quarterly, 37(4), 509–523. https://doi.org/10.1086/268109

Comment 8 [Results, Lines 299–306]:

Exclusion of certain trust items (e.g., parents, strangers) appears partially subjective and may influence construct validity. It will be nice to justify factor retention decisions.

Response 8:

We thank the reviewer for this substantive concern, which goes to the heart of the study's construct validity. We address it on three levels: empirical, theoretical, and interpretive.

Comment 9 [Results, Lines 352–356]:

Null findings for the emotional pathway are used to challenge broader literature too aggressively. I would recommend avoiding overstating contradictions with prior studies, particularly given the cross-sectional design.

Response 9:

We have rephrased the expression to be more tactful and avoid overstating the contradiction with previous studies. The language has been substantially tempered [Lines 356–361].

Comment 10 [Results, Lines 369–373]:

Interpretation of pathway size comparisons may exaggerate practical significance despite relatively small indirect effects. Emphasize effect size magnitude more cautiously.

Response 10:

The revised text reports the association-size in more measured terms [Lines 369–375].

Comment 11 [Results, Lines 379–418]:

Sensitivity analyses are extensive but are interpreted with overly strong confirmatory language. So, consider framing sensitivity analyses as supportive rather than definitive.

Response 11:

The sensitivity analysis section has been revised throughout to use explicitly supportive rather than confirmatory language. The revised text now focuses on demonstrating the consistency of our results across different model specifications, thereby reinforcing the reliability of our main conclusions without overextending the interpretation [Lines 380–407].

Comment 12 [Discussion, Lines 447–457]:

The discussion repeatedly frames social trust as the “primary” mechanism despite cross-sectional data and relatively modest effect sizes. Please temper down the claims and present findings as associative rather than definitive.

Response 12:

Agree. We have downplayed these claims and regarded the findings as associative rather than definitive [Lines 413–422].

Comment 13 [Discussion, Lines 458–467]:

Statements such as “first study” and “provides that answer” are overly absolute and likely overstated. I would recommend authors use more cautious scholarly language unless it is supported by systematic review evidence.

Response 13:

Agree. Both formulations have been removed [Line 423].

Comment 14 [Discussion, Lines 486–494]:

Cultural interpretations regarding Chinese digital ecosystems and trust mechanisms extend beyond directly measured data. Consider providing a clearly distinguished speculative contextual interpretation from empirical findings.

Response 14:

We have revised the manuscript to ensure that our interpretations remain closely anchored to the empirical results. To strengthen this argument, we have integrated additional empirical evidence “These findings are consistent with existing research: negative emotions do not arise directly, but are rather induced by the erosion of trust resulting from problematic social media use, with trust playing a critical mediating role (Lin et al., 2021). In the Chinese cultural context, a substantial body of research also confirms that the "weakening of trust" is a core antecedent of negative emotions (Li & Yang, 2021; Wang & Zhang, 2025)” [Lines 444–449].

Comment 15 [Discussion, Lines 559–578]:

While limitations are acknowledged, they are not sufficiently emphasized relative to the manuscript’s strong conclusions. So, expand the limitations discussion, particularly regarding causality, measurement constraints, and residual confounding.

Response 15:

The Limitations section has been substantially expanded [Lines 522–533].

Round 2

Reviewer 2 Report

Comments and Suggestions for Authors

I have no further comments. I am glad that the reviewers accept my comments and make corresponding amendments.

Reviewer 3 Report

Comments and Suggestions for Authors

Thank you for addressing my comments thoroughly. I have read the revision and am fully satisfied with the revision.