-->PONE-D-25-65610-->-->Exploring the mediating role of health-related social capital in the association between socioeconomic status and oral frailty risk among community-dwelling older adults: A longitudinal study using the JAGES-->-->PLOS One

Dear Dr. Tadaka,

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PLOS One

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“This study used data from JAGES (the Japan Gerontological Evaluation Study). This study was supported by Grant-in-Aid for Scientific Research (19K02200, 20H00557, 20H03954, 20K02176,20K10540, 20K13721, 20K19534, 21H00792, 21H03196, 21K02001, 21K10323, 21K11108, 21K17302, 21K17308, 21K17322, 22H00934, 22H03299, 22J00662, 22J01409, 22K01434, 22K04450, 22K10564, 22K11101, 22K13558, 22K17265, 22K17364, 22K17409, 23K16320, 23H00449, 23H03117, 23K19793, 23K21500, 23K19796, 23K2790903 from JSPS (Japan Society for the Promotion of Science), Health Labour Sciences Research Grants (19FA1012, 19FA2001, 21FA1012,22FA2001, 22FA1010, 22FG2001), the Research Funding for Longevity Sciences from National Center for Geriatrics and Gerontology (21-20), Research Institute of Science and Technology for Society (JPMJOP1831, †RISTEX, JPMJRX21K6) from the Japan Science and Technology (JST), a grant from Japan Health Promotion & Fitness Foundation, contribution by Department of Active Ageing, Niigata University Graduate School of Medical and Dental Sciences (donated by Tokamachi city, Niigata), TMDU priority research areas grant and National Research Institute for Earth Science and Disaster Resilience.”

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Additional Editor Comments :

Two reviewers have raised several critical concerns, and I ask the authors to respond to all of these points. In addition to the reviewers’ comments, I would like to raise the following issues:

1) It is unclear why the authors concluded that individual‑level social capital mitigates SES‑related disparities in oral frailty risk. Which specific results support this conclusion? In the Introduction, the manuscript refers to “mediation,” and the title also implies a mediating effect. However, the study does not appear to assess mediation in a systematic manner, such as through mediation analysis. Please clarify how the authors evaluated a mediating effect and which findings indicate that social capital mediates, rather than moderates, the association between SES and oral frailty risk.

2) The meaning of the reported sensitivity (0.94) and specificity (0.67) on page 9, line 205, is unclear. Sensitivity and specificity of what measure or classification? Additionally, it is not clear why the oral frailty risk score was calculated using a logistic regression equation rather than using the raw score. Please explain the rationale for this approach.

3) There are instances of overstatement and insufficient description. For example, line 412 states that “In the high‑SES group, community‑level social capital had no significant effect on oral frailty.” However, this appears to apply only to the civic participation score. In the low‑SES group, the social cohesion score also shows no significant effect on oral frailty. In the original manuscript, since the results derived from multiple measurement items are being interpreted conveniently, please clarify the interpretation of the results.

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Reviewers' comments:

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1. Is the manuscript technically sound, and do the data support the conclusions?

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Reviewer #1: Yes

Reviewer #2: Partly

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-->2. Has the statistical analysis been performed appropriately and rigorously? -->

Reviewer #1: Yes

Reviewer #2: No

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Reviewer #1: Yes

Reviewer #2: No

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-->5. Review Comments to the Author

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Reviewer #1: Thank you for the opportunity to review this article.

This longitudinal cohort study examined the mediating role of health-related social capital in the relationship between socioeconomic status (SES) and oral frailty risk among community-dwelling older adults in Japan, using data from the Japan Gerontological Evaluation Study (JAGES). The study is well-structured and based on a large, nationally representative dataset, and the topic is timely. Below are suggestions to improve clarity, transparency, and scientific validity, particularly with respect to observational study reporting guidelines.

First, the paper mostly aligns with STROBE reporting standards, but a few checklist items could be improved for completeness and transparency. The abstract includes a clear summary of the design and findings, though the specific mention of the longitudinal nature of the cohort could be made more explicit. A flow diagram is appropriately provided (Figure on page 35), and descriptive statistics and model outputs are clearly presented (Tables 1–7, pages 14–18). However, information on missing data for each variable (STROBE Item 14b) is not fully reported. It would be helpful to specify the extent of missingness for key variables and how they were handled, particularly given the large initial sample and substantial exclusions during follow-up.

Second, the use of a validated predictive model to estimate oral frailty risk at follow-up is appropriate, but the model itself is based on non-clinical indicators (e.g., swallowing function, chewing difficulty). The distinction between predicted risk and actual clinical diagnosis should be more clearly emphasized, and the outcome measure described consistently throughout the manuscript. This is important for construct validity.

Third, while the SES measure (equivalent income) and social capital dimensions are well defined, the rationale for dichotomizing SES at 2 million yen could be clarified. Additionally, although the authors note adjustment for potential confounders, the selection criteria for covariates and whether any sensitivity analyses were conducted to test alternative specifications (STROBE Item 12e, 17) are not stated. Reporting on robustness checks would strengthen the internal validity of the findings.

Fourth, the stratified analysis by SES adds value, but subgroup sizes and event counts in each group should be reported directly to allow readers to assess precision. Furthermore, interpretation of effect sizes should be presented cautiously, especially given the relatively small differences in mean scores and odds ratios near 1.0 (e.g., OR 0.947, 95% CI: 0.932–0.963 for individual-level social capital).

Fifth, the discussion is generally well reasoned, and limitations are acknowledged. However, some conclusions remain slightly overextended in terms of policy recommendations. For example, while the study supports associations between social capital and oral frailty risk, statements that interventions “may contribute to the sustainability of social security systems” or that social capital “reduces risk” could be rephrased more conservatively, given the observational nature of the data.

Sixth, the manuscript does not report whether any efforts were made to address potential bias, including unmeasured confounding or selection bias due to loss to follow-up (STROBE Item 9, 12d). While the exclusion criteria are thorough, the potential for differential loss should be discussed in more detail.

Seventh, the statistical methods are clearly described, and the models are adjusted for relevant demographic and health-related covariates. Odds ratios and confidence intervals are presented appropriately. However, as noted above, the paper would benefit from sensitivity analyses—such as alternative SES thresholds, interaction terms, or models excluding certain predictors—to assess robustness.

Overall, this is a rigorous and policy-relevant study that offers valuable insight into the intersection of SES, social capital, and aging-related oral health. A few clarifications on methodological decisions and greater transparency in reporting would enhance the manuscript further. I hope the authors find these suggestions helpful.

Reviewer #2: I thank the authors for submitting this manuscript addressing an important and timely topic. The investigation of social capital as a potential buffer against oral frailty risk among older adults with lower socioeconomic status represents a meaningful contribution to the gerontological and public health literature. The use of longitudinal data from a large, well-established cohort study is commendable, and the research question has clear implications for healthy aging policies.

While the manuscript addresses a relevant question with appropriate data, several conceptual and methodological issues require attention before the work can be considered for publication. Most critically, there is a fundamental inconsistency between the stated aim (examining "mediating effects") and the analytical approach employed (stratification by SES). Stratification examines whether the association between social capital and oral frailty differs across SES strata and this is effect modification or moderation, not mediation. Throughout the manuscript, there is no mention of formal mediation analysis techniques (e.g., causal mediation analysis, structural equation modeling). I strongly recommend that the authors either (a) revise the title, aims, and framing to accurately reflect a moderation analysis, or (b) conduct and report proper mediation analyses if the original research question is indeed about mediation pathways.

Additionally, the authors describe their work as a "multilevel approach," which may mislead readers familiar with multilevel (hierarchical) regression models. The current analysis aggregates community-level variables and includes them as individual-level predictors in standard logistic regression, which does not account for the nested data structure (individuals within municipalities). A true multilevel model would better accommodate community-level effects and the clustering of participants. If such modeling was not feasible, this should be acknowledged as a limitation, with recommendations for future research.

Bellow, I present section-specific questions and some comments aimed at helping improve the reporting of the investigation.

ABSTRACT: The phrasing "longitudinal data from the Japan Gerontological Evaluation Study (JAGES) collected in 2019 and 2022" is imprecise. "In 2019 and 2022" denotes two discrete time points, not a range. Consider revising to "collected at baseline (2019) and follow-up (2022)" or similar phrasing that accurately reflects the two-wave design.

INTRODUCTION

--- The manuscript would benefit from a clear definition of "healthy life expectancy," briefly characterizing what is understood as health during this life stage, particularly in the Japanese societal context. Does it mean maintaining the integrity of physiological and psychological capacities? Is it related to individual autonomy and social integration? A brief clarification would anchor the reader's understanding.

--- I am not sure the argument that health inequalities "widen with age and become more pronounced later in life" is clearly stated. Why would that be? The mechanism or evidence supporting this claim should be briefly articulated.

--- Is the problem really "identifying effective and equitable strategies to reduce health disparities regardless of SES," or is it more precisely to account for the influences of SES on said health disparities? The current framing seems to understate the centrality of SES as a structural determinant.

--- How does access to oral health services impact oral frailty in the context of Japan? Do older adults have universal access to dental care? Is SES relevant because only more privileged individuals are granted access to oral health care, or are there other pathways? I believe this aspect of the Japanese healthcare system should be clarified, as it may significantly blur the interpretation of SES effects.

METHODS

---Which 76 municipalities were included? Out of how many total municipalities in Japan? Providing this context would help readers assess the generalizability of findings.

--- Was a baseline sample size estimated a priori? If so, please report the parameters used.

--- How were participants randomized in municipalities with over 5,000 residents? The sampling procedure should be described in sufficient detail for replication.

--- The exclusion criteria appear very strict. While I understand the rationale for ensuring a functionally independent baseline sample, this should be acknowledged when discussing generalizability.

--- What is the exact reasoning behind the differential weighting of community-level indicators of social capital? As currently presented, the different weights seem arbitrary. In the referenced Saito et al. original scale, there is no such weighting suggestion; rather, factor scores are estimated. A clear justification should be presented for the weighting scheme used. Furthermore, in their investigation, Saito et al. use multilevel regression to model exposure and outcomes. Was this not possible in the current investigation? A multilevel model would better account for common community-level variation in social capital and the clustering of individuals within municipalities.

--- Is it possible to specify which chronic diseases were considered and how they were modeled in the regression (e.g., score range, categorization)?

--- It would be helpful if the authors could better describe attrition and missing data at baseline and follow-up, particularly for the 40,000 participants excluded from analysis. Do excluded participants differ systematically from those retained? Of those, how many presented with oral frailty risk at baseline?

--- Could the authors provide better context regarding the equivalent household income variable? Why was the 2 million yen threshold chosen for segregating SES groups? Is this based on minimum wage, an indicator of poverty, or a similar underprivileged situation in Japan? While this may be clear to those familiar with the Japanese economy, for a broader international readership it would be helpful to have additional explanation given that this is the main exposure variable.

RESULTS

--- Table 2 could be consolidated as a first or final row in Table 1, rather than presented as a separate table. Additionally, in terms of descriptive potential, an initial table might be more informative if structured by the outcome variable (oral frailty risk) rather than by SES level.

--- I would recommend reconsidering the presentation of oral frailty incidence by person-years (lines 314–315), as this metric is not explored elsewhere in the manuscript and may confuse readers given the discrete two-wave design.

--- The mean values for community-level indicators are nearly identical across SES groups (indeed, identical for reciprocity), with statistical significance likely driven by sample size rather than meaningful differences. This limited between-group variation in community-level social capital may explain the null findings for community-level moderation effects reported later, a point worth acknowledging in the discussion as a potential limitation of the analytic strategy rather than evidence that community-level social capital is unimportant.

DISCUSSION

--- I believe it would be valuable to add a sentence or two in the discussion regarding the dissipation of sex effects on oral frailty in the high-SES group across all three models. Why does being a woman appear protective among low-SES participants but not among high-SES participants? This pattern warrants interpretation.

--- In a brief PubMed search, I identified several studies with either corroborating or conflicting findings that could strengthen the discussion, particularly regarding the effects of reciprocity and civic participation on oral health outcomes in older adults. I recommend the authors consider engaging with the following works:

------ Community Dent Oral Epidemiol. 2023 Oct;51(5):879-886. doi: 10.1111/cdoe.12780.

------ PLoS One. 2015 May 18;10(5):e0125557. doi: 10.1371/journal.pone.0125557.

------ BMC Oral Health. 2022 Mar 12;22(1):68. doi: 10.1186/s12903-022-02102-8.

------ J Appl Gerontol. 2022 Mar;41(3):671-679. doi: 10.1177/07334648211028391.

------ BMC Public Health. 2025 Apr 15;25(1):1401. doi: 10.1186/s12889-025-22649-9.

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Reviewer #2: Yes: Cézar Luquine

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-->PONE-D-25-65610R1-->-->Exploring the mediating role of health-related social capital in the association between socioeconomic status and oral frailty risk among community-dwelling older adults: A longitudinal study using the JAGES-->-->PLOS One

Dear Dr. Tadaka,

Thank you for submitting your manuscript to PLOS ONE. After careful consideration, we feel that it has merit but does not fully meet PLOS ONE’s publication criteria as it currently stands. Therefore, we invite you to submit a revised version of the manuscript that addresses the points raised during the review process.

Please submit your revised manuscript by Jun 12 2026 11:59PM. If you will need more time than this to complete your revisions, please reply to this message or contact the journal office at plosone@plos.org. When you're ready to submit your revision, log on to https://www.editorialmanager.com/pone/ and select the 'Submissions Needing Revision' folder to locate your manuscript file.

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We look forward to receiving your revised manuscript.

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Academic Editor

PLOS One

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Additional Editor Comments:

Thank you for your efforts to improve the manuscript. However, the reviewer still has several concerns that must be addressed. Please carefully review the comments and provide a point-by-point response to all of them.

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Reviewer #2: (No Response)

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Reviewer #2: Partly

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Reviewer #2: No

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Reviewer #2: No

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-->6. Review Comments to the Author

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Reviewer #2: I thank the authors for their thorough point-by-point response and for the substantive revisions made to the manuscript. Several of my initial concerns have been appropriately addressed, including the clarification of healthy life expectancy, the addition of the cumulative advantage/disadvantage framework, the explanation of the Japanese universal healthcare context, and the rationale for the 2-million-yen SES threshold. These revisions improve the manuscript.

However, three of my central methodological concerns have not been adequately resolved, and a few of the smaller points would benefit from revisions being made visible in the manuscript itself rather than only in the response letter. I detail these below.

MEDIATION ANALYSIS IS INCONSISTENT WITHIT THE MANUSCRIPT:

Based on Figure 2, for instance, the path diagram depicts SES as the exposure, with direct paths from SES to education, household composition, sex, and oral frailty risk, and an indirect path from SES through community-level civic participation to oral frailty risk. This is, structurally, a mediation model in which SES is the exposure. However, the figure title ("Mediating structure of Community-level Civic participation in Low-SES for Oral frailty risk") and the methods text ("SEM was conducted for both the low-SES and high-SES groups to analyze the mediating structure") describe stratified estimation within SES subgroups. These are incompatible: SES cannot simultaneously be the exposure in a fitted path model and the variable used to split the sample into two separate models. If the mediation model in Figure 2 was estimated within the low-SES subsample, the SES → civic participation path cannot be meaningfully estimated because within-subsample variance in SES is restricted by the stratification itself. Conversely, if SES is a functioning exposure variable in the model, then the "in Low-SES" labeling is inaccurate. The authors should clarify exactly what was estimated.

Beyond this internal inconsistency, the model specification in Figure 2 raises concerns even taken on its own terms. The paths SES → sex and SES → education cannot be interpreted causally, since sex is determined at birth and educational attainment is typically completed decades before SES measurement in this cohort. This suggests the arrows are being used as statistical regression paths rather than directed causal relationships, which is required by mediation analysis for the indirect effect to have meaning. Additionally, modeling covariates (education, household composition, sex) as outcomes of the exposure rather than as exogenous adjustment variables changes the meaning of the direct and indirect effects in ways the manuscript does not address. Covariates should typically be modeled as exogenous predictors of the mediator and outcome (Valeri & VanderWeele, 2013, Psychological Methods, 18(2), 137–150).

Finally, no decomposition of total, direct, and indirect effects is reported, which is the purpose of a mediation analysis. The authors' statement that the SEM findings "are consistent with the associations observed in the logistic regression analyses" suggests the SEM is being used descriptively to recover the regression estimate rather than to quantify mediation pathways.

Two further technical issues warrant clarification. First, oral frailty risk is a binary outcome, but the estimator used in Amos is not specified; default maximum likelihood estimation with a binary outcome produces somewhat biased estimates. Second, the decision to fit SEM only for social capital variables significant in the low-SES logistic regression is a post-hoc selection step that compromises interpretation of the corresponding high-SES models, which are estimated conditionally on results from the other stratum.

I recommend the authors take one of two paths. Either (a) fit a unified mediation model with SES as exposure on the full sample and report indirect, direct, and total effect decomposition, or (b) remove the mediation framing entirely, revise the title, aims, and discussion to present this as a moderation/effect modification study, and report the stratified analyses transparently as such. The current version attempts to frame a stratified analysis as mediation, which will mislead readers.

MULTILEVEL MODELLING:

The removal of "multilevel approach" from the manuscript is appropriate, and the added limitation at Lines 554–558 is a reasonable compromise. However, the rationale provided in the response letter is inconsistent with the study design. The authors state that "our primary analytical focus was to examine the association between individual characteristics and the provision of social support." Social support provision is not, as I understand it, the outcome of this study; oral frailty risk is. This phrasing suggests either a drafting error or that this justification was adapted from another context, and I would ask the authors to clarify.

More substantively, the authors note that Saito et al. employed multilevel regression with the JAGES community-level social capital indicators, which implies that the data structure does, in fact, support multilevel modeling. The constraint is therefore analytical choice rather than data availability. Thys, justification as currently written is not coherent and should be revised.

WEIGHTING FOR COMMUNITY-LEVEL INDICATORS

The authors clarify that the weights are derived from factor loadings in the original JAGES scale development. I thank them for pointing to the methodological documentation. However, this raises a methodological question that the revised manuscript does not address: if the weights are factor loadings, the principled approach is to compute factor scores (e.g., regression-based or Bartlett scores from a measurement model fitted to the data), which is the approach taken in Saito et al. original work. A weighted composite using loadings as coefficients is an approximation that does not account for residual variance or the uncertainty in the factor structure. The authors should either justify why a weighted composite is preferred over factor scores in this specific context or acknowledge this as an additional methodological limitation if they are not able to estimate factor scores from a measurement model and re-run the analyses. At present, the community-level social capital measurement departs from the referenced scale development without justification.

Beyond the major methodological concerns above, I raise attention about some smaller issues for the next revision:

1. Several of the authors' clarifications, like the national equivalent disposable household income figures underlying the 2-million-yen threshold (2.653M in 2018; 2.794M in 2020), and the rationale for the post-hoc power analysis are informative but are not reflected in the manuscript. The income reference values and source should be added to Lines 250–253 so that international readers need not consult the response letter.

2. The authors' statement that excluded participants were older and in poorer health is helpful, but this is not documented in the manuscript. Given that approximately 40,000 participants were excluded, please add either a supplementary table comparing baseline characteristics of included versus excluded participants, or a brief paragraph in the Methods or Results describing the differences, with an accompanying limitation on potential selection bias.

The concerns raised above remain the core issues preventing publication. Addressing them substantively, rather than through reframing or additional caveats, is essential before the manuscript can be considered further. I hope these comments are useful to the authors in strengthening what is an important and timely investigation.

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Reviewer #2: Yes: Cézar Luquine

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Associations Between Health-Related Social Capital and Oral Frailty Risk Among Older Adults: A Stratified Analysis by Socioeconomic Status in the JAGES Longitudinal Study

PONE-D-25-65610R2

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The revisions have satisfactorily addressed the previous concerns, and the manuscript is now suitable for publication. Thank you for your effort.

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