Snapchat-Based Structured Education Reduces Kinesiophobia and Improves Psychological Readiness and Perceived Knee Function Following Anterior Cruciate Ligament Reconstruction: A Quasi-Experimental Study

Comment 1 (Abstract, Lines 22 to 23): The study is described as "quasi-experimental, two-arm study with non-randomized allocation at the clinic-branch level." While the rationale for cluster allocation (minimizing contamination) is understood, the lack of individual randomization is a notable limitation. Please justify why a randomized approach was not feasible in this specific clinical setting to strengthen the methodological defense.

We thank the reviewer for this important observation. We agree that the rationale for forgoing individual randomization warranted a more detailed justification. To preserve abstract brevity within the MDPI word limit, the expanded justification has been added to the Methods and the Limitations sections rather than the abstract itself.

Section 2.2 (Setting and Recruitment) has been revised to articulate that individual (within-site) randomization was not operationally feasible for two reasons: (i) the intervention was delivered via Snapchat, a peer-connected platform on which within-site individual allocation would have permitted contamination through patient-to-patient content sharing, and (ii) branch-level allocation was necessary to preserve therapist blinding.

Section 4.6 (Limitations) now includes a detailed three-reasons justification covering (a) platform-mediated contamination, (b) preservation of therapist blinding, and (c) unavoidable within-branch visual exposure through shared waiting areas and rehabilitation gyms.

Please see the revised Sections 2.2 and 4.6.

Comment 2 (Abstract, Line 31): The conclusion claims "clinically meaningful improvements." It is recommended to specify whether the changes in TSK-17 and IKDC exceeded the Minimum Clinically Important Difference (MCID) or Smallest Detectable Change (SDC) specifically validated for post-operative ACLR cohorts.

We fully agree with the reviewer. The phrase "clinically meaningful" has been removed from the abstract conclusion, which now states: "Snapchat-based structured education is associated with improvements in kinesiophobia, psychological readiness, and perceived knee function…" The revised wording is consistent with the detailed MCID/SDC interpretation provided in Section 4.2 and the epistemically calibrated Conclusion (Section 5), where we now explicitly state that "changes on TSK-17 and ACL-RSI did not definitively exceed established MCID or SDC thresholds."

Please see the revised Abstract and Section 5 (Conclusions).

Comment 3 (Introduction, Line 45): The authors state that contemporary protocols prioritize biomechanical criteria over psychological factors. To enhance the theoretical framework, please briefly discuss the reciprocal relationship between kinesiophobia and neuromechanical deficits (e.g., altered gait or stiff-knee landing) to bridge the gap between movement science and psychology.

We thank the reviewer for this valuable suggestion, which considerably strengthens the theoretical framework. A new sentence has been added to the second paragraph of the Introduction: "Importantly, kinesiophobia and neuromechanical function are reciprocally linked: elevated fear of movement has been associated with altered lower-limb biomechanics during functional tasks, including reduced knee flexion excursion, stiff-knee landing patterns, and greater inter-limb asymmetry, which in turn may reinforce fear-avoidance beliefs and delay unrestricted return to activity [Hart et al. 2024]." This bridges the psychosocial and movement-science dimensions as requested.

Please see the revised Introduction (paragraph 2) and new reference [50].

Comment 4 (Introduction, Line 50): The choice of Snapchat is justified primarily by popularity. I suggest adding a sentence regarding the pedagogical advantages of "micro-learning" or "short-form visual reinforcement" in medical education to provide a more robust academic rationale for the platform choice.

We appreciate this suggestion, which strengthens the pedagogical rationale for platform selection. A new sentence has been added to the Introduction: "Short-form video platforms align with established principles of micro-learning and short-form visual reinforcement in medical education, including bite-sized content delivery, spaced repetition, and multimodal encoding, which have been shown to improve knowledge retention and behavior change compared with traditional didactic approaches [Morgado et al. 2024]." This reframes the platform choice from a popularity argument to a pedagogically grounded one.

Please see the revised Introduction (paragraph 3) and new reference [51].

Comment 5 (Methods, Line 64): The use of only two branches (k=2) for allocation introduces significant risk of cluster-level confounding (e.g., differences in clinic equipment or therapist style). Please clarify if a fidelity audit was performed to ensure that the "standard rehabilitation" was truly identical across both branches.

We thank the reviewer for this critical point. Fidelity of the standard rehabilitation protocol across both participating branches was supported by four structural mechanisms: (i) a single written, phase-based, criteria-driven ACLR rehabilitation protocol covering pre-rehabilitation education and four rehabilitation phases, each with phase-specific progression checklists (Figure A1); (ii) uniform therapist training, with all treating therapists at both branches completing a standardized in-house training workshop on the protocol approximately one year prior to study initiation; (iii) daily per-session electronic medical record documentation of exercises prescribed and progression checklist items completed for every patient; and (iv) unified clinical governance, with a single medical director overseeing all four Joint Clinics branches.

We acknowledge that a formal prospective fidelity audit with pre-specified quantitative inter-branch comparisons was not conducted as a separate sub-study. This limitation has been explicitly addressed in Section 4.6, where we note that residual branch-level variation cannot be fully excluded despite protocol-level safeguards.

Please see the revised Section 4.6.

Comment 6 (Methods, Line 67): The TSK-17 cutoff of >37 is cited from chronic low back pain literature. It would be beneficial to acknowledge if this threshold has been specifically validated for acute/sub-acute ACLR patients to ensure the sample represents true clinical kinesiophobia in this population.

We fully agree. Section 2.3 has been revised to explicitly acknowledge that although the > 37 threshold has been applied in post-ACLR contexts (e.g., Almalki 2019, reference [22]), it originated in chronic low back pain research and has not, to our knowledge, been independently validated in ACLR populations. The revised sentence now reads: "…although this cutoff was originally derived from chronic low back pain populations [21] and has not, to our knowledge, been independently validated in ACLR populations."

The cutoff was retained because it is the prevailing threshold applied across the ACLR literature, ensures comparability with prior work, and identifies individuals with clinically elevated fear during the most modifiable rehabilitation window.

Please see the revised Section 2.3.

Comment 7 (Methods, Lines 70 to 74): The study relies exclusively on Patient-Reported Outcome Measures (PROMs). For a study in human movement science, the absence of objective functional measures (e.g., limb symmetry index, quadriceps strength) is a weakness. I recommend clarifying why physical performance data were not included as secondary outcomes.

We thank the reviewer for this important point and agree that the absence of objective functional measures is a meaningful limitation. The rationale is methodological: participants were enrolled across a heterogeneous post-operative window (Phases 1 and 2; 0 to 3 months post-surgery), consistent with evidence that kinesiophobia is highest and most modifiable during early rehabilitation. Because objective measures such as limb symmetry index, isokinetic quadriceps strength, and hop tests are strongly time-dependent after ACLR, aggregating such scores across participants at markedly different post-operative stages (e.g., 12 weeks vs. 6 months post-op by study end) would have introduced timing-related variance unrelated to the intervention. In contrast, TSK-17, ACL-RSI, and IKDC capture current fear, readiness, and perceived function in a manner interpretable across rehabilitation phases.

This trade-off is now explicitly acknowledged in Section 4.6, with a recommendation that future trials enrolling at a uniform post-operative timepoint incorporate objective functional measures alongside PROMs to enable triangulation of psychological and biomechanical outcomes.

Please see the revised Section 4.6.

Comment 8 (Methods, Line 91): The power analysis was conducted for a standard ANCOVA but does not appear to account for the Design Effect associated with cluster allocation. With a cluster-level design, the required sample size typically increases based on the Intra-cluster Correlation Coefficient (ICC). Please re-verify if the sample of 120 is sufficient when accounting for clustering.

We appreciate this important methodological point. The a priori G*Power analysis was conducted at the individual level and yielded a minimum sample size of 103 participants; 120 were recruited. With only two clusters (k = 2), the intra-cluster correlation coefficient cannot be reliably estimated from the study data, and a cluster-adjusted power calculation could not be performed without fabricating ICC assumptions. We have therefore addressed this in two places:

Section 2.6 now explicitly states that "the analysis was conducted at the individual level per standard practice for ANCOVA; a cluster design effect could not be incorporated because the intra-cluster correlation coefficient is not estimable with only two clusters."

Section 4.6 notes that "observed between-group effect sizes (d = 0.54 to 0.88) exceeded the planning assumption (d = 0.56) for two of three outcomes, providing empirical evidence of adequate signal detection, though the precise contribution of any cluster effect to the observed effects cannot be quantified."

Please see the revised Sections 2.6 and 4.6.

Comment 9 (Methods, Line 99 and Results, Lines 290 to 292 / Page 11, Lines 298 to 299): The use of Last Observation Carried Forward (LOCF) for missing data is a major concern. LOCF is often criticized in top-tier journals for biasing results and underestimating variance. I strongly suggest re-analyzing the data using Multiple Imputation (MI) or Mixed-Effects Models for Repeated Measures (MMRM) to provide a more robust intent-to-treat analysis.

We thank the reviewer for this important methodological recommendation. The intent-to-treat analysis has been entirely re-performed using Multiple Imputation (MI) as the primary approach, with LOCF retained only as a sensitivity analysis.

Methods (Section 2.7): "Intent-to-treat analyses used Multiple Imputation (MI) to handle missing 12-week outcome data. Fifty imputed datasets (M = 50) were generated via multivariate imputation by chained equations (MICE), incorporating all three outcome measures, baseline covariates, and auxiliary variables, with 20 burn-in iterations preceding the final imputations. The number of imputations was set consistent with published guidance that M should equal or exceed the percentage of missing data [Sullivan 2018; White 2011]. ANCOVA models were fitted within each imputed dataset and pooled using Rubin's rules, with Barnard-Rubin adjusted degrees of freedom."

Results (Section 3.7 and Table 6): The MI-based pooled ANCOVA confirmed all findings: TSK-17 (adjusted mean difference = −2.94, 95% CI [−4.43, −1.45], p < 0.001, d = 0.75); ACL-RSI (+7.93, 95% CI [4.07, 11.80], p < 0.001, d = 0.82); IKDC (+8.85, 95% CI [3.13, 14.56], p = 0.003, d = 0.61). Fractions of missing information ranged from 0.10 to 0.15. The LOCF-based sensitivity analysis (Table 5) produced convergent results.

Abstract updated: "Intent-to-treat analyses using multiple imputation confirmed all findings."

The former LOCF apology sentence has been removed from Section 4.6, as it is no longer applicable given the upgrade to MI as the primary ITT method.

Please see the revised Sections 2.7, 3.7, Tables 5 and 6, Abstract, and new references [52, 53].

Comment 10 (Results, Page 8, Lines 223 to 225): The authors report a significant violation of homogeneity of variance for the IKDC data (F(1, 100) = 15.50, p < 0.001), stating that the results should be "interpreted with caution." Please re-analyze these data using robust standard errors, generalized linear models, or an appropriate non-parametric alternative. Merely advising cautious interpretation is insufficient, as severe assumption violations render standard ANCOVA results unreliable.

We fully agree that cautious interpretation alone is insufficient. The IKDC ANCOVA has been re-estimated using two complementary corrective approaches:

(i) Heteroscedasticity-consistent (HC3) robust standard errors: adjusted mean difference = +8.90, robust SE = 2.98, 95% CI [2.98, 14.82], p = 0.003.

(ii) Quade's rank-based ANCOVA (non-parametric sensitivity): t = 3.19, p = 0.002.

Both corrective analyses confirmed a significant between-group effect on IKDC, indicating that the finding is robust to the variance heterogeneity. The phrase "interpret with caution" has been removed from Section 3.4 and the Table 4 note. The methodology and corrective results are now reported in Sections 3.4 and 3.6.

Please see the revised Sections 3.4 and 3.6 and the revised Table 4 note.

Comment 11 (Discussion, Pages 12 and 15, Lines 330 to 333 and 430 to 431): The authors concede that the improvements in TSK-17 and ACL-RSI did not definitively exceed the established MCID or SDC thresholds. However, the conclusion asserts that the intervention is associated with "clinically meaningful improvements." Please revise the discussion and conclusion to resolve this discrepancy.

We thank the reviewer for identifying this inconsistency. The wording has been reconciled across the abstract, discussion opening, and conclusion:

Abstract conclusion: "clinically meaningful improvements" deleted; now reads "is associated with improvements in kinesiophobia, psychological readiness, and perceived knee function."

Section 4 (Discussion opening): "and clinically meaningful" deleted; now reads "associated with statistically significant improvements across all three outcomes, with moderate-to-large effect sizes."

Section 5 (Conclusions): revised to explicitly acknowledge the MCID/SDC gap: "associated with statistically significant improvements in kinesiophobia, psychological readiness, and perceived knee function, with moderate-to-large effect sizes, although changes on TSK-17 and ACL-RSI did not definitively exceed established MCID or SDC thresholds."

The revised wording is now fully consistent with the detailed MCID/SDC interpretation already provided in Section 4.2.

Please see the revised Abstract, Section 4, and Section 5.

Comment 12 (Discussion, Page 13, Lines 350 to 352, and Figure 8): The discussion proposes pathways involving "descending pain modulatory mechanisms" and behavioral changes driving "physical improvements." Please constrain these mechanistic claims strictly to the measured psychosocial domains, or explicitly label Figure 8 as a hypothetical framework requiring future validation.

We agree and have adopted both corrective measures recommended by the reviewer.

Section 4.4 has been revised to reframe the proposed pathways as hypothesized rather than demonstrated: "Improvements in perceived knee function alongside psychological outcomes may operate through several hypothesized pathways… Because this study relied exclusively on self-reported outcomes without objective kinematic, biomechanical, or physiological measures, these proposed pathways remain speculative and require empirical validation in future trials incorporating objective functional assessment and formal mediation analysis." The phrase "potentially via descending pain modulatory mechanisms" now carries explicit hedging language.

Figure 8 has been retitled as "Hypothetical framework for the proposed mechanism of action," and the caption now includes: "This figure presents a hypothetical model requiring future empirical validation and is not derived from mediation or biomechanical analyses within the current study." Arrows are described as representing "proposed (not empirically tested) causal pathways."

Please see the revised Section 4.4 and revised Figure 8 caption.

Comment 1 (Keywords): I suggest removing the first two keywords, as it is not common to repeat words from the title as keywords.

We thank the reviewer for this recommendation, which aligns with standard indexing practice. The two keywords that duplicated title terms ("anterior cruciate ligament reconstruction" and "kinesiophobia") have been removed. The revised keyword list is: "psychological readiness; social media; digital health; fear avoidance; return-to-sport; rehabilitation."

Please see the revised Keywords line.

Comment 2 (References): Reference number 49 confirms my impression after reading the entire manuscript, that the material was carefully edited, probably after the first round of review or after the editor's intervention. However, this most recent reference (from 2026, while the closest one is from 2023; there is a two-year gap) was obviously added later, because after 13 and 14 there should be 15, not 49. It was not incorporated sequentially, and it also seems that you did not use a reference manager. Therefore, it will be necessary to carefully check and arrange all the references in the paper, from 14 to 49.

We thank the reviewer for this careful observation and fully agree. The non-sequential placement of reference 49 reflected the fact that it was added after the initial submission, along with four further references (Hart et al. 2024, Morgado et al. 2024, Sullivan et al. 2018, and White et al. 2011) that were incorporated during the current revision in response to Reviewer 1's methodological and theoretical requests.

In response to this comment, we have now fully re-ordered the entire reference list so that all references appear in strict order of first citation in the manuscript text. The five previously out-of-sequence references have been renumbered and re-positioned as follows: Hart et al. (2024) has moved from position 50 to position 10; AlMuhaya et al. (2026) has moved from position 49 to position 16; Morgado et al. (2024) has moved from position 51 to position 19; Sullivan et al. (2018) has moved from position 52 to position 34; and White et al. (2011) has moved from position 53 to position 35. All remaining references have been shifted accordingly to preserve sequential numbering from 1 to 53, and every in-text citation throughout the manuscript has been updated to match the new numbering. The complete reference list has been cross-checked for accuracy, completeness, and consistency with the in-text citations

Please see the revised Reference List.

Comment 3 (Effect sizes): I would also note that in order to calculate and display the effect size, in addition to partial eta squared, it is not necessary to include Cohen's d; ensure it is not redundant.

We thank the reviewer for this observation. After careful consideration, we have retained both effect-size indices because they serve complementary purposes in the analysis: partial eta squared (η²p) is the natural effect size for the 2 × 2 mixed repeated measures ANOVA time × group interactions reported in Tables 3 and 5, while Cohen's d is the natural effect size for between-group ANCOVA mean differences (Tables 4 and 6) and aligns with the MCID/SDC-based clinical interpretation framework used in rehabilitation research (Section 4.2). Dropping either would create reporting inconsistency across complementary analyses. We have retained both to preserve interpretability across the RM-ANOVA and ANCOVA frameworks and to facilitate comparison with existing ACLR rehabilitation literature, which commonly reports both.

Please see the revised Section 2.7 and Tables 3, 4, 5, and 6.

Comment 1 (Abstract, within-site randomization justification): "The expanded three-point justification for avoiding within-site randomization (platform-mediated contamination, therapist blinding, and shared gym visual exposure) is exceptionally well-argued and practically grounded. This provides a strong methodological defense for the quasi-experimental design. No further edits are required here; excellent work."

We thank the reviewer for this kind assessment. As no further edits were requested, this section remains unchanged in the current revision.

Comment 2 (Figure 8 caption, mechanistic framework): "The revisions to the mechanistic claims are excellent. Stating that the pathways are speculative and require formal mediation analysis perfectly calibrates the claim. The updated title for Figure 8 (“Hypothetical framework...”) is also highly appropriate. To add a final layer of methodological refinement, please ensure that the text clearly delineates that the mechanisms mapped in the figure (Expectation Management, Uncertainty Reduction, Confidence Building) are theoretical constructs driving the intervention design, rather than empirically measured mediators in this specific cohort."

We thank the reviewer for this valuable final refinement. We fully agree that the distinction between theoretical design constructs and empirically measured mediators warrants explicit clarification. Accordingly, the following sentence has been added to the Figure 8 caption:

"The three intervention mechanisms depicted (expectation management, uncertainty reduction, and confidence building) are theoretical constructs that guided the design of the educational content and were not empirically measured as mediators in the current cohort."

This clarification reinforces that the three pathway constructs functioned as design inputs shaping the educational content rather than as measured variables within the present analysis, and it aligns the caption with the hedged language already introduced in Section 4.4.

Please see the revised Figure 8 caption (Section 4.4).

Comment 3 (Effect sizes, “one of three outcomes”): "The manuscript correctly states that the observed between-group effect sizes (d = 0.54 to 0.77) exceeded the planning assumption (d = 0.56) for ‘one of three outcomes.’ While the response letter mistakenly claimed it exceeded for two of three outcomes, the manuscript text remains perfectly accurate (d = 0.77 for ACL-RSI is the only one > 0.56). I commend the authors for ensuring the manuscript remained factually accurate despite the typo in the rebuttal letter. No further changes are needed here."

We appreciate the reviewer’s careful cross-check. We confirm that the manuscript text accurately states “one of three outcomes,” and we regret the inconsistent phrasing in our previous rebuttal letter. No change to the manuscript is required for this point.

Comment 4 (Basic clinical milestones such as ROM and effusion): "I completely agree with your methodological justification that objective functional measures (e.g., isokinetic strength, hop tests) are highly time-dependent and inappropriate to aggregate across a heterogeneous 0 to 3 month window. However, as a biomechanics researcher, I must point out that basic clinical markers such as Range of Motion (ROM) or effusion are standard progression criteria for Phases 1 and 2 in your protocol. I recommend adding a brief sentence acknowledging that even basic objective clinical milestones (e.g., achieving full extension or minimal effusion) were not extracted from the medical records for secondary analysis, which could be a valuable focus for future retrospective studies."

We thank the reviewer for this excellent and constructive suggestion. We agree that basic phase-appropriate clinical milestones represent a meaningful additional layer of objective data that is less confounded by post-operative timing than performance-based measures, and that these indicators could have been extracted from the electronic medical records for secondary analysis. The following addition has been incorporated into Section 4.6 (Strengths and Limitations), immediately following the existing statement on objective functional measures:

"In addition, basic objective clinical milestones that are already embedded in our phase-based progression criteria, such as achievement of full knee extension or resolution of effusion, were not extracted from the electronic medical records for secondary analysis in the present work. Retrospective extraction of such phase-appropriate clinical markers represents a valuable direction for future work, as these indicators are less confounded by post-operative timing than performance-based measures and could complement patient-reported outcomes in characterizing recovery."

Please see the revised Section 4.6.

Comment 5 (Final remarks): "The statistical re-analyses (especially the use of 50 imputed datasets via MICE and Quade’s rank ANCOVA) were executed flawlessly and reported with high transparency. The manuscript is methodologically sound, thoughtfully discussed, and clinically relevant. Please address the minor point regarding basic ROM/effusion metrics, and this manuscript will be an excellent contribution to the literature."

We are deeply grateful for this generous final assessment and for the reviewer’s rigorous engagement with both revision rounds. The basic ROM and effusion point has been addressed in Section 4.6 as described in Response 4 above.