Predicting Intrinsic Motivation After an Adventure Education Program in Primary Schools: Enjoyment, Self-Confidence and Resilience According to Gender

Round 1

Reviewer 1 Report

Comments and Suggestions for Authors

I struggled with parkour being included in Adventure "Education" - believe it would more firmly fit into recreation as there is no mention of educational attributes. That all said, thought the results are valid, and pertinent.

There was minimum experience with parkour for the students (seven sessions), which also lends to "recreational" rather than educational.

Comments for author File: Comments.pdf

Author Response

Response to Reviewers

Manuscript ID: behavsci-4272669

Title: Predicting intrinsic motivation after an Adventure Education program in Primary Schools: enjoyment, self-confidence and resilience according to gender.

 

Dear Editor, dear Reviewers,

 

We would like to express our sincere gratitude for the careful reading of our manuscript and for the constructive comments received. The remarks and suggestions provided have been very useful for clarifying the positioning of the study, tightening the methodological description, and refining the way in which the findings are interpreted. We have addressed all the points raised, and the changes introduced in the revised version are highlighted in blue throughout the manuscript so that they can be easily identified. The line numbers cited below refer to the revised manuscript.

 

Below we provide a point-by-point response to each reviewer.

Reviewer 1

We thank the reviewer for the supportive overall assessment and for the helpful annotations made directly on the manuscript. The comments have allowed us to clarify several aspects of the rationale and the procedure that, on rereading, were indeed underspecified.

Comment 1. Justification of parkour as Adventure Education (“need to convince me parkour is adventure education”).

We fully agree that the link between parkour and the Adventure Education framework deserved a more explicit treatment. The introduction has therefore been expanded (lines 65–77) to make this connection visible. We now describe the conceptual roots of parkour in the méthode naturelle developed by Georges Hébert in the early twentieth century and in the obstacle and challenge-course traditions that have informed adventure education for decades, and we identify the three pedagogical features that, in our view, place parkour within the AE family: unfamiliar physical situations involving perceived risk, problem-solving, and the cooperative negotiation of obstacles. The reference Atkinson (2009) has been added in support of this lineage.

Comment 2. Description of the intervention (“how many sessions? consistent across groups, ages, etc.?”).

The reviewer rightly noted that the TIDieR description was too generic. The corresponding entries have been rewritten with concrete information. Item 6 (“How”, lines 240–243) now states that the program was delivered through seven structured sessions of 50–55 minutes each, integrated into the regular Physical Education timetable, and that the same seven-session structure was applied to all participating groups across the 12 schools, regardless of grade (5th or 6th), in order to ensure consistency of dose across sites and age groups. Item 8 (“When and how much”, lines 246–249) now specifies the second academic term of 2025, one session per week for approximately seven weeks, and the timing of the pre- and post-tests with respect to the first and last sessions.

Comment 3. Implementation fidelity (“what teaching occurred?”).

We agree that the previous wording on fidelity was not sufficiently informative. Item 12 has been expanded (lines 251–258) to explain that each session was guided by a common written protocol, that teachers completed a brief checklist after every session recording delivery, duration of each phase, and any incident or adaptation introduced, and that these checklists were periodically reviewed by the research team to monitor cross-site consistency. We have also acknowledged explicitly that delivery was distributed across 12 schools and several teachers, which inevitably introduces some variability even when the protocol is held constant.

Comment 4. Long-term follow-up.

This is an important point that was previously underdeveloped in the limitations. We have now made the suggestion explicit (lines 506–509) and proposed follow-up assessments at three, six, and twelve months after the end of the intervention as a concrete next step.

Comment 5. Access to a parkour course in primary schools.

We have incorporated this concern as part of an additional limitation paragraph (lines 526–531). We clarify that parkour requires a minimum of materials and adapted spaces (mats, boxes, benches, parallel bars, urban-style obstacles), that not every primary school has direct access to a dedicated parkour course, and that the activities used in this study were intentionally designed to be implemented with standard PE equipment in order to ease replication.

Reviewer 2 Report

Comments and Suggestions for Authors

This manuscript addresses an interesting and practically relevant question concerning the use of a parkour-based Adventure Education (AE) programme to enhance intrinsic motivation and related psychological variables in primary school students. The sample size is strong, the school-based context is valuable, and the focus on applied educational practice is a clear strength. The paper is well written and the analyses are competently conducted.

However, there are several important issues that need to be addressed to ensure the claims made are aligned with the design and purpose of the study. In its current form, the manuscript reads as though it is testing mechanisms and causal effects, whereas the design is more consistent with a pilot/exploratory study intended to generate hypotheses. Clarifying this positioning would substantially strengthen the paper.

1. Study design and absence of a control condition

The study uses a pre–post quasi-experimental design with no control group. While this is acceptable for exploratory or pilot work, the implications need to be made much more explicit throughout the manuscript. At present, the paper interprets the observed increases in motivation, enjoyment, self-confidence, and resilience as effects of the intervention. Without a control condition, however, these changes could plausibly reflect a number of possibilities including maturation or natural development over time, testing or familiarity effects, novelty or engagement effects associated with a new activity, or contextual or teacher-related influences. Although you acknowledge this limitation briefly , but it needs to be foregrounded much more strongly and consistently reflected in the interpretation of results.

To address this you need to reframe the study explicitly as exploratory/pilot work and avoid causal language. Phrases such as “produced increases” or “demonstrates effectiveness” should be replaced with more cautious wording (e.g., “is associated with”, “coincided with increases”).

2. Framing of the research question

The research question is reasonable but currently presented as if it is testing well-specified theoretical predictions. In reality, the study is better understood a exploring whether an AE programme is associated with changes in key variables and examining how these variables co-vary within this context. The current hypotheses (e.g., enjoyment predicting intrinsic motivation) are highly consistent with existing theory and are therefore not especially risky or novel. More importantly, the manuscript does not sufficiently justify why parkour specifically should have unique effects relative to other PE activities and why a seven-session intervention would be expected to influence constructs such as resilience, which are typically more stable.

Therefore, the suggestion is to strengthen the rationale by either clearly articulating what is unique about parkour/AE, or repositioning the study as an initial exploration of feasibility and potential impact rather than a definitive test of theory. I suggest the latter as you do not have control data.  

3. Interpretation of predictive analyses (mechanisms vs associations)

A key issue in the manuscript is the interpretation of regression analyses as indicating underlying processes or mechanisms. The hierarchical regression shows that enjoyment, self-confidence, and resilience predict intrinsic motivation. However, these variables are measured at the same time points and the analyses are cross-sectional (within pre and post separately) and there is no temporal ordering between predictors and outcome. As such, these findings demonstrate association, not mechanism. Statements implying that enjoyment “drives” or “leads to” intrinsic motivation are therefore not supported by the design.

The suggestion is to reframe these findings as descriptive of relationships among variables within this context. If mechanistic explanations are offered, they should be clearly identified as speculative and theory-informed, not empirically tested.

 

4. Conceptual overlap between variables

There is a degree of conceptual proximity between some of the constructs, particularly intrinsic motivation and enjoyment. Given that intrinsic motivation (within SDT) is partly defined by inherent enjoyment, the finding that enjoyment is the strongest predictor is somewhat expected and may reflect shared variance rather than a distinct explanatory process. Therefore,  please acknowledge this overlap and discuss its implications. This would strengthen the conceptual clarity of the paper and avoid overstating the novelty of the findings.

5. Intervention specification and variability

The intervention is described as a seven-session programme delivered across 12 schools by different teachers . While this enhances ecological validity, it also introduces variability including differences in delivery style, differences in fidelity across sites and potential clustering effects. Further, these factors are not addressed analytically. Therefore, you should acknowledge this as a limitation and, if possible, clarify how fidelity was monitored beyond general statements. Future work should consider multi-level modelling or more controlled implementation.

6. Contribution and positioning of the study

The study has value, but its contribution is currently overstated. It does not establish causal effects, nor does it test mechanisms or  isolate the unique contribution of parkour or AE.

What it does provide is evidence that an engaging, novel PE programme is associated with positive changes in self-reported psychological variables and  preliminary data that can inform more rigorous future studies. You should reposition the contribution accordingly and emphasise feasibility, acceptability, preliminary effect patterns and  hypothesis generation

Author Response

Response to Reviewers

Manuscript ID: behavsci-4272669

Title: Predicting intrinsic motivation after an Adventure Education program in Primary Schools: enjoyment, self-confidence and resilience according to gender.

Dear Editor, dear Reviewers,

We would like to express our sincere gratitude for the careful reading of our manuscript and for the constructive comments received. The remarks and suggestions provided have been very useful for clarifying the positioning of the study, tightening the methodological description, and refining the way in which the findings are interpreted. We have addressed all the points raised, and the changes introduced in the revised version are highlighted in blue throughout the manuscript so that they can be easily identified. The line numbers cited below refer to the revised manuscript.

Below we provide a point-by-point response to each reviewer.

Reviewer 2

We are grateful to the reviewer for the depth of the comments and for the clear distinction drawn between the descriptive evidence the study can legitimately provide and the more ambitious claims of mechanism or efficacy. We share this view and have revised the manuscript accordingly. The wording has been adjusted throughout the abstract, discussion and conclusions to match the design of the study, and the limitations section has been substantially expanded.

Comment 1. Study design and absence of a control condition; causal vs. associative language.

We accept the reviewer’s point that the previous wording was, in places, more causal than the design allows. The relevant passages have been rephrased throughout the manuscript. In the abstract, the closing sentence now reads “suggesting that the changes coincided with the program in a comparable way for both genders. Given the absence of a control group, these findings should be interpreted as preliminary evidence rather than as a causal test of the program’s effectiveness” (lines 30–33). In the discussion, the previous “produces a significant increase” has been replaced by “is associated with a significant increase … from pre-test to post-test. Given that no control condition was included, however, these changes should not be interpreted as causal effects of the intervention in a strict sense, but rather as changes that coincided with its implementation” (lines 449–453). Equivalent revisions have been applied in the conclusions (lines 540–545; 551–559; 569–573).

Comment 2. Framing of the research question and unique role of parkour.

We have strengthened the rationale for the choice of parkour in the introduction (lines 65–77), as also requested by Reviewer 1, by linking the discipline to the méthode naturelle and to the broader obstacle/challenge-course tradition that underpins AE, and by identifying the specific pedagogical features that justify its use as an AE content. We have also moderated the framing of the contribution at the end of the discussion and in the closing sentence of the conclusions (lines 569–573), where the study is now positioned as preliminary evidence consistent with a positive effect, rather than as a definitive test.

Comment 3. Interpretation of predictive analyses (mechanisms vs. associations).

We agree that, given the simultaneous assessment of predictors and outcome, the regression results describe association rather than mechanism. The corresponding passage in the discussion has been rewritten (lines 460–470) to make this clear: “the regression analyses were cross-sectional within each measurement point, with predictors and outcome assessed simultaneously, so the present findings describe co-variation among constructs rather than directional or mechanistic relationships”. The same caveat has been added to the third objective in the conclusions (lines 553–559).

Comment 4. Conceptual overlap between intrinsic motivation and enjoyment.

We have added an explicit acknowledgment of this overlap in the discussion (lines 466–470): “a degree of conceptual proximity exists between intrinsic motivation and enjoyment within SDT, where inherent enjoyment is itself part of the definition of intrinsic motivation; the strong association between the two variables therefore partly reflects shared theoretical content, and should not be read as evidence that enjoyment causes intrinsic motivation”. A briefer reference to this point has also been added to the conclusions (lines 555–558).

Comment 5. Intervention specification, variability and clustering.

This concern has been addressed at two levels. First, the TIDieR description has been rewritten (items 6, 8 and 12; lines 240–258) to give a more transparent account of dose, frequency, common protocol and fidelity monitoring. Second, a dedicated paragraph has been added to the limitations (lines 519–531) acknowledging that delivery across 12 schools and several teachers introduces variability in instructional style, possible differences in fidelity between sites, and a clustered structure (students nested within classes and schools) that was not modelled analytically in the present work. We explicitly recommend, in the same paragraph, that future studies should consider multi-level approaches, more controlled implementation, and explicit measures of fidelity beyond session checklists.

Comment 6. Contribution and positioning of the study.

The contribution has been recalibrated in line with the reviewer’s suggestion. We no longer present the study as a test of efficacy: in the abstract, in the closing of the discussion, and in the final paragraph of the conclusions (lines 569–573), the study is now positioned as preliminary evidence consistent with a positive effect of the program, supporting feasibility and providing a basis for the design of future randomised or controlled studies. We believe that this repositioning preserves the value of the empirical material — a quasi-experimental study with N = 492 across 12 schools — while bringing the interpretive claims into line with what the design can support.

Best regards.

Reviewer 3 Report

Comments and Suggestions for Authors

Overall this research is well designed with clear hypotheses, research methods and analysis. Authors have been clear and transparent about relevant limitations to the study. Tables are well used and displayed throughout the article.

Most of my comments are fairly minor in nature and are listed below.

1. Citations. There are several instances where three authors were listed for the in-text citation but should instead by listed be listed as (author, et al., date)
2. Page 2, line 58. Don't include "among others" in your list of citations. Either include the actual other citations or leave it with just the citations you have.
3. Page 2, line 60. Wrapping up the history of parkour to "emerged in France in the 1990s" without any citation or credit to where it has come from is missing information. Parkour actually started before the 1990's and has a common origin in other aspects of adventure education (see Georges Hébert and history of challenge course/high ropes course). Fill this out more to demonstrate knowledge of where the sport actually came from.
4. Page 8, line 324. The results are actually presented in table 6 (not 5).
5. Page 10. There is something wrong with the section headers. It goes from 3.3 to 3.4.1 through 3.4.4. Those should be 3.3.1 through 3.3.4
6. References. You have listed the World Health Organization in your references but you have not actually cited WHO in text.

Author Response

Dear Editor, dear Reviewers,

 

We would like to express our sincere gratitude for the careful reading of our manuscript and for the constructive comments received. The remarks and suggestions provided have been very useful for clarifying the positioning of the study, tightening the methodological description, and refining the way in which the findings are interpreted. We have addressed all the points raised, and the changes introduced in the revised version are highlighted in blue throughout the manuscript so that they can be easily identified. The line numbers cited below refer to the revised manuscript.

Below we provide a point-by-point response to each reviewer.

Reviewer 3

We thank the reviewer for the careful reading and for the very precise list of corrections, which have allowed us to fix several errors that had escaped previous proofreading rounds. All the points have been addressed.

Comment 1. In-text citations with three authors.

The relevant in-text citations have been corrected to “et al.” in the first mention. Specifically, “Becerra-Fernández, Mayorga-Vega & Guijarro-Romero, 2025” (line 40), “Goudas, Biddle and Fox (1994)” (line 168), “Moreno, González-Cutre and Chillón (2009)” (line 169) and “Andrade, Lois, and Arce (2007)” (line 182) now read as Becerra-Fernández et al. (2025), Goudas et al. (1994), Moreno et al. (2009) and Andrade et al. (2007), respectively.

Comment 2. “Among others” in the citation list (page 2, line 58).

The phrase has been removed (line 63). The list now ends with the last named citation.

Comment 3. History of parkour (page 2, line 60).

We agree that the previous wrap-up of parkour as having “emerged in France in the 1990s” was too narrow. The paragraph has been rewritten (lines 65–77) to acknowledge the earlier movement traditions on which parkour draws, in particular the méthode naturelle developed by Georges Hébert and the obstacle/challenge-course traditions linked to it. The reference Atkinson (2009) has been added to support this point.

Comment 4. Page 8, line 324 — table number.

Corrected: the regression analysis results for the boys are now correctly presented as Table 6 (line 356).

Comment 5. Section numbering 3.4.1–3.4.4.

Corrected: the four subsections have been renumbered as 3.3.1, 3.3.2, 3.3.3 and 3.3.4 (lines 404, 412, 419 and 425), so that they now hang correctly from section 3.3 (“2x2 repeated measures ANOVA”).

Comment 6. World Health Organization reference not cited in text.

A citation to the World Health Organization (2024) has been added in the opening paragraph of the introduction (lines 39–40), where it now supports the contextual statement on the relevance of physical activity for child and adolescent health. The corresponding entry in the reference list has been kept.

We hope that the revised manuscript adequately addresses all the concerns raised. We thank the reviewers and the Editorial Office once again for the time and attention dedicated to our work.

 

On behalf of the authors,

Round 2

Reviewer 2 Report

Comments and Suggestions for Authors

The revision is better than a version that simply claimed effectiveness, because the authors now repeatedly acknowledge the absence of a control group and the limits on causal inference. However, the paper continues to oscillate between cautious language and stronger causal claims, and the study design does not justify the stronger wording.

The abstract has improved: it explicitly states that, because there is no control group, the findings should be interpreted as “preliminary evidence rather than as a causal test of the program’s effectiveness”. That is welcome. However, the article still opens by saying the study aimed to analyse the “effects” of the programme, and H1 states that participation “will lead to” increases in motivation, enjoyment, self-confidence and resilience. This is still causal language. With a one-group pre-post design, the authors can say scores increased after the programme, but they cannot say participation led to those increases. The design cannot separate the programme from maturation, school context, teacher effects, repeated testing, novelty, seasonal effects, or broader changes in PE lessons.

The Methods section reinforces the problem. The authors describe the design as “quasi-experimental, cross-sectional, descriptive, and correlational”. This is conceptually confused. A pre-post design is not cross-sectional in the usual sense, but the regression analyses are cross-sectional at each time point. The article needs to be much clearer: the intervention component is a single-arm pre-post design, while the regression analyses are cross-sectional associative analyses conducted separately at pre-test and post-test. The word “quasi-experimental” is also potentially misleading unless the absence of a control group is foregrounded each time claims about change are made.

The strongest remaining problem is that the authors still present the repeated-measures ANOVA as though it evaluates intervention effects. They state that the ANOVA was conducted “with the aim of analysing the effects of the intervention on intrinsic motivation”. This should be rewritten. The ANOVA tests whether mean scores differ over time and whether that time difference varies by gender. It does not test whether the intervention caused the change. Similarly, the results state that there was “a significant increase in intrinsic motivation following the intervention”. That wording is acceptable only if “following” is used temporally, but throughout the paper it risks being read causally. A safer formulation would be: “Intrinsic motivation scores were significantly higher at post-test than at pre-test.”

There is also a major issue with the interpretation of the non-significant gender interaction. The authors write that “the absence of interaction is not a negative finding; rather, it indicates that the program is effective and equitable for both genders”. This is not justified. A non-significant interaction does not prove equivalence, equity, or equal effectiveness. It only indicates that the study did not detect evidence that the pre-post change differed by gender. To claim equity, the authors would need an equivalence or non-inferiority framework, pre-specified margins, and ideally a controlled design. This sentence should be removed or substantially softened.

The regression language also remains too strong in places. The authors refer to the “predictive capacity” of enjoyment, self-confidence and resilience on intrinsic motivation, but the variables were measured at the same time within each wave. This means the analyses are associative, not predictive in a temporal or causal sense. The Discussion does include a good caveat that the regression analyses describe “co-variation among constructs rather than directional or mechanistic relationships”. However, the Results and objectives should be aligned with that caution. The authors should use “associated with” or “statistically related to” rather than “predictor” unless they explicitly define prediction as statistical prediction only.

The paper also needs to address conceptual overlap more firmly. Enjoyment is not simply an external predictor of intrinsic motivation; it is closely embedded in the definition of intrinsic motivation. The authors do acknowledge this in the Discussion, noting the “conceptual proximity” between intrinsic motivation and enjoyment. That is useful, but it weakens the claim that enjoyment is the “main predictor.” A high association between two conceptually overlapping constructs may partly reflect shared item content, shared method variance, or theoretical redundancy rather than a substantive psychological mechanism.

The authors do now include a reasonable limitations section. They acknowledge the absence of random assignment and the lack of a control group, and they correctly note that pre-post changes cannot be unequivocally attributed to the programme because maturation, repeated questionnaire exposure, novelty, contextual influences and teacher effects cannot be ruled out. This is one of the strongest parts of the revision. However, the conclusions then drift back into stronger wording. For example, they say the programme “appears to contribute to the emotional and personal development of the students” and that the lack of gender interaction “confirms the program was equally effective”. These statements are overstated. They should be rewritten to say that the programme was associated with improvements, and that the study found no evidence that changes differed by gender.

A further methodological concern is the clustered structure of the data. Students were drawn from 12 schools and taught by different PE teachers, with implementation varying across sites . The authors acknowledge this as a limitation, but it is more than a minor limitation: students are nested within schools/classes/teachers, and responses may not be independent. The analyses treat all 492 students as independent observations. This may underestimate uncertainty and inflate precision. At minimum, the authors should report intraclass correlations or conduct sensitivity analyses using school/class as a clustering factor or clearly state that the results may be over-precise because clustering was not modelled.

There are also presentation and reporting issues. There is also confusion about who administered questionnaires: one section states researchers administered instruments, and the teacher was not present, while another states that teachers administered the pre-intervention questionnaires and supervised post-intervention administration. This inconsistency matters because teacher presence could influence socially desirable responses in a school-based intervention.

Suggested decision: I would recommend further revision, not acceptance in its current form. The authors have clearly tried to respond to concerns about causality, and some caveats are now good. However, the manuscript still contains causal and effectiveness language that is not supported by the design. The revision should consistently present the study as a single-arm exploratory pre-post study that found post-test improvements and associations among variables, not as evidence that the programme caused those improvements.

Key wording changes I would request:

Replace “effects of the intervention” with “pre-post changes following the intervention.”

Replace “participation will lead to” with “students will show higher post-test scores than pre-test scores.”

Replace “predictors of intrinsic motivation” with “variables statistically associated with intrinsic motivation.”

Replace “the programme was effective and equitable for both genders” with “there was no evidence that pre-post change differed between boys and girls.”

Replace “parkour-based AE appears to contribute to emotional and personal development” with “scores on emotional and personal development variables increased following the programme, although these changes cannot be attributed uniquely to the programme.”

 

Author Response

Dear Editor, dear Reviewer 2,

 

We are very grateful for the careful and demanding second-round review. The reviewer rightly identified that, despite the changes introduced in the first round, the manuscript still oscillated between cautious wording and stronger causal claims that the design does not support. We fully accept this assessment. The current revision has therefore been conceived as a single, consistent rewriting of all the wording across the abstract, hypotheses, objectives, methods, results, discussion and conclusions, so that every statement about what the study can claim is brought into line with a single-arm pre–post design with cross-sectional associative analyses. The five literal wording changes requested by the reviewer have been applied throughout the manuscript, and the two methodological concerns (clustered structure of the data and inconsistency regarding who administered the questionnaires) have been addressed. All changes are highlighted in blue in the revised manuscript. Line numbers below refer to the revised version.

We address each of the reviewer's points in turn.

On the persistence of causal language and the design of the study.

We acknowledge that the previous version still contained causal formulations (e.g., “effects of the intervention”, “will lead to”, “the program is effective and equitable”). All of them have been rewritten. The abstract now states that the study aims to describe pre–post changes and to examine variables statistically associated with intrinsic motivation, and explicitly concludes that, given the single-arm pre–post design and the absence of a control group, the findings should be interpreted as preliminary descriptive evidence of pre–post change and associations, and not as a causal test of the program’s effectiveness (lines 11–35). The same framing is now used in the introduction (lines 92–94, H1), in the general aim (lines 103–108), in the specific objectives (lines 110–121), and is carried consistently into the discussion (lines 471–484) and the conclusions (lines 581–611).

On the description of the design (Section 2.2).

The reviewer correctly pointed out that the previous formulation (“quasi-experimental, cross-sectional, descriptive, and correlational”) was conceptually confused. Section 2.2 has been rewritten (lines 148–158): the intervention component is now described as a single-arm pre–post quasi-experimental design with intrinsic motivation, enjoyment, self-confidence and resilience assessed before and after the programme, while the regression analyses are explicitly described as cross-sectional within each measurement point and as associative rather than predictive in a temporal or causal sense. The absence of a control group and the non-random assignment of participants are foregrounded in the same paragraph and developed in the Limitations section.

On the ANOVA and the interpretation of the non-significant interaction.

We agree that the ANOVA was previously presented as a test of intervention effects. The description of the analysis has been rewritten (lines 423–430) so that it now states that the ANOVA was carried out in order to test whether mean intrinsic motivation scores differed between pre-test and post-test and whether that time difference varied by gender, and that this analysis tests for differences in means over time and their interaction with gender, without testing whether the intervention caused those differences, given the absence of a control group. In line with the reviewer’s specific request, the previous claim that “the program is effective and equitable for both genders” has been removed. It has been replaced, both in Section 3.3 (lines 464–469) and in the conclusions (lines 601–604), by the more cautious formulation that the non-significant time × gender interaction indicates only that the study did not detect evidence that the pre–post change differed between boys and girls, and that this finding should not be interpreted as proof of equivalence or of equal effectiveness across genders, which would require an equivalence or non-inferiority framework with pre-specified margins and ideally a controlled design.

On regression analyses and the use of the term “predictor”.

We agree with the reviewer that, because predictors and outcome were assessed simultaneously within each wave, the regression analyses are associative rather than predictive in a temporal or causal sense. Hypothesis 3 (lines 98–100), the third specific objective (lines 116–118), the description of the analyses in Section 2.6 (lines 286–296) and the introduction to the regression results in Section 3.2 (lines 370–377) have all been rewritten in associative terms. In the few instances where the word “predictor” is still used inside the description of the regression model itself, it is now explicitly defined as a “statistical predictor” within the regression model and is no longer presented as implying temporal or causal precedence (lines 294–296 and 373–375). This follows the reviewer’s own suggestion that the term may remain only if it is explicitly defined in this restricted statistical sense.

On the conceptual overlap between intrinsic motivation and enjoyment.

We share the reviewer’s reading. The previous wording (“Enjoyment emerged as the main predictor”) has been removed from the abstract and the discussion. The abstract (lines 28–30), the discussion (lines 493–500) and the conclusions (lines 597–600) now state that enjoyment is the variable most strongly statistically associated with intrinsic motivation, while keeping in mind the conceptual proximity between the two constructs within SDT, and explicitly note that the strong association partly reflects shared theoretical content and should not be read as evidence that enjoyment causes intrinsic motivation.

On the clustered structure of the data and the analysis of independence.

The reviewer is right that, given that students are nested within classes, teachers and schools, treating all 492 students as independent observations is a substantive limitation. We have explicitly acknowledged this in the Limitations section (lines 555–561): because all participants were treated as independent observations and intraclass correlations were not computed in the present work, the standard errors of the analyses may be underestimated and statistical precision may consequently be overstated. We have added that the results should be read bearing this caveat in mind and that future replications should explicitly model the clustering by means of multi-level approaches and report intraclass correlations or sensitivity analyses with school or class as a clustering factor. We have not attempted to re-run the analyses in the present revision because doing so would substantially exceed the scope of a wording-focused revision and may require additional data preparation that the team prefers to address in a dedicated subsequent study; we have flagged this openly rather than understating the issue.

On who administered the questionnaires.

We thank the reviewer for spotting this inconsistency, which had escaped previous proofreading. The two passages have been harmonised. Section 2.4 (lines 210–216) now states that the instruments were administered in the classroom by the teachers themselves, following a common written protocol provided by the research team, and that the research team coordinated and supervised the administration process across the 12 schools in order to ensure procedural consistency but did not deliver the questionnaires directly. The potential influence of teacher presence on socially desirable responses has been explicitly added to the Limitations (lines 561–565). Section 2.5 is now consistent with this description.

On the five literal wording changes requested by the reviewer.

Each of the five specific reformulations requested has been applied at every relevant location in the manuscript. We summarise the mapping below for ease of cross-checking.

1. “Effects of the intervention” has been replaced by “pre–post changes following the intervention” (and equivalent associative formulations) in the abstract (lines 11–15), the general aim (lines 103–108), Section 2.5 (lines 227–229), the description of the ANOVA in Section 3.3 (lines 423–430), and the discussion and conclusions (lines 471–484; 581–611).
2. “Participation will lead to” in H1 has been replaced by “students will show significantly higher post-test scores than pre-test scores in intrinsic motivation, enjoyment, self-confidence and resilience” (lines 92–94). H4 has been rewritten in equivalent terms (lines 101–102).
3. “Predictors of intrinsic motivation” has been replaced by “variables statistically associated with intrinsic motivation” in the abstract (lines 28–30), in H3 (lines 98–100), in the third specific objective (lines 116–118), and in the discussion and conclusions (lines 493–500; 597–600).
4. “The programme was effective and equitable for both genders” has been removed and replaced by “there was no evidence that pre–post change differed between boys and girls”, both in Section 3.3 (lines 464–469) and in the conclusions (lines 601–604).
5. “Parkour-based AE appears to contribute to emotional and personal development” has been replaced, in the conclusions (lines 587–596), by “post-test scores on intrinsic motivation, enjoyment, self-confidence and resilience were significantly higher than pre-test scores, and scores on these emotional and personal development variables also increased following the programme; however, these changes cannot be attributed uniquely to the programme, given the absence of a control group and the alternative explanations described in the Limitations section”.

We have additionally suppressed two further sentences that could be read as causal claims: the formulation that the program “can increase intrinsic motivation” at the start of the discussion has been replaced by “a parkour-based AE program may be associated with higher post-test scores” (lines 476–478); and the closing sentence of the conclusions, which previously stated that “this proves that, using innovative models, PE can achieve socio-emotional goals”, now reads “these findings are in line with the idea that, using innovative models, PE may contribute to socio-emotional goals and life skills that transcend the school environment” (lines 608–611).

Closing.

We hope that the revised version now presents the study consistently as a single-arm exploratory pre–post study that documents post-test improvements and statistical associations among variables, and not as evidence that the programme caused those improvements. We have not changed the design, the analyses or the substantive findings; the changes are confined to wording, to the description of the design, and to the limitations section. We are grateful to the reviewer for insisting on this distinction, which has substantially improved the alignment between what the study can and cannot claim.

 

On behalf of the authors,

[Corresponding author]

Round 3

Reviewer 2 Report

Comments and Suggestions for Authors

Thank you for the careful and constructive revision. The manuscript has improved substantially. The study is now much more consistently presented as a single-arm pre–post design rather than as a causal test of programme effectiveness. The abstract, design section, aims, objectives, regression framing, discussion, limitations, and conclusions have all been revised in a way that better aligns the claims with the design. In particular, the abstract now explicitly states that the findings should be interpreted as preliminary descriptive evidence of pre–post change and associations, not as a causal test of effectiveness . The design section is also clearer in distinguishing the pre–post component from the cross-sectional associative regression analyses . These revisions address the main concern raised in the previous review.

There remain, however, a small number of places where the wording should still be tightened. First, the sample size/power paragraph states that the sample “ensures a high statistical power” and that the “high power observed in the main contrasts performed supports the robustness of the obtained results” . This is too strong given that the clustered structure of the data was not modelled. The later limitations section appropriately acknowledges that students were nested within classes/schools, that intraclass correlations were not computed, and that standard errors may have been underestimated . The earlier power/robustness claim should therefore be softened, for example by stating that the sample was adequate for the planned analyses, while recognising that precision estimates may be affected by the unmodelled clustering.

Second, there are still a few residual causal or effectiveness-based phrases. The sentence that “the program was carried out as planned and its effects could be verified” should be revised, because “effects could be verified” implies causal evidence that the design cannot provide . A safer formulation would be: “The program was carried out as planned, and implementation was monitored through session checklists.” Similarly, in the discussion and conclusion, wording such as “favoured more self-determined behaviours” should be softened to “was accompanied by higher self-determined motivation scores” or similar .

Third, the ethics statement requires correction before publication. 

Overall, the revision is much stronger and now largely addresses the central concern about overstatement. I recommend acceptance after minor revision, provided the authors remove the remaining causal/effectiveness phrasing, moderate the robustness/power claims, and complete the ethics statement.

Author Response

Dear Editor, dear Reviewer 2,

Thank you very much for the positive assessment of the revised manuscript and for recommending acceptance after minor revision. We have now dealt with the three points still raised in the report. To make this round easier to follow, only the changes introduced in response to the present review are highlighted in blue; the revisions made in the earlier rounds, which had already been accepted, now appear in black as part of the running text. The line numbers given below refer to this latest version.

On the sample size and statistical power claim.

We accept that the earlier wording was too strong, since the clustered structure of the data had not been modelled. The relevant passage in the sample section has therefore been rewritten (lines 140-145). It no longer claims that the sample “ensures a high statistical power” or that “the high power observed supports the robustness of the obtained results”. The text now indicates that the sample can be considered adequate for the planned analyses, and adds that the data have a clustered structure (students nested within classes and schools) that was not modelled analytically, so that precision estimates may be affected by this unmodelled clustering. This passage is now aligned with the limitation that was already acknowledged later in the manuscript.

On the residual causal and effectiveness-based phrases.

We have corrected both phrases pointed out by the reviewer. In the TIDieR description, item 12 (lines 267-268) previously stated that “the program was carried out as planned and its effects could be verified”; it now reads “the program was carried out as planned, and implementation was monitored through session checklists”, which describes the fidelity monitoring without suggesting causal evidence. In the conclusions (lines 585-586), “favoured more self-determined behaviours toward the practice of PE” has been changed to “was accompanied by higher self-determined motivation scores toward the practice of PE”. We went through the discussion again looking for similar wording: the only remaining use of the verb “favours” refers to a general postulate of Self-Determination Theory and is attributed to the cited literature, not to an effect of our own programme, so we have kept it as it was.

On the ethics statement.

The Institutional Review Board Statement, which previously still contained the MDPI template text, has now been completed (lines 622-624). It reads: “The study was conducted in accordance with the Declaration of Helsinki, and approved by the Ethics Committee of the University of Granada (UGR) (protocol code 5306/CEIH/2025, approved on 22 October 2025).” The protocol code matches the one already reported in the Procedure section. We have also completed the Informed Consent Statement (lines 625-626), specifying that informed consent was obtained from the participants and, as they were minors, from their parents or legal guardians.

We trust that these final adjustments resolve the three remaining points. We thank the reviewer for the thorough work carried out across the successive rounds, which has clearly improved the manuscript.

On behalf of the authors,