Physical inactivity and sedentary behavior (SB) are among the leading risk factors for global mortality [1]. Each year, physical inactivity is responsible for >5 million deaths worldwide [2]. In contrast, regular physical activity (PA) prevents the risk of developing chronic diseases [3,4], limits their progression [5,6], and reduces early mortality [7]. In parallel, there is a dose-response relationship between total sedentary time per day and overall mortality [7]. Meta-analyses demonstrate that the risk of mortality in adults increases steadily with a sedentary lifestyle of >3 hours per day and more significantly when this time exceeds 7 hours per day [8]. However, recent studies have suggested that high levels of PA could attenuate or even eliminate the deleterious effects of SB on overall mortality [9].

In this context, it is urgent to develop interventions that can effectively change PA. Therefore, digital health interventions constitute a new opportunity to take care of patients by involving them in their treatment in a dynamic and interactive way. Gamification is a promising avenue to capitalize on the efficacy of digital interventions. Gamification is defined as the use of game design elements in nongame contexts [10]. By integrating game mechanisms in interventions that are initially devoid of them, the purpose of gamification is to integrate into daily life the ingredients that make games enjoyable to motivate participants to engage in PA [11]. The use of motivational affordances created by gamification can influence psychological (eg, motivation, attitude, and enjoyment) and physical outcomes (eg, physical capacities) [12] and therefore appears as a potentially powerful technique for behavior change.

By gamifying PA, participants are encouraged to move and walk to play, which tends to make their activities more enjoyable and playful [13]. Unlike serious games, which refer to the use of a full-fledged video game for educational or health purposes (ie, a video game in its entirety as opposed to selected elements or individual features of a game) [10] and require a dedicated time, a location, and implementation [14], gamification techniques are relatively open to varying situational modes of engagement [10] and concern instead global PA in all aspects of daily life (eg, walking, running, or gardening). Gamification is made possible by mobile technologies and wearable devices that can track and collect daily activities in a continuous and web-based manner. This allows for intervening directly on the lifestyle of individuals without adding material or time constraints for the participants.

However, several literature reviews [13,15,16] have reported inconsistent results concerning the use of gamification in behavioral interventions, with some studies demonstrating positive effects and other studies providing more mixed effects. These reviews also emphasized the lack of high-quality studies and highlighted the need for more rigorous trials to isolate the impact of gamification (ie, randomized controlled trials [RCTs]). Importantly, Koivisto and Hamari [15] suggested that the effects of gamification could be smaller when using rigorous experimentation. In sum, these reviews indicate that there is no clear evidence of the effectiveness of gamified interventions. Nevertheless, no meta-analysis has been conducted yet. Quantifying the effect size of gamified interventions and identifying moderators of this effect would provide important information about the effectiveness of such interventions. Moreover, a meta-analysis appears as timely, as there are now enough RCTs to conduct such an analysis.

This study is the first to quantify the effects of gamified interventions on PA. Beyond the effect during or just after the intervention, we also seek to evaluate the long-term effects to determine the health relevance of these interventions. Indeed, we reasoned that to be considered effective, gamification must sustain its impacts over the long term and offer more than a short-term novelty effect [11]. The generalizability of gamification to different user populations is also a major issue because it would determine whether gamification can be introduced in health care settings with patients or it is more suited in prevention for healthy audiences.

The objectives of this systematic review and meta-analysis are to answer these research gaps by (1) evaluating the effect of gamified interventions on PA and SB, (2) assessing the long-term or sustained effects of gamified programs, and (3) evaluating the generalizability of gamification across different populations.

This review was conducted according to the PRISMA (Preferred Reporting Items for Systematic Reviews and Meta-Analyses) guidelines [17]. Following recommendations to minimize bias and provide evidence of a priori analysis intentions [18], the study was preregistered under the international prospective register of systematic reviews (PROSPERO; registration number: CRD42020186882) and on the Open Science Framework (OSF) [19]. Moreover, all materials and data are available on the OSF page of the project to facilitate reproducibility and transparency of this review [20].

We conducted a systematic literature search using five electronic databases: PubMed, Embase, Scopus, Web of Science, and the Cochrane Central Register of Controlled Trials. We combined alternate terms and keywords representing synonyms for the outcomes (PA or SB), intervention (gamification), device (eHealth), and trial (see Table S1 in Multimedia Appendix 1 [21-36] for an overview of the terms used). The search strategy was reviewed by an academic librarian. All databases were searched individually from January 1, 2010 (2010 being the date of the widespread adoption of the term gamification [10]), to December 31, 2020, and the research was restricted to English-language texts. The complete search equations for all databases are available in Multimedia Appendix 1. In addition, we complemented our search with reference harvesting from the included studies and overview articles.

Studies were eligible for inclusion if they were RCTs and if they met other criteria based on the participants, interventions, comparators, and outcomes framework.

In total, 2 authors (AM and AC) independently screened the titles and abstracts resulting from the search. Full texts of the potential included studies were checked before inclusion. Disagreements were resolved by discussion or by consulting a third author (MD), and agreement was measured using the κ statistic. A complete list of excluded studies is available on the OSF page of the project.

In the data collection process, AM and AC extracted data independently and were blinded to each other using a predetermined and tested template. Disagreements were resolved by discussion or consultation with a third author (MD). Extracted data included the results of each study and three types of potential moderators:

For each eligible study, 2 reviewers (AM and AC) assessed the risk of bias using the purpose-built Cochrane risk of bias tool (Table 8.5 in the Cochrane Handbook for Systematic Reviews of Interventions [38]), which evaluates 7 domains (sequence generation, allocation concealment, blinding of participants and personnel, blinding of outcome assessment, incomplete outcome data, selective outcome reporting, and other risk of bias). A judgment of the potential risk of bias was made from the extracted information and rated as high risk, low risk, or unclear if the related information was not available. These evaluations of bias are reported in the review and included in the analysis, and a measure of agreement with the κ statistic was calculated. After the full assessment, we decided not to present the item blinding of participants and personnel in the review because it was similar for all studies, which were rated as high risk, blinding being unfeasible for this kind of intervention.

First, data were synthesized in a qualitative review assessing the key elements of the studies and highlighting intervention differences. This qualitative review integrates all studies that met the eligibility criteria, including those for which we were unable to extract the data.

For the quantitative analysis, means and SDs of continuous PA or SB outcomes from individual studies were compiled when available or estimated using the method by Hozo et al [39] when median and IQR were reported. When the necessary data were not available in the original article, we first requested them from the authors. If data could not be obtained, we extracted them from the graphs when available. If this was not possible, we excluded the study from the quantitative analysis.

A global meta-analysis was conducted to obtain a summary effect. In addition, when sufficient data were available (ie, 4 studies or more reporting an outcome), we conducted different meta-analyses for each specific outcome (steps, MVPA, and time in SB) and for the follow-up effect. To address the nonindependence of data caused by study effect, random-effects models [40] were preferred to the usual statistical tests. In addition, the Hartung–Knapp–Sidik–Jonkman method was used to reduce the production of false positives inherent to the DerSimonian–Laird method [41] and to obtain more robust estimates of variance. Continuous outcomes were analyzed using standardized mean difference (SMD) to account for different measurement instruments or mean difference (MD) when the measurements were close enough. We computed Hedges g [42] for effect sizes, which is similar to Cohen d but corrects for small sample bias, which are recurrent in the studies included. Thus, a Hedges g of 0.2 represents a small effect; 0.5, a moderate effect; and 0.8, a large effect [43]. We computed SMDs for outcome scores after the intervention (presented in the review) and change-from-baseline outcomes. Scores on postintervention effect sizes refer to treatment group results compared with the control group results after interventions. Change-from-baseline score effect sizes were calculated as a comparison between the treatment group pre–post effect size and control group pre–post effect size.

For studies that included multiple outcomes, we kept in the main analysis the primary outcome targeted in the initial article. If none of the PA outcomes reported by a study were the primary ones, we selected the one that was the most relevant from the perspective of the intervention and the original experiment. In designs with multiple time measurements, the assessment that was the most proximal to the end of the intervention was conserved. A time assessment had to be performed >2 weeks after the end of the intervention to be included in the follow-up analysis. When studies included multiple intervention groups with gamification features, they were combined into one group following the formulae recommended by the Cochrane Handbook [38]. Studies including multiple control groups could be integrated into different subgroup analyses if they compared their gamified intervention to both an active and an inactive control group.

Statistical heterogeneity was tested using forest plots and the I² statistic, which is the most common metric for measuring the magnitude of between-study heterogeneity and is easily interpretable (0%-40% might not be important, 30%-60% may represent moderate heterogeneity, 50%-90% may represent substantial heterogeneity, and 75%-100% may represent considerable heterogeneity) [44]. We conducted different influential analyses to address between-study heterogeneity. We first explored the presence of outliers, defined as studies with CIs that do not overlap with the CI of the summary effect. We also performed leave-one-out analyses, which recalculated the summary effect several times, with 1 study omitted each time. Finally, we performed a Baujat plot [45], which is a diagnostic plot to detect sources of heterogeneity in the meta-analysis by comparing the contribution of each trial in the pooled effect with the overall Cochran Q test for heterogeneity.

We applied different methods to detect publication bias (funnel plot, Egger regression test [46], and Duval and Tweedie trim-and-fill procedure [47]). In addition, another approach to determine the evidential value of studies included in the analysis is to check the statistical power of individual studies. Therefore, we performed a sunset funnel plot [48], which is a funnel plot variant that visualizes the statistical power of each study included in the meta-analysis based on the summary effect size.

Thus, sensitivity analyses were conducted to address studies with a high risk of bias or a strong heterogeneity in the sample or studies identified as outliers. Subgroup analyses were conducted to explore possible sources of heterogeneity and test for population differences. Therefore, we conducted tests for subgroup differences using a random-effects model. In addition, moderation analyses were performed to explore the impact of potential explanatory variables and moderators on the effect size with meta-regressions when sufficient data were available (ie, at least 10 studies for each explanatory variable [38]). The results were expressed as regression coefficient estimates, 95% CIs, and P values.

For crossover trials, we first checked whether carry-over or period effects were problematic in the original texts of studies. For cluster randomized trials, we checked if the influence of the different clusters was not too important, analyzing the values of the intraclass correlation coefficient in the studies. Then, in the absence of sufficient information in the published articles, we addressed these studies as traditional parallel trials. Nevertheless, this procedure increased the probability of a unit of analysis error. Therefore, we performed sensitivity analyses without clusters and crossover trials to test the robustness of our results.

A summary of the analytical procedure is available in Multimedia Appendix 1 (Figure S1). Analyses were performed on R (The R Project for Statistical Computing) using the dmetar package [49]. Risk of bias summary and risk of bias graphs were made via the robvis R package [50].

We screened the titles and abstracts of 1626 articles, and 51 full-text articles were assessed for eligibility according to the inclusion criteria. Finally, 18 articles [21-36,51,52] were included in the qualitative analysis and 16 were included in the meta-analysis (Figure 1). The κ value of agreement for the screening phase was 0.64 between the 2 authors, reflecting good agreement [53].

Table 1 provides an overview of the characteristics of the included studies. The 16 studies included in the quantitative analysis involved 2407 participants aged 9-73 years (mean 35.7 years, SD 17.2 years), with sample sizes ranging from 20 to 602. Overall, 67% (12/18) of studies included adult participants [22,24-30,32,34-36] and 33% (6/18) of studies included adolescents (ie, <18 years [21,23,31,33,51,52]). A total of 22% (4/18) of studies included patients with chronic diseases (ie, obesity [27,36], type 2 diabetes [35], and cardiovascular disease [28]).

A total of 6 trials were conducted in Europe; 4 in the United States; 3 in Australia and New Zealand; 3 in Canada; and 2 in Asia. Studies were published between 2014 and 2020, with 39% (7/18) published after 2018.

Most studies were based on a smartphone app (n=10; [23,28,30-35,51,52]), web-based (n=3; [21,24,29]), or both (n=4; [22,26,27,36]). Nishiwaki et al [25] used a pedometer with computerized game functions. The duration of the intervention varied from 1 to 24 weeks, with a mean of 11.8 weeks, and the most common length was 24 weeks. The most used game mechanics were internet-based rewards, such as badges, medals, or trophies (13/18, 72%; [21,22,24,26-28,30,32,33,35,36,51,52]), teams or leagues (13/18, 72%; [21-24,26,27,29,32-34,36,51,52]), levels (9/18, 50%; [22,26,27,29,33,35,36,51,52]), points or scores (7/18, 39%; [22,26,27,29,30,35,36]), or the presence of a leaderboard (7/18, 39%; [22,29,30,33,34,51,52]). Almost all studies included social incentives such as team collaboration, social networking, and messaging facilities in their intervention (15/18, 83%; all except Nishiwaki et al [25], Direito et al [31], and Höchsmann et al [35]).

Studies comparing gamified interventions with active control groups used a similar intervention without game elements (ie, an equivalent nongamified app [30-32] or a self-monitoring intervention with wearables or activity monitors [25-27,34,36]).

In most studies, the interventions were based on theoretical models. A total of 6 studies [21,30,31,33,51,52] were based on the self-determination theory [54]; 5 [22-24,32,34] on sociocognitive models (ie, the transtheoretical model [55], the social cognitive theory [56], the theory of planned behavior [57], and the health action process approach [58]); and 3 [26,27,36] on behavioral economics models.

Outcomes measured in trials were diverse: they used either total PA duration or MVPA duration, SB duration, daily step count, walking duration, or active minute count. A total of 13 experiments measured PA objectively using devices such as triaxial accelerometers (n=7; [21,28,31-33,51,52]), wearable devices for the general population (ie, Fitbit, Garmin, Polar, and Withings monitors; n=6; [23,26,27,34-36]), pedometers (n=1; [25]), or smartphones (n=1; [30]), and 5 assessed PA with self-reported measures (International Physical Activity Questionnaire [22], Physical Activity Questionnaire for Adolescents [31], Active Australian Survey [24,32], or other [29]). A total of 6 trials [21,24,26,27,32,36] completed a follow-up assessment from 12 to 30 weeks (mean 14.4 weeks) after the end of the intervention.

A total of 2 studies [51,52] were excluded from the meta-analysis and were only integrated in the qualitative review because we were unable to extract their results.

The 2 authors extracted the risk of bias data with a κ coefficient of 0.79, which is synonymous with excellent agreement [53]. Multimedia Appendices 2 [21-36] and 3 present the authors’ judgments about each risk of bias item presented as percentages across all included studies in the meta-analysis and an overview of the different biases for each study. Overall, 1 study [28] was rated as high risk for sequence generation because assignments were based on recruitment order. Therefore, this study was also at a high risk for allocation concealment. A total of 3 studies [24,29,30] were at high risk of bias for the blinding of outcome assessment item because they measured PA using only self-reports. In total, 5 studies [23,29,30,49,52] were at high risk of bias for the incomplete outcome data item because they reported high dropout rates and did not include intention-to-threat analyses and 5 studies [25,28,29,31,52] were rated at unclear risk for the selective outcome reporting item because they had not been preregistered or published in a protocol-study. Finally, 2 studies had other high risks of bias. The first one [25] was a crossover trial conducted without a washout condition, and the other one [21] was a cluster randomized trial with no control of clustering, no consideration of the clustering in the statistical analysis, and no test of baseline differences among groups.

Overall, the SMD after the intervention for all PA outcomes (MVPA, daily step count, number of active minutes, and walking time) was a Hedges g of 0.43 (95% CI 0.03-0.82; I²=86%; Figure 2), representing a statistically significant small to medium effect. Similarly, we found a statistically significant SMD effect of a Hedges g of 0.38 (95% CI 0.07-0.69; I²=79%) for pre–post change scores.

Only 3 studies [23,28,31] assessed sedentary time as an outcome. Owing to this small sample size, the meta-analysis was not performed on this outcome.

In the first analysis, substantial statistical heterogeneity was observed. To address between-study heterogeneity, we first looked for the presence of outliers. A total of 3 studies were considered as outliers [21,25,35], and after removing them, we still obtained a significant effect of a Hedges g of 0.34 (95% CI 0.17-0.51) with moderate heterogeneity (I²=58%).

Leave-one-out analyses showed that sequential removal of each study did not have an important impact on the general effect size, with effect sizes ranging from a Hedges g of 0.33 (95% CI 0.00-0.66; I²=84%) to a Hedges g of 0.48 (95% CI 0.13-0.83; I²=78%; Figure S2 in Multimedia Appendix 1).

The Baujat plot (Figure S3 in Multimedia Appendix 1) shows that 4 studies explained more heterogeneity than the others, more specifically, the study by Corepal et al [21] with a heterogeneity contribution of 40.13 and an effect size influence of 3.27.

Therefore, we excluded studies with a high or unclear risk of bias. After doing so, the effect was not significant (Hedges g=0.33, 95% CI –0.16 to 0.81; I²=78%).

The inclusion of crossover and cluster randomized trials in the meta-analysis may lead to biases. Thus, we excluded these designs from the analysis and obtained a statistically significant effect of g=0.49 (95% CI 0.05-0.92; I²=67%).

Finally, we decided to exclude articles by Corepal et al [21] and Nishiwaki et al [25] in the sensitivity analyses (which have been repeated afterward for each analysis) considering their influence on the pooled result, their contribution to overall heterogeneity, and their huge risk of bias (no control of clustering, no statistical consideration of clustering, and no test of baseline differences among groups in the study by Corepal et al [21] and no washout period and very low power for the study by Nishiwaki et al [25]). After doing so, we obtained a statistically significant effect of a Hedges g of 0.42 (95% CI 0.14-0.69; I²=74%).

We found no statistical differences in the effects between studies with participants with chronic diseases or healthy participants (Cochran Q=0.73; P=.39), between adults and adolescents (Cochran Q=0.26; P=.61), between studies with objective (devices) or self-reported PA outcomes (Cochran Q=0.23; P=.63), between active or inactive control groups (Cochran Q=0.01; P=.92), and between short- and long-term interventions (less or more than 12 weeks; Cochran Q=0.60; P=.44).

When performing the sensitivity analysis, there was a statistically significant effect of intervention on PA in adults (Hedges g=0.36, 95% CI 0.03-0.69; I²=71%; Figure S4 in Multimedia Appendix 1), on healthy people (Hedges g=0.35, 95% CI 0.15-0.55; I²=63%; Figure S5 in Multimedia Appendix 1), when the PA measure was objective (Hedges g=0.45, 95% CI 0.08-0.82; I²=80%; Figure S6 in Multimedia Appendix 1), when the PA measure was self-reported (Hedges g=0.24, 95% CI 0.08-0.39; I²=0%; Figure S6 in Multimedia Appendix 1), and for short interventions of <12 weeks (equivalent to a 3-month program; Hedges g=0.44, 95% CI 0.19-0.69; I²=16%; Figure S7 in Multimedia Appendix 1).

Moreover, subgroup analyses allowed us to examine the effect of gamified interventions when compared with inactive control groups and active control groups. After sensitivity analyses, we found a statistically significant effect of gamified interventions, both when compared with inactive control groups (Hedges g=0.58, 95% CI 0.08-1.07; I²=81%; Figure S8 in Multimedia Appendix 1) and when compared with active control groups (Hedges g=0.23, 95% CI 0.05-0.41; I²=37%; Figure S8 in Multimedia Appendix 1).

The age of participants (β=.01, 95% CI –0.02 to 0.04; P=.39), their gender (β=.01, 95% CI –0.01 to 0.02; P=.47), their BMI (β=.04, 95% CI –0.16 to 0.09; P=.53), the duration of the intervention (β=-.01, 95% CI –0.06 to 0.04; P=.74), or the number of game mechanics included in the intervention (β=.01, 95% CI –0.17 to 0.19; P=.91) were not statistically significantly associated with an increase in PA.

Lack of data precluded further meta-regressions, such as comparisons of leisure PA, or test of moderators, such as the impact of social incentives or the theoretical model used to develop the intervention.

First, an inspection of the funnel plot showed that the effect sizes of individual studies were relatively symmetrically distributed around the pooled effect size. This observation was supported by the Egger test of the intercept, which indicated no asymmetry in the funnel plot (b₀=1.38, 95% CI –0.83 to 4.77; P=.19). We then applied a bias-correction technique, the trim-and-fill method, which indicated that 3 studies were missing at the bottom left of the funnel plot to obtain a full symmetry. After imputing the effect sizes corresponding of these missing studies to obtain a totally symmetrical funnel plot (Figure 3), the bias corrected summary effect was of a Hedges g of 0.24 (95% CI –0.24 to 0.73).

Finally, the sunset funnel plot (Figure 4) showed significant differences in power among studies, with some characterized by very low statistical power (7 studies under 45% power and 4 studies under 18%). The median power of all the tests was 63%.

The quality of evidence (grading of recommendations assessment, development, and evaluation, [GRADE]) in the included studies after sensitivity analyses for short-term PA, long-term PA, MVPA, steps, and daily steps was scored from high to low (Table 2). The quality was downgraded for some outcomes because of high heterogeneity, high risk of bias, or imprecision owing to large CIs. Summaries of the various meta-analysis conducted in this review both on postintervention scores and pre–post intervention change scores are presented in Multimedia Appendix 1 (Figures S9-S11).

This meta-analysis is informative regarding the effectiveness of gamified interventions. In view of the observed heterogeneity, the next step will be to investigate its causes from an interventional and theoretical perspective. Gamified interventions involve multiple interacting elements, and it is crucial to estimate the weight of each element in the behavior change process and how they interact with each other. Is it game mechanics, the implementation of behavior change techniques, or the presence of social interactions that make gamification effective? Unfortunately, the small number of studies included in the meta-analysis impeded us from conducting in-depth moderation analyses to answer this question. To better understand these relations, it is essential that both the development and assessment of gamified interventions be central, transparent, evidence-based, context-aware, and research-oriented [70]. Moreover, if theoretical psychological models are often mentioned in the introduction of articles included in the review (Table 1), few have investigated the psychological mechanisms of their interventions in the field [22,31,71]. Future studies should explicitly discuss motivational theory and systematically test the effect of gamification on psychological outcomes known to be involved in behavior change (eg, self-efficacy, attitudes, and intention) to better understand its mechanisms. The consideration of personality traits and psychological variables to determine behavioral phenotypes [68] is a promising way to evaluate participant’s responses to the interventions.

The findings from this meta-analysis allow us to draw and discuss future work concerning the gamification of PA and SB. First, future trials should be conducted with more adequately powered sample sizes and should be strictly multiple arms–RCTs to isolate the effects of gamification elements and better understand gamification mechanisms. Second, the long-term effects are currently the main challenge of health interventions. Thus, it is essential to investigate the evolution of the effects of gamified interventions over time. Therefore, there is a need for more long-term follow-up measurements. In addition, the potentialities of digital technologies and their capacity to collect a large amount of real-world data could be used to assess the evolution patterns of the effect, allowing the detailed identification of its sustainability and evolvement or even make forecasts via time series analyses. Third, to our knowledge, only 1 team of researchers worked on a gamified intervention targeting SB by introducing sedentary breaks as a gaming part [72]. Following this line of research, it could be interesting to develop gamified interventions affording participants to take more sedentary breaks. Finally, the cost-effectiveness ratio of gamified interventions may be better than that of many current interventions, considering the ease of implementation and generalizability of gamification. However, this assertion will have to be tested in future trials, including economic analyses.

In light of our results, gamified interventions appear to be a promising avenue to promote PA in different populations both in prevention in healthy people and in the treatment of chronic diseases. Gamified interventions have many benefits for participants with chronic diseases, such as empowerment of participants by improving their self-management skills, an effect across broad audiences enabling to target different types of pathologies, and an everyday life fit and easy implementation. Similar to other digital health processes, gamification makes it possible to address more patients, especially those who are isolated from health care facilities. Importantly, gamified interventions are especially pertinent during a health pandemic, such as the COVID-19 outbreak, in which PAs and social interactions are restricted because of lockdown or teleworking and where structured PA possibilities are limited both indoors and outdoors. Gamifying walking and daily activities is, in this context, a great way to improve PA and limit SB of individuals in addition to providing social interaction among players. In the meantime, the face-to-face management of chronic diseases is usually suspended during the pandemic, which underlines the importance of offering remote supervision of PA.

Nevertheless, in view of the weaker postintervention effect, this study suggests that a one-shot intervention is not sufficient. A more interesting design would be to address multiple gamification doses during or after the course of treatment to obtain a sustainable implementation of the PA behavior. This configuration would also provide an ideal duration of intervention to avoid exhausting the participants with gamified interventions for >12 weeks.

To our knowledge, this is the first meta-analysis to quantitatively evaluate the effects of gamification on PA. This review has several other strengths. First, we conducted a comprehensive search strategy using multiple databases in collaboration with an academic librarian. Second, all stages of the review (screening and data extraction) were independently realized by 2 reviewers. Finally, various novel publication bias analyses and influence analyses were conducted in parallel with different subgroup analyses and meta-regressions.

However, some limitations of this work must be mentioned. Overall, the meta-analysis included a small number of studies, and some articles were feasibility or pilot trials. Therefore, several trials included small sample sizes and were highly underpowered. Some studies were conducted with a high risk of bias. One of the main limitations of this work is the impossibility of demonstrating that the effect of gamified interventions is led by gamification itself given the lack of research examining this question. Finally, in the main analysis, we included diverse PA outcomes evaluating similar constructs but which are slightly different in practice. Moreover, not all included outcomes were objectively measured. As the field matures and new trials are published, an update of this work will be important to confirm these preliminary results.

To conclude, gamified interventions appear to be a promising avenue for promoting PA in various populations. Influencing primarily the number of daily steps of the participants, gamification is an interesting way to improve daily PA and appears more efficient than equivalent nongamified interventions, such as mobile health apps. However, if the effect of gamification persists during follow-up, suggesting that gamified interventions are more than a novelty effect, this effect decreases with time with a smaller long-term effect. The integration of gamification in more global health care interventions could be a way to address this limited sustainability. Future rigorous trials are required to explore these perspectives.