Accurate measurement of knee joint kinematics is fundamental to the assessment and management of musculoskeletal conditions, including anterior cruciate ligament reconstruction recovery and knee osteoarthritis rehabilitation. Clinicians routinely monitor knee flexion and extension range of motion (ROM) to guide treatment progression, set discharge criteria, and evaluate surgical outcomes. In conventional clinical practice, the universal goniometer is used for static ROM measurement and offers acceptable intrarater reliability when used by trained clinicians [1]. However, the goniometer requires in-person contact, is limited to static or quasistatic postures, and cannot capture the dynamic joint behavior that characterizes functional tasks such as squatting, sit-to-stand transfers, and single-leg balance—tasks that more closely reflect the demands of daily living and return-to-activity benchmarks.

Laboratory-based, marker-based, motion-capture systems (eg, Vicon and Qualisys) are commonly used reference methods for 3D joint-kinematic analysis. However, they require dedicated space, specialized hardware, marker placement by trained personnel, and substantial postprocessing expertise [2,3]. These requirements limit their availability for routine or remote assessment, where neither an in-person goniometer nor laboratory motion capture is readily deployable.

The rapid development of markerless pose estimation technologies has created new possibilities for accessible, low-cost movement analysis. Deep learning–based frameworks can estimate joint positions from standard video without physical markers. Stenum et al [4] demonstrated the feasibility of automated gait analysis from single-camera 2D pose estimation. Among single-camera 2D approaches, Gupta et al [5] compared MediaPipe Pose with Kinovea 2D video annotation for knee flexion during gait, reporting a Pearson correlation of 0.941 and a mean absolute error (MAE) of 5.88°. Langley et al [6] compared both smartphone-based Deep Vision and Kinovea with 3D motion capture in patients with knee osteoarthritis. For Deep Vision, limits of agreement for peak flexion and ROM were within or equal to the study’s clinical thresholds. Koul et al [7] reported high intrarater reliability for knee flexion measurements using DETROM (intraclass correlation coefficient [ICC]=0.98) in healthy adults. Agreement with a universal goniometer was evaluated separately using Bland-Altman analysis. Akturk et al [8] applied MediaPipe to joint-angle and joint-moment estimation during sit-to-stand transfers, extending single-camera pose estimation to a functional task.

Multicamera and 3D markerless systems have also been evaluated during functional tasks. Lima et al [9] evaluated OpenCap, a multicamera system for 3D kinematic reconstruction, across functional tasks. For single-leg squatting, root mean square error (RMSE) ranged from 2.9° to 13.6° across joint angles. Peak-angle intersession ICCs across joints were 0.60 to 0.92 for single-leg squatting and 0.62 to 0.93 for the jump phase of a countermovement jump. Yoma et al [10] reported mean between-day root mean square differences <5° and mean ICCs of 0.77 to 0.83 across kinematic variables for Theia3D during single-leg squat and landing tasks, although hip flexion errors exceeded 5°. These findings provide context for single-camera studies, but differences in tasks, populations, and analysis methods limit direct performance comparisons.

Single-camera markerless measurements can be affected by self-occlusion and out-of-plane motion [3]. This study therefore focused on task-dependent agreement, the consistency of the 2D reference annotations, and repeated-session uncertainty. These measurement properties require evaluation before longitudinal or remote uses can be considered.

To our knowledge, few studies have evaluated an open-source single-camera pose-estimation system across multiple knee-related functional tasks in one cohort while examining complementary measurement properties, including agreement with a clinical instrument and a 2D video reference, interrater agreement of that 2D reference, and exploratory repeated-session performance. The selection and reporting of measurement properties were informed by COSMIN (Consensus-Based Standards for the Selection of Health Measurement Instruments) terminology [11].

The purpose of this study was to evaluate the MediaPipe BlazePose Heavy model for knee-flexion measurement in healthy young adults. We examined (1) interrater agreement of Kinovea 2D video annotation; (2) static agreement of BlazePose with goniometer-set target flexion across 4 angles; (3) dynamic agreement of BlazePose with Kinovea during squat, sit-to-stand, and bilateral single-leg stance; and (4) exploratory repeated-session agreement of BlazePose, Kinovea, and their between-method differences. We expected performance to vary by task, joint angle, and detection quality. This study did not evaluate absolute 3D kinematic accuracy, clinical populations, or cross-device equivalence.

This cross-sectional validation study evaluated agreement of smartphone-based MediaPipe BlazePose knee-flexion estimates with goniometer-set targets for static positions and with Kinovea 2D video annotations by 2 trained raters for dynamic functional tasks. Secondary analyses assessed interrater agreement of the Kinovea annotations and exploratory repeated-session performance in a 4-participant subsample. Kinovea was treated as a 2D reference, not as an absolute biomechanical standard.

We recruited 15 healthy adults (8 men, 7 women; mean age 20.8, SD 0.6, range 20‐22 years; mean height 171.1, SD 9.4 cm; mean weight 70.7, SD 15.7 kg; mean BMI 23.9, SD 3.4, range 18.8‐31.3 kg/m²) via convenience sampling from a university community. Inclusion criteria were age 18 years to 45 years, no current lower-extremity pain, and ability to perform a full-depth squat independently. Exclusion criteria included a history of lower-extremity surgery, current lower-extremity injury, or any musculoskeletal condition limiting knee range of motion. The study was approved by the Academic Ethics and Integrity Review Committee of Shanghai Sanda University (approval number 2026006). All participants provided informed consent prior to data collection. The sample size of 15 was determined by feasibility considerations (participant availability and resource constraints within a single-semester data collection window) rather than an a priori power calculation; this is acknowledged as a limitation, and the achieved precision of ICC estimates is reported via 95% CIs throughout.

A subset of 4 participants (S01–S04) returned for an exploratory second session 21 days to 29 days after their initial session (median 25 d). The second session used the same static and dynamic task protocol. The dataset comprised 15 initial-session datasets plus 4 repeated-session datasets, yielding 342 videos processed through the BlazePose pipeline (228 static and 114 dynamic). The primary cross-sectional static analysis used the 180 Session 1 trials from S01-S15; the 48 Session 2 static trials were reserved for the exploratory repeated-session analysis.

All videos were recorded with the same iPhone 17 Pro rear camera mounted on a tripod in a lateral view at knee height and 2.0 m from the participant. The device was selected because it was available and readily accessible to the research team; using one device throughout kept acquisition hardware constant. Recordings used 1920×1080 H.264 video. Participants S03-S15 and all repeated-session recordings were captured at 60 frames per second (approximately 23 Mbps), whereas S01-S02 were captured at 120 frames per second (approximately 43 Mbps) during the pilot phase. Codec profile, pixel format (yuv420p), and color space (BT.709) were verified with FFprobe. Floor markings standardized participant and camera position. The study did not compare smartphones, lenses, device-specific image processing, or frame rates.

We placed 3 small reflective markers on each participant’s test limb to support manual Kinovea annotation: the greater trochanter (hip), the lateral femoral epicondyle (knee), and the lateral malleolus (ankle). The BlazePose pipeline used MediaPipe’s native keypoint detection and did not rely on these external markers. An anterior superior iliac spine marker was placed during some pilot trials but was not used in the final analysis pipeline. Participants wore dark-colored tight-fitting trousers or compression pants and a short-cropped top and were barefoot. The background was a plain pale wall with even lighting and no harsh shadows.

Two trained raters independently annotated task-specific target frame knee angles using Kinovea 2025.2. Each rater selected maximum clinical knee flexion for squat and sit-to-stand and a steady midstance frame for single-leg stance then digitized the greater trochanter, lateral femoral epicondyle, and lateral malleolus using the reflective markers as guides. The native 2D-included angle was converted to clinical knee flexion as 180° − included angle. Kinovea served as a 2D video-analysis reference; it was not assumed to provide absolute 3D joint kinematics.

Raters were blinded to each other’s annotations and to BlazePose output. Their mean clinical flexion angle was used as the Kinovea 2D reference for dynamic agreement, and their mean target frame time stamp was used for BlazePose time matching. High interrater agreement reduces uncertainty from rater inconsistency but does not remove systematic 2D reference error.

For the primary dynamic comparison, BlazePose was evaluated at the Kinovea-selected target time rather than at BlazePose’s automated video minimum. For each of the 210 observations, the mean of the 2 rater time stamps was calculated, and the closest time stamp in the BlazePose per-frame output was selected. The native-included angle at that frame was converted to clinical flexion before analysis. This separates target-time selection by the 2D reference from BlazePose angle estimation at that time.

Each of the 342 videos received a descriptive A-D quality assurance grade based on the proportion of frames with confidence ≥0.8: Grade A (≥80%), Grade B (50%‐79%), Grade C (20%‐49%), or Grade D (<20%). These trial-level labels did not determine inclusion, weighting, or statistical inference and are not equivalent to target frame detection success. For a post hoc descriptive acquisition sequence summary, participants were grouped as S01-S06, S07-S10, and S11-S15; these groups were used only to describe target frame confidence and failure rates, without inferential testing. Detailed grade and detection quality distributions are reported in Tables S1-S5 in Multimedia Appendix 1 .

The original analyses used Python 3.9.6, pingouin for ICCs, and scipy.stats. The revision-stage participant cluster analyses used Python 3.12.14, NumPy 2.3.5, pandas 2.2.3, and SciPy 1.16.2. ICC_2,1 was recomputed from the same ANOVA formula and verified against the frozen results. Figures were generated using matplotlib.

This study was approved by the Academic Ethics and Integrity Review Committee of Shanghai Sanda University (approval number 2026006, April 14, 2026). The study was conducted in accordance with the Declaration of Helsinki. All participants provided informed consent prior to enrollment.

The cross-sectional analysis included 15 healthy adults (8 men, 7 women; mean age 20.8, SD 0.6, range 20‐22 years; mean height 171.1, SD 9.4 cm; mean weight 70.7, SD 15.7 kg; mean BMI 23.9, SD 3.4, range 18.8‐31.3 kg/m²). All 15 participants completed the full data collection protocol without reported adverse events. Four participants (S01-S04; 2 men, 2 women) returned for the exploratory repeated-session assessment after 21 days to 29 days (median 25 d).

For the primary cross-sectional analyses, 180 static trials (15 participants × 12 conditions) and 210 dynamic Kinovea-annotated target-frame observations were available.

Figure 1 summarizes the task-specific interrater agreement, angle-specific static signed error, and task-specific conditional dynamic agreement with detection failure rates. Detailed results are presented in Tables 1–5 and Multimedia Appendix 1.

Overall interrater agreement for the Kinovea 2D clinical flexion annotations was high (ICC_2,1=0.999, cluster-bootstrap 95% CI 0.998 to 0.999; MAE=1.56°; n=210 observations from 15 participants; Table 2; Figure 2C). This indicates consistent annotation between these 2 raters but does not establish absolute accuracy against 3D kinematics.

Task-specific ICCs were 0.999 for squat, 0.885 for sit-to-stand, and 0.973 for single-leg stance. The sit-to-stand point estimate of 0.885 was less than the a priori descriptive benchmark of 0.90, and its cluster-bootstrap 95% CI was 0.804 to 0.918. Sit-to-stand had the largest interrater MAE (3.13°) and a clinical-flexion bias of +2.65° for Rater A minus Rater B. The lower sit-to-stand ICC may reflect the more gradual transition around peak flexion, which makes the selection of a single target frame less distinct than in squat; this is a plausible explanation rather than a demonstrated mechanism.

Across 180 static observations from 15 participants, ICC_2,1 was 0.874 (cluster-bootstrap 95% CI 0.770 to 0.953), MAE was 10.01°, and RMSE was 15.49° (Table 3; Figure 2A). These differences include uncertainty in target positioning and holding as well as BlazePose estimation and are reported without a universal clinical acceptability cutoff.

Signed error varied by target angle. BlazePose overestimated clinical flexion at 30° (+11.11°) and 60° (+10.18°) and underestimated it at 90° (−4.64°) and 120° (−10.60°). Dispersion was substantially wider at 90° and 120° than at 30° and 60°. This range compression did not support a single fixed correction across the tested angles and did not identify one causal mechanism.

Excluding the 3 static Session 1 videos reprocessed at the lower pose detection threshold changed static ICC from 0.874 to 0.870 and RMSE from 15.49° to 15.58°. This sensitivity analysis quantifies the effect of the protocol deviation; full results are reported in Multimedia Appendix 1 (Table S14).

Dynamic measurement was available for 177 of 210 (84.3%) observations. The remaining 33 of 210 (15.7%) observations had target-frame confidence <0.3. Availability reached 71 of 75 (95%) observations for squat, 58 of 75 (77%) observations for sit-to-stand, and 48 of 60 (80%) observations for combined single-leg stance. Failures occurred for 5 of 30 (17%) observations on the left and 7 of 30 (23%) observations on the right. Participant counts and distributions are reported in Tables S1 and S5 in Multimedia Appendix 1.

Failures were concentrated in S10 (11/14, 79%), S13 (6/14, 43%), and S12 (5/14, 36%). Kinovea flexion medians for failed versus retained observations were 113.2° versus 131.0° for squat, 89.0° versus 81.0° for sit-to-stand, and 10.2° versus 8.8° for combined single-leg stance. These are descriptive contrasts not evidence of why detection failed; only 4 squat observations failed. Quartiles, ranges, and participant counts are in Table S5 in Multimedia Appendix 1.

Detection performance also varied by acquisition group. Target-frame median confidence and failures were 0.939 and 2 of 84 (2%) observations, respectively, for S01-S06; 0.643 and 14 of 56 (25%) observations, respectively, for S07-S10; and 0.694 and 17 of 70 (24%) observations, respectively, for S11-S15. No recorded device nor encoding variable changed uniquely at S07 or aligned with the persistent later-group decrease; the known 120-to-60 frames-per-second change occurred earlier, between S02 and S03. Because lighting, exact camera geometry, exposure and focus, attire, and background were incompletely recorded, the cause remains unresolved.

Task-specific ICCs were 0.773 (95% CI 0.564 to 0.875; n=71, 15 participants) for squat, 0.632 (95% CI 0.455 to 0.726; n=58, 12 participants) for sit-to-stand, and 0.136 (95% CI −0.078 to 0.482; n=48, 15 participants) for combined single-leg stance (Table 4). Squat and sit-to-stand had high Pearson correlations (r=0.885 and r=0.896), but their absolute-agreement ICC point estimates were good and moderate, respectively. BlazePose overestimated clinical flexion by +6.17° and +6.43°, respectively. The restricted near-extension range in single-leg stance reduced between-participant variance and made the ICC sensitive to modest error; occlusion, out-of-plane rotation, perspective shortening, side selection, and landmark localization are additional plausible contributors.

Across 177 retained observations, the pooled cross-task ICC was 0.982 (cluster-bootstrap 95% CI 0.967 to 0.992), with bias +5.12° and repeated-measures LoA −11.30° to +21.55° (Figure 2B). This is a secondary descriptive mixture because between-task angle range inflates between-observation variance; it does not imply uniform agreement across tasks.

Participant mean results are provided in Table S18 in Multimedia Appendix 1. These compare the average retained measurements per person and task, not individual observations. The numbers averaged varied because of detection failures. Earlier exploratory participant-by-task summaries in Tables S10-S11 in Multimedia Appendix 1 are retained with their distinct units and unadjusted intervals explicitly identified.

In the all-output stress test, retaining all 210 numeric outputs produced the largest deterioration for squat, for which the ICC decreased from 0.773 to 0.428 and RMSE increased from 8.78° to 25.43°. The sit-to-stand ICC decreased from 0.632 to 0.596, and the combined single-leg stance ICC decreased from 0.136 to 0.119. The pooled ICC decreased from 0.982 to 0.942. These estimates characterize performance without the quality gate and do not replace the conditional primary analysis.

At the stricter target-frame threshold of ≥0.5, availability was 158 of 210 (75.2%) observations; task-specific ICCs were 0.770 (n=70) for squat, 0.670 (n=50) for sit-to-stand, and 0.204 (n=38) for combined single-leg stance (Table S15 in Multimedia Appendix 1). This sensitivity analysis describes the availability-agreement tradeoff and does not establish an optimal threshold.

Across all 342 videos, the descriptive quality-grade distribution was Grade A, 164/342 (48%); Grade B, 21/342 (6.1%); Grade C, 31/342 (9.1%); and Grade D, 126/342 (36.8%; Table S4 in Multimedia Appendix 1). These video-level quality assurance labels did not determine target-frame inclusion, weighting, or statistical inference and are not measures of target-frame detection success.

Detailed detection quality, retest, subject mean, and sensitivity results are provided in Multimedia Appendix 1.

Agreement of single-camera BlazePose knee-flexion estimates with the study references depended on task, flexion angle, and detection quality. With measurement availability of 177 of 210 observations (84.3%), task-specific conditional ICC point estimates ranged from good for squat to poor for single-leg stance. The primary cross-sectional CIs now account for repeated observations through participant-cluster resampling, and LoA incorporated within- and between-participant variance. These changes did not remove the uncertainty from only 12 to 15 contributing participants per dynamic task. Static differences changed direction across target angles and included target-setting and holding uncertainty. Kinovea interrater agreement did not establish 3D accuracy, and 4-participant repeated-session findings remained exploratory.

High Kinovea interrater agreement indicates that 2 raters produced similar 2D annotations and reduced 1 source of uncertainty in the BlazePose comparison. It did not establish Kinovea’s accuracy against 3D kinematics or show that every between-method difference originates from BlazePose. Both methods used a single sagittal view and may have shared projection, landmark, and out-of-plane error.

Task-specific estimates are more informative than the pooled cross-task ICC because pooling squat, sit-to-stand, and near-extension single-leg stance greatly expanded the angle range. Squat and sit-to-stand showed strong relative association but only good-to-moderate absolute agreement, illustrating why correlation cannot substitute for agreement metrics. In the clinical-flexion space, BlazePose overestimated flexion by approximately 6° for these tasks, and every task-specific LoA interval extended beyond at least one of the descriptive ±10° anchors. If reproduced clinically, this error direction could make recovery appear greater than it is; the healthy sample cannot quantify that clinical consequence.

The conditional analysis also described performance only when target-frame confidence was adequate. Retaining all numeric outputs produced marked deterioration for squat, and failure rates varied by task, participant, and acquisition group. The unresolved confidence decrease after S01-S06 shows that a constant camera model and file format did not guarantee consistent detection. Any future deployment would therefore require explicit measurement availability reporting and a per-recording quality gate rather than relying only on accuracy among successful detections.

Static signed error changed from flexion overestimation at 30° and 60° to underestimation at 90° and 120°. The angle-specific signed bias exceeded the descriptive ±5° anchor at 30°, 60°, and 120°, and every angle-specific LoA interval extended beyond at least one of the descriptive ±10° anchors. Together with the overall RMSE, this direction reversal and dispersion did not support a single calibration offset across the tested range. The result was agreement with goniometer-set targets in healthy participants not evidence that BlazePose can replace clinical goniometry. The goniometer was reapplied and reread before every trial but removed for recording and not reapplied afterward. Consequently, target-setting error, rounding, drift during the hold, and goniometer error cannot be separated from BlazePose error; the manufacturer-stated accuracy is not an in-study calibration estimate.

Plausible contributors included mismatch between image-based and palpated anatomical landmarks, perspective shortening, out-of-plane limb rotation, occlusion or crossing limbs, side-selection errors, and amplification of small landmark displacements when segments approach collinearity. These mechanisms are consistent with the observed angle and task dependence but were not isolated experimentally and should not be stated as proven causes.

Single-leg stance had poor concurrent agreement. Because the supporting knee occupied a narrow range near full extension, between-participant variance was small, and ICC was especially sensitive to modest measurement error. Occlusion by the nonstance limb, out-of-plane rotation, perspective, and landmark localization may add error in a single lateral view. Exploratory repeated-session findings from 4 participants did not resolve whether this uncertainty was task-related, method-related, or sample-related and did not establish that instability is intrinsic to the task.

The repeated-session analyses were based on 4 participants assessed 21 days to 29 days apart and cannot support definitive reliability or bias stability claims. The n=24 dynamic analysis was an ungated, automated, video-minimum stress test not a time-matched measure, and 10 of the 24 pairs included at least one low-confidence raw peak. The ICC for the between-method difference was imprecise and is best interpreted as insufficient evidence for a stable fixed offset not proof of universal bias drift. The 21‐to-29-day interval also permits real within-person change to contribute to disagreement, so measurement error and biological variation cannot be separated here.

The cross-sectional sample was small (n=15) and recruited by convenience from healthy young adults at one university, and no a priori power calculation was performed. The repeated-session subsample contained 4 participants, producing imprecise estimates from repeated observations nested within individuals. Findings cannot be generalized to older adults, knee osteoarthritis, anterior cruciate ligament reconstruction, total knee arthroplasty, or other clinical populations. One readily available iPhone 17 Pro was used throughout to hold hardware constant; equivalence across phones, lenses, frame rates, and device-specific image processing was not tested.

The static comparator was a rounded goniometer-set target rather than an independent measurement of the recorded posture, and the dynamic comparator was Kinovea 2D annotation rather than marker-based 3D kinematics, so absolute biomechanical accuracy remains unknown. We reprocessed 5 static videos at a lower pose-detection threshold, which was a protocol deviation; sensitivity analyses excluding them changed the estimates only slightly. The 33 failures from the 210 dynamic detection observations were unevenly distributed, making the retained-observation agreement estimates conditional on adequate detection. Target-frame confidence decreased after S01-S06 and did not recover in S11-S15; because acquisition conditions were incompletely recorded, the cause could not be identified. Participant-cluster CIs and repeated-measures LoA addressed clustering in the primary cross-sectional analyses, but with only 12 to 15 contributing participants per dynamic task, all interval procedures remained approximate; bootstrap intervals may have had inadequate coverage. The LoA variance model assumes approximately normal differences, common within-participant variance within a stratum, and conditionally independent residual differences. Consecutive repetitions may violate the last assumption. Resampling whole participants preserves the observed dependence but does not validate those distributional assumptions or guarantee future coverage. Across-angle and cross-task pooled LoA are descriptive only. The target-frame cutoff was established during analysis without a documented calibration basis, and sensitivity analyses did not make it a validated deployment threshold. Four-participant repeated-session intervals remained unadjusted and descriptive. Detailed angle-, side-, participant-, and sensitivity-level estimates are exploratory and were not adjusted as multiple confirmatory tests. The study assessed 1 BlazePose model, sagittal-plane angles, and selected task frames only; frontal/transverse motion and temporal variables were not evaluated.

This evidence supports only feasibility or screening-level research use under controlled acquisition with explicit quality checks. It does not support replacing a clinical goniometer, making precise longitudinal treatment decisions, assuming that a fixed calibration is stable, or using the method as an unconditional remote clinical measurement. Because BlazePose overestimated clinical flexion in squat and sit-to-stand, an unverified reading could overstate apparent recovery or mask a residual deficit; measurements that would affect care should be confirmed with an established clinical assessment.

Priorities for future work are larger, prospectively sized, and multisite cohorts; validation against 3D motion capture; testing in relevant clinical populations; direct cross-device evaluation; and controlled experiments that vary camera geometry, lighting, attire, occlusion, and out-of-plane motion. Repeated-session studies should prespecify the estimand, retain participant-level sampling in the analysis, and report both measurement availability and agreement conditional on successful detection.

Single-camera MediaPipe BlazePose had dynamic measurement availability of 177 of 210 (84.3%) observations: This included 71 of 75 (95%) observations for squat, 58 of 75 (77%) observations for sit-to-stand, and 48 of 60 (80%) observations for single-leg stance. Among the retained observations, the corresponding ICCs for squat, sit-to-stand, and single-leg stance were 0.773, 0.632, and 0.136, respectively with participant-cluster intervals showing substantial uncertainty. Static agreement with goniometer-set targets varied by angle and included uncertainty in the reference positioning. Four-participant repeated-session findings did not establish stable calibration or reliable longitudinal change measurement. These data support further controlled feasibility and screening-level evaluation with per-recording quality checks not replacement of clinical measurement or routine remote clinical decision-making.