This was a retrospective cohort study. We collected data on consecutive adult patients (aged 18 years and older) with laboratory-confirmed COVID-19 [29], admitted in one of 41 participating hospitals in Brazil from March 2020 to August 2022. Details of the cohort have been published elsewhere [30]. Pregnant women; patients undergoing palliative treatment, or with a history of prior KRT or already in KRT upon hospital presentation; and those who were transferred from or to another hospital were excluded from this particular analysis (Figure 1).

Two predictive models were developed and validated: 1 for KRT and 1 for in-hospital mortality. Both models presented imbalanced class distributions, but in different proportions, and were used as case studies. These outcomes were selected due to their clinical relevance and prognostic implications in hospitalized patients with COVID-19 [31].

Sociodemographic, clinical, and laboratory data; medications; interventions; and outcomes were extracted from medical records by trained researchers using the REDCap (Research Electronic Data Capture) electronic platform [32,33], hosted at the Telehealth Center of the University Hospital of the Universidade Federal de Minas Gerais [34,35]. An automated data verification algorithm was implemented to ensure data quality, checking for inconsistencies. Any discrepancies were resolved in consultation with the coordinating researchers.

Candidate predictors were selected based on clinical relevance, prior literature, and data availability (Multimedia Appendices 1 and 2). No automated feature selection was applied, as the study objective was not to maximize predictive performance but to assess how different evaluation metrics behave under identical modeling conditions. The same predictor set was maintained across all experiments to ensure comparability between models and evaluation strategies. KRT was defined as the initiation of dialysis during hospitalization, excluding patients with preexisting chronic dialysis. In-hospital mortality refers to death occurring during hospitalization, as documented in medical records. Patients were classified into binary outcome groups for each end point (KRT vs no KRT; death vs survival).

Extreme gradient boosting (XGBoost) was chosen due to its strong performance in structured clinical data, ability to capture nonlinear relationships, native handling of missing values, and favorable calibration properties reported in prior studies [36-38]. Since XGBoost supports missing values natively, no imputation method was used in the primary analysis.

A 10-fold stratified cross-validation strategy was used. In each iteration, 1-fold was held out as the test set, while the remaining 9-folds constituted the training set. Within this training partition, a further split was performed to create a validation subset used exclusively for hyperparameter tuning and model selection. All preprocessing and rebalancing procedures that did not require imputation, which are detailed in the next subsection, were performed strictly within the training data of each fold. The test set remained fully held out and was used only for final performance evaluation, preserving the original data distribution and preventing data leakage.

Three key hyperparameters were systematically explored: (1) booster (gbtree, gblinear, and dart), which defines the base learner used to build the ensemble; (2) eta (learning rate), which controls the step-size shrinkage during boosting to prevent overfitting by making the learning process more conservative; and (3) max_depth, which controls the maximum depth of individual trees, thereby regulating model complexity. The complete grid of values evaluated for each hyperparameter is reported in Multimedia Appendix 3.

After selecting the optimal hyperparameter configuration, the model was retrained on the full training data (training + validation) following standard practice and prior work [39,40], as well as the default behavior of widely used libraries such as scikit-learn (GridSearchCV with refit=True). The held-out test fold was then used exclusively for final performance evaluation. This process was repeated across all folds, so that each fold served once as the test set, and the reported results correspond to the average performance across the 10 iterations. This strategy ensures robust performance estimation and minimizes data leakage [41,42]. The overview of the analytical pipeline is presented in Figure 2.

To assess the impact of data imbalance on model performance, both oversampling and undersampling techniques were applied exclusively on the training data. For each method, default resampling parameters were used, without additional tuning, following the standard implementation of each algorithm. Due to the intrinsic operational characteristics of certain resampling methods, a fully balanced (1:1) class distribution was not always achieved. The final class proportions after resampling are presented in Multimedia Appendix 3.

Oversampling techniques included Random Oversampling [43], Adaptive Synthetic [44], Synthetic Minority Oversampling Technique (SMOTE) [45], BorderlineSMOTE [46], SVMSMOTE [47], and KMeansSMOTE [48], which increase minority-class representation through random duplication or synthetic sample generation [43,49]. Undersampling methods included Random Undersampling [44], Redundancy-Based Undersampling [39], e2sc-us (Effective, Efficient, and Scalable Confidence-Based-UnderSampling) [39], Condensed Nearest Neighbor [50], Near Miss 1 [51], and Near Miss 2 [51], which reduce majority-class instances while attempting to preserve relevant decision boundaries [39].

Because most resampling algorithms cannot handle missing values, the MissForest imputation method was incorporated into the pipeline when required, exclusively within the training data for rebalancing experiments [52]. Importantly, the imputation model was fitted exclusively on the training partition within each cross-validation fold and subsequently applied to the corresponding validation and test sets, thereby preventing information leakage.

For each resampling strategy, the entire modeling pipeline, including imputation (when applicable), resampling, and model training, was re-executed within each cross-validation iteration. Hyperparameter tuning was performed from scratch for each resampled dataset, ensuring that model optimization was specific to each data configuration. Details of the hyperparameter search space are provided in Multimedia Appendix 4. No information from the test set was used at any stage of model development, including imputation, resampling, or hyperparameter tuning.

To enable direct comparison across models, a fixed probability threshold of 0.5 was used for classification. This threshold was selected based on its consistent performance across preliminary analyses. All experiments were conducted using a fixed random seed (random_state=42), applied consistently across all stochastic components of the pipeline, including cross-validation splitting, imputation, resampling procedures, and model initialization, ensuring full reproducibility.

Model performance was assessed using a complementary set of metrics that offer different perspectives to evaluate model performance, capturing global discrimination, class-specific behavior, calibration, and clinical usefulness (Multimedia Appendices 5 and 6). All metrics were computed on the held-out test fold in each iteration and averaged across folds. Specifically, we analyzed global metrics, such as accuracy and AUROC, as well as metrics that are more sensitive to class imbalance, such as macro-F₁ and per-class precision and recall, including precision and recall across both majority and minority classes and the impact of different decision thresholds on the values of these metrics.

We first evaluated global performance using accuracy and AUROC. These metrics summarize overall discrimination across all instances but treat all elements equally, regardless of their class, which inherently biases these metrics toward the majority class in imbalanced datasets [2,4]. Accuracy represents the proportion of correctly classified instances [4], while AUROC quantifies the model’s ability to rank positive cases higher than negative ones across all decision thresholds [6,11]. However, what is considered a “correct” prediction depends on the chosen decision threshold for the risk score, as different thresholds influence the balance between sensitivity and specificity [4].

To explicitly capture performance under class imbalance, we additionally reported per-class precision, recall, and F₁-score, as well as macro-F₁, which assigns equal weight to each class regardless of prevalence [50,51,53]. To better characterize performance under class imbalance, we first examined class-specific precision and recall, which directly quantify errors for both minority and majority outcomes. Regarding the positive class, recall (sensitivity) reflects the proportion of true cases correctly identified, whereas precision (positive predictive value) reflects the proportion of predicted positives that are true events. The same logic applies to the negative class, where recall corresponds to specificity and precision to negative predictive value [54,55].

In addition to these class-specific metrics, we evaluated resampling strategies using TPRGap, a bias-oriented measure that quantifies performance disparity between classes as the absolute difference between their true-positive rates. This metric directly captures classifier favoritism toward the majority class, which may persist even when global performance measures remain high [56]. Finally, to summarize the trade-off between precision and recall in a single indicator, we reported the F₁-score and its macroaveraged form, which assigns equal weight to each class and is therefore robust to outcome imbalance [50,51,54,57].

While this perspective is common in the ML literature, it may be less intuitive for health care professionals, who are generally more familiar with metrics such as sensitivity and specificity. By reporting both precision and recall for each class, we provide a more nuanced and clinically interpretable understanding of model performance, especially relevant in the presence of class imbalance [50,51,54,57]. This approach enables assessment not only of how well the model identifies patients at risk but also how confidently it excludes those unlikely to experience the outcome. Therefore, it supports a more comprehensive assessment of predictive usefulness and more informed decision-making in clinical applications.

Primary analyses were conducted using a default probability threshold of 0.5, consistent with standard binary classification practice. To explore clinically relevant trade-offs between missed events and false alarms, we further evaluated precision-recall behavior across varying decision thresholds using precision-recall curves [50,56]. The precision-recall curve was generated by plotting precision against recall at various decision thresholds [54].

Model calibration was assessed using the plot with predicted probability against observed probability, testing intercept equals zero and slope equals 1. In a well-calibrated model, there is agreement between observed and predicted events, allowing the probability to be interpreted as the confidence in the prediction [58,59]. In addition, the global accuracy of the model was assessed using the Brier score. The Brier score ranges from 0 to 1, with lower values indicating better probabilistic accuracy [15].

Clinical usefulness was assessed through decision curve analysis, which quantifies net benefit across a range of decision thresholds compared with “treat-all” and “treat-none” strategies [55,57]. While decision curves assess whether model-guided decisions outperform simple strategies, they do not ensure balanced error distribution or detect bias toward the majority class, reinforcing the need for class-specific performance metrics [55,57]. Finally, the learning curves were used as a graphical representation of how a model’s performance evolves as training data are added [60].

This study adheres to the TRIPOD+AI (Transparent Reporting of a multivariable prediction model for Individual Prognosis Or Diagnosis + Artificial Intelligence) standards for transparent reporting (Multimedia Appendix 7) [6]. To ensure methodological rigor, we used the PROBAST+AI (Updated Quality, Risk of Bias, and Applicability Assessment Tool for Prediction Models Using Regression or Artificial Intelligence Methods) to assess risk of bias and applicability (Multimedia Appendix 8). The study was considered to have a low risk of bias in all domains (participants, predictors, outcomes, and analysis). However, the lack of external validation of the model should be considered as a point of attention in the domain of analysis. Applicability concerns were judged to be low across all domains [16].

The study was approved by the Brazilian National Research Ethics Committee—Comissão Nacional de Ética em Pesquisa (CAAE 30350820.5.0000.0008) and internal approval of ethics boards from each hospital. Individual informed consent term was waived due to the pandemic situation and analysis of deidentified data, based on chart review only.

The database included 17,018 patients (median age of 60 years, IQR 37‐83; 54.6% were men). The outcome distributions were highly imbalanced (Figure 3). Approximately 9.5% (1617/17,018) of the patients underwent KRT (1617 patients), resulting in an imbalance ratio of 9.5:1. Similarly, 18% (3063/17,018) of the patients died, corresponding to an imbalance ratio of 4.6:1.

The predictive XGBoost model demonstrated high overall performance when considering accuracy (0.910) and AUROC (0.928; Table 1). However, due to class imbalance, the other metrics revealed some important observations that would otherwise be overlooked. Notably, the macro-F₁-score of 0.695 suggests relatively lower performance, specifically for the minority class (KRT=yes; Tables 1 and 2). This is mainly due to the low recall (0.372), indicating that the model struggles to correctly identify a large proportion of actual KRT cases. The precision for this class was 0.539, resulting in an F₁-score of 0.439 (Table 2).

The confusion matrices for KRT prediction also highlight this trend, showing that lowering the threshold from 50% to 10% enhances sensitivity, evidenced by a 174.5% increase in true positive (from 51 to 140). However, this adjustment also leads to a 284.0% rise in false positive (from 50 to 192; Figure 4A).

Changing the cutoff threshold affected the model’s precision, recall, and F₁ values. In this context, considering the class of interest, which is KRT, and the default cutoff threshold of 50%, the precision was 0.539, recall was 0.372, and F₁-score was 0.439 (Table 2). Lowering the cutoff threshold to 20% resulted in a precision of 0.449, recall of 0.701, and an improved F₁-score of 0.547 (Table 2). The data presented in Multimedia Appendix 9 elucidate the trade-off between precision and recall, where an increase in precision usually implies a reduction in recall and vice versa.

The calibration plot shows systematic deviation from the diagonal, with predicted probabilities falling below the diagonal at higher values and above it at lower values, indicating overconfidence at the extremes (Figure 5A). This pattern is further supported by a calibration slope of 0.60 and an intercept of −0.14 (Figure 5B), indicating both overconfident predictions and a slight global overestimation of risk.

The precision-recall curve for each class (Figure 6A) showed that the non-KRT class achieved high precision and recall simultaneously, which is desirable, while the KRT class showed a performance closer to random. In other words, the model is relatively good at recalling non–KRT patients (high specificity), but it struggles to identify the ones who underwent KRT (low sensitivity).

It is observed that the curve for the class that did not undergo KRT remains close to the upper right corner, indicating that the model can achieve high precision and recall rates simultaneously. Conversely, the curve for the (interest) minority class (underwent KRT) approaches the diagonal, suggesting that the model is struggling to balance precision and recall, with performance close to random.

The decision curve analysis (Multimedia Appendix 10) indicates that the proposed model generates a positive net benefit for low to moderate decision thresholds, starting at approximately 0.10 and gradually decreasing to zero as the threshold increases to 0.5. Consequently, the model exhibits a practical benefit for decision thresholds (P≤.5), indicating usefulness in scenarios that tolerate decisions based on relatively moderate predicted probabilities. In contrast, the strategy of treating all cases shows a positive net benefit only at very low thresholds, reaching zero around a threshold of 0.10 and becoming increasingly negative thereafter.

The predictive XGBoost model achieved high values of accuracy (0.900) and AUROC (0.945; Table 3). However, due to class imbalance, the macro-F₁-score of 0.830 indicates lower performance (Table 3). Specifically, for the minority class (deceased=yes), the precision is 0.725, the recall is 0.718, and the F₁-score is 0.721 (Table 4).

The confusion matrices for mortality prediction demonstrated a similar precision-recall trade-off (Figure 4B). Reducing the cutoff threshold from 50% to 10% enhanced recall, with true positives increasing by approximately 29.1% (from 202 to 261), but also resulted in a 113% increase in false positives (from 88 to 188).

As with KRT, the cutoff threshold affected the precision, recall, and F₁-scores. At a 50% cutoff threshold, the precision is 0.725, the recall is 0.718, and the F₁-score is 0.721 (Table 4). Lowering the threshold to 20% increased the recall (0.880) and improved the F₁-score (0.748), while precision decreased to 0.651 (Table 4 and Multimedia Appendix 4). Similar to KRT, the calibration plot (slope=0.72; intercept=−0.16) was not satisfactory, and the Brier score was low (0.072; Figure 5C and D and Table 3).

The precision-recall curves for each class (Figure 6B) followed a similar pattern to that observed for KRT, with the non–death class exhibiting higher precision and recall than the death class. Once again, the model performed well in identifying survivors (high specificity) but demonstrated limited ability to detect patients who died (low sensitivity).

It is observed that the curve for the non–death class remains close to the upper right corner, indicating that the model can achieve high precision and recall rates simultaneously. In contrast, the curve for the death class, which is the minority class and of greater interest, approaches the diagonal (random model).

Similar to KRT, the decision curve for death shows that the net benefit of the strategy of treating all cases is approximately 0.2, while the proposed model achieves a substantially higher net benefit, around 0.8 (Multimedia Appendix 11). This behavior demonstrates that indiscriminate intervention quickly becomes inadequate as the decision threshold increases, while the proposed model maintains its practical usefulness over a substantially wider range of thresholds.

The model for KRT, which exhibited higher class imbalance, demonstrated superior performance for accuracy and AUROC when compared with the model for mortality. However, when examining the precision and recall for the minority class, the performance was suboptimal, and the KRT model exhibited lower performance than the mortality model. This pattern was also reflected in the macro-F₁-score, where the KRT model displayed a more significant drop in performance, further highlighting the impact of class imbalance.

It is important to highlight that KRT represents a distinct endpoint from mortality. Although both models used the same set of variables, the features and the importance of each feature vary depending on the endpoint (Multimedia Appendices 12 and 13). Therefore, discrepancies in the performance of the KRT and mortality models should not be solely attributed to differences in class balance.

The learning curves show a plateau-like shape, with stable validation performance across all training set sizes for both outcomes (Figures 7A and 7B). This pattern suggests limited change in performance as the training set size increases, indicating that model performance does not substantially improve with additional data.

When evaluating the impact of class rebalancing strategies, we observe a clear and systematic discrepancy between AUROC and metrics that explicitly account for class-specific behavior. As shown in Multimedia Appendices 12 and 13, AUROC remains consistently high across all experimental conditions, exceeding 0.8 in every scenario, regardless of whether rebalancing is applied or whether minority-class performance substantially improves or deteriorates. This stability may give the misleading impression that rebalancing strategies have limited effect on model behavior.

However, a closer inspection using alternative metrics reveals a markedly different picture. In particular, TPRGap provides a direct measure of classifier bias induced by class imbalance, capturing disparities in true-positive rates between classes. Using this metric, several rebalancing techniques substantially reduce bias relative to the unbalanced baseline. For instance, in the death outcome, TPRGap decreases from 0.230 in the unbalanced setting to 0.043 when using Redundancy-Based Undersampling, indicating a pronounced reduction in class-dependent performance disparity. In contrast, AUROC changes only marginally in the same scenario, from 0.945 to 0.941, failing to reflect this improvement.

Similar patterns are observed across other class-aware metrics, particularly positive-class precision, recall, and F₁-score. These metrics exhibit significant sensitivity to rebalancing strategies, capturing both beneficial and harmful effects on minority-class performance. In several cases, rebalancing leads to meaningful gains in recall at the expense of precision, or vice versa, reflecting trade-offs that are critical in clinical decision-making contexts. Yet, AUROC remains largely unchanged, masking these trade-offs and providing little insight into how the classifier’s behavior actually shifts.

An especially illustrative example arises in the death outcome under the Near Miss 2 undersampling strategy. In this case, the positive-class F₁-score drops sharply from 0.721 in the unbalanced model to 0.345, signaling a severe degradation in clinically relevant performance. Despite this substantial decline, AUROC remains comparatively high, decreasing from 0.945 to 0.809. This modest reduction does not adequately reflect the magnitude of the performance loss experienced by the minority class, underscoring the disconnect between AUROC and clinically meaningful outcomes.

In recent years, the rapid expansion of ML applications in health care has led to an increasing number of predictive models being proposed for clinical use. However, many of these studies continue to rely primarily, or even exclusively, on AUROC to report model performance, even in highly imbalanced clinical scenarios. Our findings demonstrate the limitations of this practice, showing that high AUROC values may coexist with poor performance for clinically critical minority outcomes.

Although methodological literature has long acknowledged the limitations of AUROC and accuracy in imbalanced settings, clinical prediction studies frequently continue to emphasize these global metrics. By applying complementary class-specific measures and analyzing the learning curves in a large cohort of over 17,000 hospitalized patients with COVID-19, our study provides practical evidence of how metric selection directly influences clinical interpretation, particularly when outcomes are imbalanced.

For both KRT and in-hospital mortality, AUROC values suggested excellent discrimination. However, class-specific metrics revealed substantial deficiencies in identifying minority outcomes. The KRT model achieved an AUROC of 0.928. However, recall for the KRT class was only 0.372, meaning that the model failed to identify nearly two-thirds of patients who would require dialysis. In a real clinical scenario, such as a hospital without dialysis services, this could result in missed opportunities for early referrals, with serious consequences for patient care. This discrepancy was captured by the macro-F₁-score (0.695), which penalizes imbalanced performance across classes and thus offers a more clinically realistic summary of the model’s performance than AUROC alone.

Calibration analysis further highlighted these limitations. Calibration slopes of 0.60 and 0.72, along with negative intercepts, indicate suboptimal calibration for both outcomes. Although Brier scores were low, this likely reflects strong discrimination combined with outcome imbalance, rather than well-calibrated probability estimates. These findings reinforce that no single metric adequately captures model performance in imbalanced clinical settings.

Precision-recall analysis further highlighted the limitations of AUROC-based evaluation by prioritizing performance on the minority class, which often represents the clinically most relevant outcome [57]. While decision curve analysis further illustrates that clinically meaningful usefulness may vary substantially across thresholds [61,62] and demonstrated net benefit across certain thresholds, it did not capture how prediction errors were distributed between classes. By examining class-specific precision and recall across varying thresholds, we directly linked model behavior to real-world clinical trade-offs between underdiagnosis and overdiagnosis. Given that class prevalence directly affects metrics such as precision and recall, particularly in imbalanced settings [11,61,63], relying on AUROC alone may obscure clinically relevant deficiencies in minority-class performance. These results underscore the importance of reporting complementary, class-aware metrics, as no single metric adequately captures model performance across different clinical contexts. Therefore, metric selection should be guided by the intended clinical application. In high-risk settings, maximizing recall may be preferable to avoid missing cases, even at the expense of increased false positives. In contrast, in resource-limited settings, higher precision may be prioritized to reduce unnecessary interventions. These trade-offs cannot be adequately captured by a single metric, reinforcing the need for a multidimensional evaluation approach.

Learning curve analysis provided an additional and complementary perspective on model performance. In general, learning curves may reflect either progressive improvement with increasing data or early convergence in relatively simple prediction tasks [60]. In our study, however, the combination of flat learning curves, persistently low minority-class performance, and stable AUROC values across increasing training set sizes suggests limited gains in performance as more data are added, highlighting that AUROC alone may not capture important aspects of model behavior in imbalanced settings.

This finding has relevant methodological considerations. Despite consistently high AUROC values (>0.92), the lack of substantial improvement in performance with increasing training data suggests that discrimination alone may not fully reflect how model performance evolves, particularly for identifying high-risk patients. In this context, AUROC may reflect stable ranking ability driven by dataset characteristics, such as class imbalance, rather than improvements in clinically relevant performance. Therefore, reliance on AUROC alone may lead to overestimation of model performance and potential underrecognition of high-risk patients.

Learning curves offer a complementary tool to assess how model performance changes as additional data are incorporated [60]. When performance remains relatively stable, caution is warranted in interpreting high discrimination metrics as sufficient evidence of model adequacy. Together, these findings reinforce that AUROC alone is insufficient to determine whether a model is suitable for clinical use, particularly in imbalanced scenarios.

International reporting frameworks such as PROBAST+AI and TRIPOD+AI emphasize comprehensive evaluation of predictive model performance and transparency in results presentation but remain focused on global performance measures of discrimination, calibration, and overall clinical usefulness [6,16]. Although these frameworks acknowledge the impacts of class imbalance on outcomes, they do not offer strategies for measuring the redistribution of errors across classes with varying thresholds, nor do they recommend incorporating learning curve analysis into model evaluation [6,16].

Additionally, according to PROBAST+AI, applicability concerns were considered low, as the study population, predictors, and outcomes are consistent with real-world clinical settings. However, this should not be interpreted as evidence supporting clinical use of the models. Despite this apparent applicability, the models demonstrated important limitations in clinically relevant performance, including suboptimal calibration and limited sensitivity for the minority class. This apparent contradiction highlights a key finding of our study: even when models are developed using appropriate data and aligned with clinical contexts, reliance on conventional metrics such as AUROC may obscure critical weaknesses. Therefore, methodological soundness and contextual relevance alone are insufficient to ensure clinically meaningful performance, reinforcing the need for comprehensive, class-aware evaluation frameworks before considering any potential clinical implementation.

Our findings provide a methodological contribution that extends beyond these current standards. Specifically, we demonstrate that high AUROC values were maintained despite limited changes in performance across increasing training set sizes. This observation suggests that AUROC alone may not reflect whether a model has learned clinically meaningful patterns but rather may capture stable discrimination driven by dataset characteristics such as class imbalance, highlighting the need for more transparent and comprehensive reporting.

This has important implications: models may comply with current reporting standards while still underperforming in clinically relevant minority outcomes, which are often the most clinically relevant. Because learning curves are rarely reported, this limitation may go unrecognized in many published models. Incorporating learning curve analysis alongside class-specific metrics can therefore enhance transparency and provide a more robust assessment of model performance.

Resampling techniques, including over- and undersampling, resulted in only modest improvements in minority-class performance and did not resolve the fundamental limitations of AUROC-based evaluation [28,62,64,65]. Even when class distributions were artificially modified, AUROC remained largely insensitive to clinically meaningful changes in recall and precision. This reinforces that rebalancing alone cannot compensate for inappropriate performance metrics.

Our study contributes to literature by bridging theoretical concerns with practical, real-world application. By evaluating 2 predictive models in a large clinical cohort with varying degrees of outcome imbalance, we demonstrate how metric selection and threshold choice directly influence clinical interpretation and link how these shifts directly affect clinical decision-making. By evaluating per-class precision and recall across multiple cutoffs and visualizing these relationships through precision-recall curves, we make explicit the trade-offs inherent to real-world model deployment.

These trade-offs are particularly relevant in health care, where underdiagnosing high-risk patients (low recall) may lead to missed interventions, while overdiagnosis (low precision) can result in unnecessary procedures and resource strain [66]. In high-stakes settings, such as intensive care units or emergency triage, prioritizing recall may be appropriate, even at the cost of more false positives, to avoid missing patients at risk of deterioration. On the other hand, in resource-constrained environments, higher precision may be preferable. Together, these findings reinforce that no single metric is sufficient and that different clinical contexts require different operating points and different emphases on recall, precision, or their balance, which is effectively summarized by the macro-F₁.

Despite growing methodological awareness [4,6-9,50,64], most applied health care research still relies predominantly on this AUROC for model evaluation (Multimedia Appendices 14 and 15) [67]. For example, DynaMed, a widely used evidence-based clinical reference platform, currently lists 26 predictive models specifically developed for COVID-19—1 diagnostic and 25 prognostics, including outcomes such as severe disease progression, thrombosis, intensive care unit admission, KRT, and mortality (Multimedia Appendix 11) [67]. Notably, 88.5% (23/26) of these models primarily report AUROC as the main performance metric [67].

Additionally, some studies report multiple metrics without adequately contextualizing their relevance or the trade-offs involved [67-69]. Our findings highlight the importance of not only reporting multiple metrics but also interpreting them in relation to clinical context and outcome imbalance.

Therefore, metric selection and learning curve analysis may substantially influence the clinical interpretation of model performance. Choosing evaluation strategies that account for outcome imbalance and clinical priorities is essential to support more rigorous evaluation before potential clinical implementation of predictive models.

The methodology focused on a single algorithm (XGBoost), although the observed patterns are not model-specific and reflect broader issues related to class imbalance and performance evaluation. External validation was not feasible due to data availability; however, this does not affect the central methodological contribution of the study, which concerns the interpretation of model performance rather than the generalizability of a specific model. Therefore, our findings should not be interpreted as supporting the clinical use of the models presented, given the lack of external validation and suboptimal calibration. Importantly, the aim of this study was not to develop the best-performing predictive model but to examine how evaluation strategies influence the interpretation of model performance in imbalanced clinical scenarios.

In prediction tasks with imbalanced outcomes, which are common in health care, reliance on accuracy and AUROC alone may obscure clinically important failures. Complementary metrics, including precision, recall, and macro-F₁, provide a more realistic assessment of model performance and should be systematically reported. In addition, learning curve analysis offers insight into a model’s learning dynamics and helps explore how model performance evolves as more training data are incorporated. Together, these approaches support a more comprehensive and clinically meaningful evaluation of predictive models, particularly in imbalanced settings, rather than their direct translation into clinical practice.