The literature on antidepressant safety in BD divides sharply between those who emphasise the undertreatment of bipolar depression and those who prioritise iatrogenic mood destabilisation risk. Gijsman et al. [4] demonstrated short-term antidepressant efficacy in BD depression but with significantly elevated switch rates in unprotected patients. Sidor and Macqueen’s meta-analysis found that antidepressant class strongly moderates switch risk: TCAs carry the highest rate (approximately 48%), followed by SNRIs (32%), SSRIs (28%), and bupropion (18%). Mood stabiliser co-prescription reduces switch risk substantially but does not eliminate it, with lithium providing the most robust protection. The CANMAT and ISBD Task Force guidelines recommend antidepressant use only as adjunctive therapy in BD-II with adequate mood stabiliser coverage, and actively discourage antidepressant use in BD-I, rapid cyclers, and those with prior AICA history. Despite these recommendations, real-world prescribing data show that antidepressants are prescribed to 40% - 60% of BD patients across healthcare systems, often without adequate mood stabiliser cover [11].

ML approaches to psychiatric treatment safety have grown substantially in the prediction of antipsychotic side effects, antidepressant response, and lithium-related adverse events [12]. For BD specifically, Tondo et al. [13] developed a clinical scoring instrument for switch risk that included BD-I diagnosis, prior switch history, and absence of mood stabiliser, achieving moderate discrimination (AUC ≈ 0.71). No study has extended beyond clinical scoring to integrate circadian digital biomarker features, model the pharmacological trajectory as a structured feature set, or applied ensemble methods with decision-theoretic evaluation. The gap between clinical scoring instruments and ML-calibrated risk models with formal uncertainty quantification and clinical utility assessment remains wide [14].

Circadian rhythm disruption is both a core feature of BD and a specific vulnerability marker for pharmacological mood destabilisation. The IS score (interdaily stability), derived from 10-minute epoch accelerometry, measures the consistency of the 24-hour rest-activity pattern across days: lower IS scores indicate greater circadian fragmentation. IV score (intraday variability) measures within-day rhythm fragmentation. In BD, lower IS scores have been associated with more episodes, greater illness severity, and poorer treatment response [15]. HRV time-domain parameters (SDNN, RMSSD) reflect autonomic nervous system tone and have been shown to differ between depressive, euthymic, and manic states in BD patients. The integration of these continuously measured circadian markers with pharmacological history into a unified AICA prediction framework has not previously been attempted.

Random Forest, [16] XGBoost, [17] and LightGBM [18] represent the dominant gradient boosting and ensemble architectures for tabular clinical data. Out-of-fold stacking with a logistic regression meta-learner has been shown to produce superior calibration and discrimination compared to any single base learner across multiple clinical prediction benchmarks [19], by combining the diverse inductive biases of tree-ensemble and boosting architectures while protecting against target leakage through the OOF training protocol. SHAP (SHapley Additive exPlanations) [20] provides the most theoretically grounded decomposition of ensemble predictions into per-feature additive contributions, preserving consistency and local accuracy properties absent in surrogate explanation methods.

This study used an entirely synthetic cohort of N = 850 independent simulated patients with bipolar disorder (BD-I: 58%; BD-II: 42%) and a simulated AICA prevalence of 29.1%. No patient-level observations were extracted from STEP-BD, CANMAT, the Istituto di Psicopatologia, hospitals, registries, or electronic health records. Published studies and guidelines were used only to define clinically plausible variable ranges, relative prevalence targets, and directional associations. The pharmacological domain comprised categorical treatment variables and bounded dose or exposure variables; episode chronology comprised count, rate, proportion, and duration variables; and circadian biomarkers comprised bounded continuous measures. The primary simulation imposed complete feature availability, while random measurement noise was added to generated continuous variables and 3% of outcome labels were inverted as diagnostic noise. Because the cohort was simulated, the 29.1% prevalence is a design target rather than an empirical estimate. External validation on independently collected data remains necessary.

To make the revised simulation fully reproducible, the narrative design was operationalised as a fixed reconstructed generator (Supplementary Table S1). Three standardised latent factors pharmacological vulnerability (P), illness severity (S), and circadian disruption (C) were sampled from a zero-mean multivariate normal distribution with correlation matrix Σ = [[1.00, 0.25, 0.20], [0.25, 1.00, 0.35], [0.20, 0.35, 1.00]]. Binary variables were sampled from Bernoulli distributions with logistic probabilities, count variables from bounded Poisson distributions, and continuous variables from truncated normal, beta, gamma, or log-normal distributions. Antidepressant-class probabilities were TCA 0.12, SSRI 0.48, SNRI 0.22, NDRI 0.15, and MAOI 0.03 before latent-factor adjustment. Core circadian assumptions were IS = N (0.62 − 0.10C − 0.04S, 0.10²), IV = N (0.72 + 0.12C + 0.04S, 0.14²), and relative amplitude = N (0.78 − 0.08C − 0.03S, 0.10²), each truncated to its stated range. Published evidence informed only plausible ranges, class ordering, and directional associations [3][4][8]-[10][15]; no patient-level values were copied. The feature-generation seed was 1,115,670. The primary complete-data experiment introduced no feature-level missingness; stochastic residual variation was included in every continuous draw, values were clipped to prespecified clinical ranges, and the outcome-noise mechanism was handled separately in Section 3.3. These values are simulation design constants, not estimates of real-patient distributions.

Pharmacological history (24 features) encoded antidepressant class (TCA, SSRI, SNRI, NDRI, MAOI), a pharmacological risk index, standardised dose, treatment duration, index-episode polarity at initiation, number of prior antidepressant trials, abrupt versus gradual titration, mood stabiliser class and adequacy, mood stabiliser duration, cytochrome P450 metaboliser status (CYP2D6 and CYP2C19 poor metabolisers), and family history of BD and rapid cycling. The pharmacological risk index was an ordinal class-risk score scaled to [0, 1], with lower values assigned to lower-risk classes and higher values assigned to classes assumed to carry greater switch or cycle-acceleration risk, following the risk ordering described in the clinical literature. Mood stabiliser adequacy was operationalised as a binary indicator of guideline-concordant therapeutic coverage at antidepressant initiation, incorporating the simulated agent, therapeutic dose or serum-level status, treatment duration, and adherence; 1 represented adequate coverage and 0 represented absent or subtherapeutic coverage. Episode chronology (18 features) included depressive, manic, hypomanic, and mixed episode counts, total episode rate per year of illness, mixed-episode fraction, prior rapid-cycling status, prior AICA, mean episode duration, and mean inter-episode interval. Circadian digital biomarkers (16 features) comprised IS score, IV score, relative amplitude, sleep-onset variability, mean sleep duration and quality, napping frequency, HRV SDNN and RMSSD, LF/HF ratio, daily step count and its coefficient of variation, smartphone app-use entropy, communication frequency, a circadian alignment index, and a pre-antidepressant mood slope from 30-day ecological momentary assessment. The circadian alignment index was defined as a normalised composite in which higher IS and relative amplitude and lower IV and sleep-onset variability indicated better alignment; higher values therefore represented a more stable rest-activity rhythm.

AICA was operationally defined as a simulated switch to mania or hypomania, induction of rapid cycling (four or more episodes in twelve months), or emergence of a mixed state within sixteen weeks after antidepressant initiation, not attributed by the simulator to spontaneous illness progression. The label-generating function included prespecified main effects for prior AICA history, antidepressant-class pharmacological risk, inadequate mood stabiliser coverage, mixed-episode fraction, prior rapid cycling, low circadian IS, BD-I diagnosis, abrupt antidepressant titration, CYP450 poor-metaboliser status, and family history of rapid cycling. Prespecified nonlinear interactions represented risk amplification between prior AICA and high-risk antidepressant class, between antidepressant-class risk and inadequate mood stabiliser coverage, and between mixed-episode history and circadian fragmentation. These coefficients and interactions were fixed before model fitting and were not estimated from the training or test data. The intercept was calibrated to obtain the target prevalence, after which 3% of labels were inverted to represent diagnostic noise. Because the outcome was generated from variables later supplied to the models, performance measures the ability to recover the simulator’s rule structure rather than clinical prediction in an independent population.

The reconstructed label generator used the exact scaling and coefficients reported in Supplementary Table S2. Let risk denote the antidepressant-class risk index; inadequateMS = 1 − mood-stabiliser adequacy; mixedScaled = min(max(mixed-episode fraction/0.50, 0), 1); lowIS = min(max((0.65 − IS)/0.35, 0), 1); and CYPpoor = 1 when either CYP2D6 or CYP2C19 poor-metaboliser status was present. The baseline linear predictor was η = −14.890 + 7.20 (prior AICA) + 4.80 (risk) + 4.50 (inadequateMS) + 3.75 (mixedScaled) + 3.15 (prior rapid cycling) + 4.65 (lowIS) + 1.65 (BD-I) + 1.35 (abrupt titration) + 1.20 (CYPpoor) + 1.05 (family rapid-cycling history) + 5.70 (prior AICA × risk) + 4.50 (risk × inadequateMS) + 4.20 (mixedScaled × lowIS), plus four prespecified threshold bonuses detailed in Table S2. Event probability was p = 1/(1 + exp(−η)); labels were sampled as Bernoulli (p). Using the fixed Bernoulli and inversion random-number streams, the intercept was calibrated before model fitting so that the final post-inversion dataset contained 247 AICA labels among 850 simulated cases (29.1%); 26 labels were inverted using label seed 20261113 to represent diagnostic uncertainty. No coefficient was estimated from the model-training or test data.

Label-generation robustness was specified by repeating the complete simulation and modelling workflow under three alternative assumptions: 1) all main-effect and interaction coefficients reduced by 20%; 2) all coefficients increased by 20%; and 3) interaction terms removed while retaining the main effects. An additional noise analysis compared label-inversion rates of 0%, 3%, and 6%. The prespecified robustness criterion was preservation of the ordering of test-set AUCs and the qualitative ranking of the five leading SHAP predictors.

All sensitivity reruns used the same 850-row feature matrix, the fixed training/validation/test indices generated with seeds 1701 and 1702, the same preprocessing and model hyperparameters, and the same label random-number stream. For each alternative coefficient or noise scenario, only the specified generator assumption was changed and the intercept was recalibrated to retain 247 events overall. AUC intervals were estimated with 1000 bootstrap resamples of the fixed test set. The full numerical results are reported in Supplementary Table S3.

The full workflow was defined before test evaluation. First, the synthetic cohort was divided once using a stratified 70/15/15 allocation into training, validation, and held-out test sets. All preprocessing, resampling, model fitting, and stacking were confined to the training data. The reported model hyperparameters were fixed a priori from the analysis specification and were not selected using the test set. Within the training set, a five-fold out-of-fold stacking protocol generated meta-features from three Level 1 learners: Random Forest (300 trees, minimum samples per leaf = 2, square-root feature subsampling), XGBoost (400 boosting rounds, learning rate 0.04, maximum depth 5, subsample 0.8), and LightGBM (400 rounds with matching learning-rate and subsampling settings and early stopping). SMOTE was applied only to the training partition inside each fold and never to the fold-specific holdout, validation set, or test set. A logistic-regression meta-learner (C = 1.0) was fitted to the out-of-fold prediction matrix. After the stacking procedure was fixed, the base learners were refitted on the full training set. The validation set was used for early-stopping decisions where applicable and to select the F1-maximising classification threshold of 0.30. The untouched test set was evaluated once after all modelling and threshold choices had been finalised, preventing test-set information from influencing training, resampling, hyperparameters, or threshold selection.

Five baseline models were evaluated using the same prespecified split: Logistic Regression (L2, C = 0.1), SVM with RBF kernel (C = 1.0), Random Forest (300 trees), XGBoost (400 rounds, learning rate 0.04), and LightGBM (400 rounds). The baseline hyperparameters were fixed before test evaluation. SMOTE, where used, was restricted to training partitions, and the validation and test observations were never synthetically oversampled.

Discrimination was assessed using AUC, F1, sensitivity, specificity, and precision, with 95% bootstrap confidence intervals based on 1000 resamples. Calibration was assessed using the Brier score and reliability diagrams. Clinical-utility hypotheses were explored through decision-curve analysis over threshold probabilities 0.05 - 0.70, but net-benefit findings were interpreted only as internal synthetic results. BIC, WAIC, and Bayes-factor summaries were retained as exploratory model-fit and parsimony analyses and were not treated as substitutes for held-out discrimination. SHAP TreeExplainer was applied to the three tree-based learners, and their absolute SHAP matrices were averaged for global attribution. Pairwise AUC comparisons used DeLong’s method [21]. For subgroup analyses, the number of AICA events was reported for each subgroup. Approximate 95% AUC intervals were calculated analytically from subgroup event and non-event counts, and sensitivity intervals used the Wilson binomial method; these intervals were interpreted cautiously because several subgroups were small and overlapping.

Figure 1Figure 1 presents reliability diagrams for all six models. XGBoost achieved the lowest Brier score (0.077), followed closely by the proposed ensemble (0.079), LightGBM (0.083), logistic regression (0.093), SVM (0.097), and Random Forest (0.117). Therefore, the results do not support the original claim that the ensemble had the lowest Brier score. Figure 2Figure 2 presents decision-curve analysis. Within the reported threshold range of 0.20 - 0.60, the ensemble showed the highest estimated net benefit in this synthetic test set. This finding is hypothesis-generating and does not establish clinical utility or justify antidepressant-prescribing decisions without external validation.

Table 1 presents comparative performance on the held-out synthetic test set (n = 128). The ensemble achieved AUC = 0.939 (95% bootstrap CI: 0.889 - 0.976), F1 = 0.850 (95% CI: 0.754 - 0.929), sensitivity = 0.839 (95% CI: 0.704 - 0.949), and specificity = 0.946 (95% CI: 0.894 - 0.989). XGBoost achieved a nearly identical AUC of 0.937 and the lowest Brier score. Random Forest achieved the highest specificity (0.967) but lower sensitivity (0.650). The ensemble’s numerical advantage in AUC over XGBoost was small and should not be interpreted as evidence of clinically meaningful superiority. The results instead show that all models recovered strong signal embedded in the synthetic label-generating process.

Figure 1. Calibration curves (reliability diagrams) for all six models. Brier scores: XGBoost 0.077 (lowest), Proposed Ensemble 0.079, LightGBM 0.083, LR 0.093, SVM 0.097, and RF 0.117. Perfect calibration is shown by the dashed diagonal. XGBoost and the ensemble show the closest tracking in the middle probability range of this synthetic test set.

Figure 2. Decision-curve analysis in the synthetic test set. The proposed ensemble shows the highest estimated net benefit across threshold probabilities 0.20 - 0.60. This internal result does not demonstrate real-world clinical utility and requires prospective external validation.

Table 1. Comparative model performance-test set (n = 128).

95% bootstrap CI (1000 resamples) for proposed ensemble: AUC [0.889 - 0.976], F1 [0.754 - 0.929], sensitivity [0.704 - 0.949], specificity [0.894 - 0.989]. Threshold = 0.30 (F1-optimised on validation set). Brier: lower = better calibration.

The reconstructed sensitivity analysis approximately reproduced the high discrimination of the primary synthetic experiment but showed that exact model ordering was not invariant. With all coefficients reduced by 20%, the ensemble remained highest (AUC 0.948, 95% CI 0.890 - 0.988), followed by XGBoost (0.944) and Random Forest (0.939). With coefficients increased by 20%, logistic regression ranked first at 0.940 and the ensemble remained within 0.003 at 0.937; all leading confidence intervals overlapped. Removing all interactions materially changed the result: logistic regression retained AUC 0.928, whereas the tree models and ensemble fell to 0.873 - 0.882, showing that their advantage depended on nonlinear structure embedded in the label rule. With 0% label inversion, the ensemble and boosting models reached AUC 0.972 - 0.975; the reconstructed 3% scenario produced ensemble AUC 0.947; and 6% label inversion reduced all models to 0.843 - 0.874, with the ensemble still numerically highest at 0.874. Therefore, the broad conclusion that several model families recover the synthetic rule was robust to moderate coefficient perturbation, but the prespecified exact-ranking criterion was only partially met, and performance was sensitive to interaction removal and higher diagnostic noise.

Figure 3Figure 3 presents the SHAP beeswarm for the top 20 predictors. The five highest-ranked variables were prior AICA history, IS score, mood stabiliser adequacy, antidepressant-class risk, and mixed-episode fraction. In the synthetic cohort, these rankings are expected to reflect both the prespecified label-generating coefficients and correlations among the simulated predictors. They should therefore be interpreted as recovery of the simulator’s structure rather than independent confirmation of clinical mechanisms. Figure 4Figure 4 further illustrates the fitted dependence patterns for the three leading predictors.

Figure 3. SHAP beeswarm plot-top 20 predictors. Each point represents one test patient. Colour encodes normalised feature value (red = high, blue = low). Horizontal position encodes SHAP contribution magnitude and direction. Prior AICA history, circadian IS score, mood stabiliser adequacy, antidepressant class risk, and mixed episode fraction are the five dominant predictors.

Figure 4. SHAP dependence plots for the three dominant predictors in the synthetic test set. Left: prior AICA history. Centre: IS score, with lower values associated with higher model contributions. Right: mood stabiliser adequacy, with adequate simulated coverage associated with lower model contributions. Curves are second-degree polynomial fits and are descriptive rather than causal or clinically validated.

Figure 5Figure 5 presents ROC curves with 95% bootstrap confidence bands. All six models achieved AUC > 0.92 in the synthetic test set. The ensemble and XGBoost had overlapping curves and nearly identical AUCs (0.939 versus 0.937), indicating that the numerical difference was small. Random Forest achieved the highest specificity at the selected operating point but substantially lower sensitivity. These findings demonstrate strong recoverability of the simulated outcome rule but do not establish transportability to clinical data.

Figure 5. ROC curves with 95% bootstrap confidence bands (400 resamples) in the synthetic test set. All six models achieved AUC > 0.92. The Proposed Ensemble achieved AUC 0.939 (95% CI: 0.889 - 0.976), closely followed by XGBoost at 0.937. The overlapping curves indicate similar discrimination under the simulation assumptions.

Figure 6Figure 6 presents the confusion matrix for the ensemble at the validation-selected threshold of 0.30. Among 128 synthetic test cases, 31 of 37 AICA cases and 86 of 91 non-AICA cases were classified correctly, corresponding to sensitivity 0.839 and specificity 0.946. The six false negatives and five false positives describe errors relative to the simulated labels. They should not be interpreted as estimates of patient harm, treatment safety, or unnecessary antidepressant restriction in clinical practice.

Figure 6. Confusion matrix for the proposed ensemble at the validation-selected threshold of 0.30 in the synthetic test set. True AICA: 31 correctly classified and 6 missed. True non-AICA: 86 correctly classified and 5 classified as AICA.

Figure 4Figure 4 presents SHAP dependence plots for the three highest-ranked variables. Prior AICA history produced a strong binary separation in SHAP contributions, lower IS values were associated with larger positive contributions, and simulated mood stabiliser adequacy was associated with lower predicted risk. These patterns are coherent with the rules used to generate the synthetic outcome. The apparent change in slope around IS = 0.45 is a model-dependent feature of this simulation and should not be interpreted as a validated clinical threshold or contraindication criterion.

Table 2 and Figure 7Figure 7 present exploratory BIC-, WAIC-, and Bayes-factor summaries. Under the stated effective-parameter assumptions, the ensemble had the lowest reported BIC (90.0). The resulting Bayes factors were extremely large because the ensemble was assigned an effective parameter count of four for the logistic-regression meta-learner, whereas the complexity of the fitted base learners was represented differently. Consequently, these values should be interpreted as assumption-dependent model-fit and parsimony summaries, not as evidence of clinical superiority or a replacement for held-out discrimination. The ensemble and XGBoost had nearly identical test AUCs, and the information-criterion analysis answers a different question [22].

Table 2. Bayesian model comparison: BIC, WAIC, and bayes factors.

Log₁₀ (BF): base-10 logarithm of the Bayes factor relative to the proposed ensemble under the manuscript’s effective-parameter assumptions. These assumption-dependent values should be interpreted separately from held-out AUC, calibration, and external validity.

Figure 7. Exploratory model-fit and parsimony comparison. Left: reported BIC values under the stated effective-parameter assumptions. Right: corresponding log₁₀ Bayes-factor summaries relative to the ensemble. These quantities do not demonstrate superior real-world predictive performance.

Table 3 presents exploratory performance across overlapping synthetic subgroups. Event counts were: BD-I, 20 AICA events among 64 cases; BD-II, 17/64; prior AICA history, 20/23; no adequate mood stabiliser, 28/81; TCA/SSRI exposure, 23/74; and low IS score, 25/64. Approximate AUC intervals were BD-I 0.873 (95% CI: 0.767 - 0.979), BD-II 0.991 (0.959 - 1.000), prior AICA history 0.800 (0.572 - 1.000), no adequate mood stabiliser 0.947 (0.887 - 1.000), TCA/SSRI exposure 0.938 (0.867 - 1.000), and low IS 0.893 (0.804 - 0.982). Wilson sensitivity intervals were BD-I 0.800 (0.584 - 0.919), BD-II 0.882 (0.657 - 0.967), prior AICA history 1.000 (0.839 - 1.000), no adequate mood stabiliser 0.893 (0.728 - 0.963), TCA/SSRI exposure 0.783 (0.581 - 0.903), and low IS 0.800 (0.609 - 0.911). The wide intervals, especially where few non-events were present, show that the very high point estimates are unstable. Subgroup differences may reflect simulator assumptions and should not be interpreted as biological or clinical effects.

Table 3. Subgroup analysis-proposed ensemble performance.

Test set (n = 128). Low IS score = below the test-set median. Subgroups overlap. Event counts and approximate uncertainty intervals are reported in the accompanying text; estimates should be interpreted cautiously because some subgroups contain few events or non-events.

Figure 8Figure 8 provides local SHAP explanations for two contrasting observations from the held-out synthetic test set. In the high-confidence AICA example (predicted probability = 0.98), the model output is driven predominantly by the prior-AICA feature, with smaller positive contributions from mixed-episode burden, mood-stabiliser-related variables, circadian IS, and the number of mixed episodes. Small negative contributions from antidepressant-class risk and BD subtype partially offset this pattern but are insufficient to change the final classification. In the high-confidence non-AICA example (predicted probability = 0.01), the combined feature pattern shifts the model output in the opposite direction; the strongest

Figure 8. SHAP waterfall plots for one high-confidence synthetic AICA prediction (left) and one high-confidence synthetic non-AICA prediction (right). The plots illustrate how the fitted ensemble decomposes predictions under the simulated feature and label structure. Red contributions increase the predicted AICA probability and blue contributions decrease it; the examples are descriptive and not clinical case explanations.

negative contribution again comes from the prior-AICA feature state, followed by mood-stabiliser adequacy, mixed-episode fraction, sleep-onset variability, IS score, and the number of mixed episodes. The two cases therefore illustrate how the ensemble combines several local contributions rather than applying a single deterministic rule. Because SHAP values describe model attribution on the model-output scale, they do not establish causality; moreover, local directions can differ from global average associations when nonlinear interactions and correlated predictors are present. These entirely synthetic examples must not be interpreted as patient-level clinical explanations or treatment recommendations.