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Synthetic minority data is redundant or invalid: a data-dependent validity theory and a de-biased test
Ahmad B. Hassanat, Ahmad S. Tarawneh, Ghada A. Altarawneh
Intelligence
Status: succeeded | Model: Gemma-4-26B-A4B | Prompt: intel-v1 | Confidence: 93%
Last extracted: 7/24/2026, 2:15:47 AM
Summary
This paper challenges the validity of synthetic minority oversampling techniques (like SMOTE) for class-imbalanced learning. It argues that standard validity checks are biased because they score synthetic points against the data that generated them. The authors propose a de-biased estimator using withheld real data to assess validity. They prove that validity is a property of the data (specifically, class overlap) rather than the method, establishing an 'invalidity floor' that no faithful generator can escape. Empirical audits across 91 methods show that synthetic data is often redundant or invalid, providing negligible information gain and damaging model calibration compared to simple baselines like class weighting.
Entities (11)
Relation Signals (10)
class overlap → causes → Invalidity Floor
confidence 95% · class overlap sets an invalidity floor no faithful generator escapes
resample-audit → implements → De-biased Validity Test
confidence 95% · we release resample-audit... that reports both [validity and information gain]
ERsplit → isa → De-biased Validity Estimator
confidence 95% · The resulting estimator, ERsplit, is consistent
ERnaive → isa → Classical Validity Check
confidence 95% · The standard check computes... ERnaive
SMOTE → isa → Synthetic Minority Oversampling Technique
confidence 95% · SMOTE [1] and its descendants number well over a hundred variants
SMOTEFUNA → isa → Oversampler
confidence 92% · we audit SMOTEFUNA [4], an oversampler from our own group
SMOTEFUNA → fails → De-biased Validity Test
confidence 90% · the de-biased test finds up to 88% of its certified 'minority' to be majority in truth
ERsplit → outperforms → ERnaive
confidence 90% · the de-biased estimator tracks it closely... while the classical test underestimates true invalidity
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Abstract
Abstract:For two decades, the standard remedy for class-imbalanced learning has been to fabricate synthetic minority examples, and the standard evidence of their validity has been a check that cannot fail: synthetic points are scored against the very data that generated them. We de-bias the check. Validity becomes a population quantity -- the probability that a synthetic point truly belongs to the minority class -- with a consistent estimator that scores synthetic points against withheld real data. Where held-out ground truth is available, the classical test underestimates true invalidity in 96-99% of method-by-imbalance-ratio cells, while the de-biased estimator tracks it closely. We prove validity is a property of the data, not the method: class overlap sets an invalidity floor no faithful generator escapes, making oversampling redundant where classes separate and invalid where they overlap. Across 91 methods, three classifiers, and datasets spanning medicine and finance -- including a generator engineered to pass the classical check -- none clears both bars: gains over the best trivial baseline are noise-thin (median below 0.01 F1, a decision threshold's reach), and most damage calibration. We release the audit as a pip-installable test and flip the burden of proof: synthetic minority data must now demonstrate, on the data at hand, both validity and information gain.
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- Source: https://arxiv.org/abs/2607.20787v1
- Canonical: https://arxiv.org/abs/2607.20787v1
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Synthetic minority data is redundant or invalid: a data-dependent validity theory and a de-biased test Ahmad B. Hassanat Corresponding author: ahmad.hassanat@gmail.com Faculty of Information Technology, Mutah University, Karak, Jordan Ahmad S. Tarawneh Faculty of Information Technology, Mutah University, Karak, Jordan Ghada A. Altarawneh Department of Accounting, Mutah University, Karak, Jordan Abstract For two decades, the standard remedy for class-imbalanced learning has been to fabricate synthetic minority examples, and the standard evidence of their validity has been a check that cannot fail: synthetic points are scored against the very data that generated them. We de-bias the check. Validity becomes a population quantity—the probability that a synthetic point truly belongs to the minority class—with a consistent estimator that scores synthetic points against withheld real data. Where held-out ground truth is available, the classical test underestimates true invalidity in 96–99% of method-by-imbalance-ratio cells, while the de-biased estimator tracks it closely. We prove validity is a property of the data, not the method: class overlap sets an invalidity floor no faithful generator escapes, making oversampling redundant where classes separate and invalid where they overlap. Across 91 methods, three classifiers, and datasets spanning medicine and finance—including a generator engineered to pass the classical check—none clears both bars: gains over the best trivial baseline are noise-thin (median below 0.01 F1, a decision threshold’s reach), and most damage calibration. We release the audit as a pip-installable test and flip the burden of proof: synthetic minority data must now demonstrate, on the data at hand, both validity and information gain. 1 Introduction A hospital deploys a model to flag a rare, lethal post-surgical complication. The complication occurs in one patient in fifty, so before training, the team reaches for the default remedy for class imbalance: a synthetic oversampler that manufactures artificial “patients” until the classes balance. The practice is ubiquitous—SMOTE [1] and its descendants number well over a hundred variants, cited across medicine, fraud detection, genomics and ecology [2]—and it feels safe, because the synthetic points can be checked: score each one against the training data, confirm that its nearest real neighbours are minority patients, and certify the augmentation as valid. The trouble is that this certificate is printed by the party it certifies. The synthetic points are interpolations between real minority cases, so their nearest neighbours in the training sample are, with high probability, their own parents—and a parent votes “minority” by construction. The check is not measuring whether synthetic points represent the minority population; it is measuring whether interpolation lies near its own endpoints, which is a tautology. We show this parent leakage is a systematic, sample-size-independent bias (Lemma 0L); beneath it lies an epistemic limit. In the worst case no statistic of the training sample alone can falsify the claim that a synthetic point is minority—a two-point Le Cam construction exhibits a data-independent generator unfalsifiable at any sample size (Proposition 0). That is an existence result about worst-case generators; what convicts interpolators concretely is the parent-leakage bias of Lemma 0L. Either way, synthetic data cannot certify itself: falsification needs withheld reference data. The repair is as old as statistics: withhold. Define validity as a population quantity—V(G)V(G), the expected probability that a point drawn from generator G truly belongs to the minority class—and estimate its complement by scoring synthetic points against real data the generator has never seen. The resulting estimator, ERsplitER_split, is consistent (Proposition 1), costs one line of protocol, and changes the verdict everywhere. On three clinical datasets from our own earlier studies, the classical check certifies 30, 14 and 19 of ninety-one oversamplers as valid; the de-biased check certifies none of the three. And where reality itself is available to consult—datasets rich enough that we can hide real minority cases and treat them as ground truth—the de-biased estimator tracks true invalidity closely (dataset-level correlation 0.79–0.93; per-ratio cells 0.47–0.98, weakest near class balance; mean error 0.03–0.05), while the classical test underestimates it in 96–99% of cells (method × imbalance-ratio combinations), by a margin that grows exactly where the stakes do: as imbalance becomes extreme (Fig. 1, Fig. 2). What “invalid” means. The word carries a precise, deliberately narrow sense: a synthetic point is invalid when it falls in the Bayes-majority region at the deployment prior, however faithfully it mimics a real minority case—a statement about the operating class balance, not about realism. This is exactly why the criterion bites, and why it convicts even real data: as an identity control makes concrete (§3), verbatim real minority, scored the same way, is itself judged invalid at the same floor rate, because under class overlap the minority-typical region is genuinely majority-dominated. The invalidity is a fact about the data’s geometry and prior, not an artefact of fabrication—and it is precisely the cost a classifier pays when overlap-region synthetic points are trusted as minority. Why does a fabricated patient look valid to the sample yet prove majority in truth? Because validity was never the method’s property to lose—it is the data’s property to grant. Our central result (Principle D with Theorem 1) decomposes any generator’s invalidity into a data-driven floor and a method-driven excess: 1−V(G)=[1−V∞(P)]+[V∞(P)−V(G)]1-V(G)=[1-V_∞(P)]+[V_∞(P)-V(G)]. The floor is set by the overlap of the true class distributions: where minority and majority intermingle, a fraction of genuinely minority-typical space is nonetheless majority-dominated, and any generator faithful to the minority distribution—SMOTE in its large-sample limit [3], or a perfect sampler of the minority density itself—inherits that fraction as irreducible invalidity. A method escapes the floor only by abandoning the overlap region, which forfeits faithfulness and, as we show, any information gain. The dilemma has two horns and no exit: where classes separate the floor vanishes but a plain classifier already succeeds, so oversampling is redundant; where classes overlap the classifier needs help exactly where synthetic points are invalid. In a controlled sweep of class separation, the trajectory of every oversampler hugs these two axes and never enters the valid-and-informative corner (Fig. 4). The prescription follows from the accounting. At the model level, appending synthetic minority of density g is exactly class-weighting plus a geometric error term r(x)r(x) that vanishes only when g equals the true minority density (Lemma C)—so everything recoverable about oversampling is available for free from a class weight or a decision threshold, and everything else is unrecoverable distortion that no scalar recalibration can remove. The empirical record agrees, and it is classifier-independent: across 91 methods, logistic regression, XGBoost and LightGBM, honest protocols show median F1 gains over the best trivial baseline near zero, PR-AUC and ROC-AUC unmoved, and calibration worsened in 77–93% of cases. The apparent wins reported for two decades are, on an honest test, threshold shifts in disguise—reproducible for free, at no calibration cost, by moving the threshold (Fig. 5). We close the case from both ends. Data-side: on credit-card fraud—a new domain, a new feature geometry, imbalance up to 450:1—the same gap, the same tracking of held-out truth, the same redundancy (Fig. 6). Method-side: we audit SMOTEFUNA [4], an oversampler from our own group whose acceptance rule is the classical validity check, built into the generator. It passes that check perfectly—ERnaive=0.000ER_naive=0.000 by construction—and the de-biased test finds up to 88% of its certified “minority” to be majority in truth (Fig. 7). A criterion that a method can saturate while failing is a gamed criterion [5]; the withheld-data estimator is the version that cannot be gamed [6]. This paper therefore asserts a standard, not a prohibition: a synthetic-minority method earns its place on a given dataset only by demonstrating validity (ERsplit→0ER_split→ 0, against withheld data) and information gain (performance no trivial baseline matches), and we release resample-audit, a documented, pip-installable instrument that reports both for any resampler on any dataset in one call. Because validity is data-dependent, it cannot be assumed to transfer from benchmark to deployment—it must be measured in place. The burden of proof flips from those who question synthetic minority data to those who deploy it. Our contributions: (i) a population validity functional V(G)V(G) with a consistent, de-biased estimator, validated against held-out ground truth (§2); (i) an impossibility account—unfalsifiability of self-certification (Prop. 0), the data-driven floor 1−V∞1-V_∞ (Thm. 1, Principle D), and the contamination identity (Lemma C) unifying validity, redundancy and calibration harm in one frame that also explains prior findings [3, 7, 8, 9, 10]; (i) the largest honest audit to date—91 methods, three classifiers, medical, financial and high-dimensional data, plus deep generative oversamplers—with both capstones (a new domain; a check-gaming method) (§4–§5); (iv) a released, DOI-archived diagnostic tool and full reproduction pack (§6). Earlier instruments from our group [11, 12] already withheld the majority side of the reference; this work completes the de-biasing on the minority side—a continuation, not a recantation, of that program. Figure 1: Withhold, then test against what was withheld. (a) The classical check retains the synthetic point’s own parents in the reference, so its nearest real neighbour is a parent that votes “minority” by construction (ERnaive≈0ER_naive≈ 0). (b) The de-biased check generates on one half of each class and scores against the withheld half, where the nearest real neighbour is majority (ERsplitER_split is consistent for 1−V(G)1-V(G)). (c) The ground-truth design hides real minority before generation and scores against it. Geometry is computed, not drawn. 2 A validity functional and a de-biased estimator Validity as a population claim. Let the data law P have minority and majority class-conditional densities f1,f0f_1,f_0 with priors π1,π0 _1, _0, and let η(x)=P(Y=1∣X=x)η(x)=P(Y=1 X=x) be the true posterior. A generator G that emits synthetic “minority” points X~∼g X g makes a population claim about each: this point is more likely minority than majority, i.e. η(X~)≥12η( X)≥ 12. We define the synthetic validity of G as V(G)=X~∼g[η(X~)]V(G)=E_ X g[η( X)] (Definition 1), and its information gain I(G)I(G) as the improvement in downstream performance over the best trivial alternative—no resampling, class-weighting, or a tuned decision threshold—under an honest protocol that resamples only training data (Definition 2). The standard this paper asserts is a conjunction: a generator earns its place on a dataset only if V(G)→1V(G)→ 1 and I(G)>0I(G)>0 there. Why the classical check cannot fail (Fig. 1). The field’s default check computes, for each synthetic point, the class of its nearest real neighbour in the training sample that generated it, and reports the majority-vote rate—ERnaiveER_naive. Interpolating generators place each synthetic point between two of its own minority parents, which remain in the reference. We show (Lemma 0L) that for SMOTE-type generators the nearest reference neighbour of a synthetic point is one of its own parents with probability bounded below uniformly in the sample size: parent and independent-reference distances shrink at the same n−1/dn^-1/d rate, so the leakage never washes out, and a parent votes “minority” by construction. The result is a non-vanishing downward bias—ERnaiveER_naive converges not to 1−V(G)1-V(G) but to a quantity smaller by a constant factor. Empirically the effect dwarfs this worst-case bound—ERnaiveER_naive near 0.0000.000 against ERsplitER_split near 0.80.8 on overlapping clinical data—so Lemma 0L, which only certifies a positive capture probability p⋆>0p >0, understates the bias it names. This is bias, not noise; no amount of data repairs it. The deeper obstruction is informational. Proposition 0 formalizes it as a two-point argument in the style of Le Cam [13]: for any statistic T computed from the training sample and the synthetic points, there exist two populations, identical except on a region the sample is unlikely to have probed, whose induced distributions of T are within total variation nεn of each other, yet whose true validities differ maximally. This is a worst-case existence result—the separating generator is data-independent, so it shows self-certification is unfalsifiable in principle; the interpolator-specific conviction is instead the parent-leakage bias of Lemma 0L. Either way, synthetic data cannot certify itself—falsifiability requires reference data the generator has never seen, and scales with the amount of withheld real data and nothing else (Proposition 0′). The de-biased estimator. Split each class at random into halves A and B; run the generator on A only; score each synthetic point by the class of its nearest neighbour in B—real data the generator never saw—and average over splits: ERsplit=Pr(nearest B-neighbour of X~ is majority)ER_split= (nearest B-neighbour of X is majority). Proposition 1 shows ERsplitER_split is consistent for 1−V(G)1-V(G): the nearest-neighbour vote converges to a Bernoulli draw of η(X~)η( X) [14], so its mean converges to [1−η(X~)]E[1-η( X)]. We report Wilson intervals throughout, use a scale-free distance by default [15], and provide a k-nearest-neighbour variant for high-dimensional regimes (§7). Withholding, not the particular vote, is the substance: our earlier instruments [11, 12] already hid a share of the majority from the generator; ERsplitER_split completes the same de-biasing on the minority side, and the ground-truth design below closes the triangle by hiding minority. One epistemic device—withhold, then test against what was withheld—in three roles: falsify, estimate, verify. Verification against reality. An estimator of a population quantity should be checked against the population, and imbalance offers a natural way: take a dataset rich in real minority, remove most of it to manufacture the target imbalance, run the generators on the depleted data, and score their synthetic points against the removed—genuinely real, genuinely unseen—minority. Call the resulting oracle ERtruthER_truth. Across four datasets and 1,040 method-by-imbalance cells (Fig. 2; fraud in §5): MAE vs truth corr. with truth classical dataset (cells) classical de-biased classical de-biased underestimates spambase (383) 0.318 0.052 0.67 0.91 96% MagicTelescope (310) 0.357 0.039 0.43 0.93 99% Pima diabetes (159) 0.592 0.036 0.21 0.79 97% credit-card fraud (188) 0.133 0.037 0.79 0.90 96% Table 1: The de-biased estimator (ERsplitER_split) tracks held-out real invalidity; the classical test (ERnaiveER_naive) underestimates it in 96–99% of cells. MAE and correlation are against the oracle ERtruthER_truth. The de-biased estimator tracks held-out reality to within a few hundredths and ranks methods almost as truth does; the classical test’s shortfall grows with the imbalance ratio (Fig. 2)—blindness is worst exactly where oversampling is reached for. A closed-form control confirms the estimator itself is not the artifact: in a two-Gaussian model where 1−V∞1-V_∞ is analytic, ERsplitER_split tracks the exact curve within ±0.011± 0.011 at every imbalance from 1:1 to 100:1 and at every reference size, while ERnaiveER_naive undershoots by a margin growing to 0.22 (Fig. 3). The verdict on real data. Re-auditing the clinical datasets of our earlier medical study under both protocols: the classical check certifies 30 of 91 oversamplers on Pima diabetes, 14 on thoracic surgery, 19 on Framingham; the de-biased check certifies 0, 0 and 0, with median invalidity 0.49, 0.83 and 0.79. Methods the 2022 protocol scores as perfect (ERnaive=0.000ER_naive=0.000) carry de-biased invalidity of 0.58–0.86 on clinical data. The gap between the two columns is Lemma 0L made visible: the invalidity the field’s standard check structurally cannot see. 3 Validity is data-driven The decomposition. Write V∞(P)=X∼f1[η(X)]V_∞(P)=E_X f_1[η(X)] for the validity of a perfect minority sampler—a generator that draws from the true minority density itself. Then any generator’s invalidity splits identically into two parts (Principle D): 1−V(G)=[ 1−V∞(P)]⏟data-driven floor+[V∞(P)−V(G)]⏟method-driven gap.1-V(G)\;=\; [\,1-V_∞(P)\,]_data-driven floor\;+\; [\,V_∞(P)-V(G)\,]_method-driven gap. (1) The first term depends only on the data law: the minority-typical probability mass that falls in majority-dominated territory. Under class overlap—a positive fraction ε∞ _∞ of minority draws land where the likelihood ratio favours the majority—the floor is strictly positive, 1−V∞≥ε∞/2>01-V_∞≥ _∞/2>0 (Theorem 1), and it is independent of sample size: a limit, hence bias, not variance. Validity is therefore not a certificate a method carries between datasets; it is granted, or refused, by the data. Why the floor is real and is the last layer standing. Theorem 1 leans on recent limit theory rather than fighting it. Sakho et al. [3] prove SMOTE’s law converges to f1f_1 itself as the minority sample grows; Lyu et al. [8] bound its finite-sample interpolation bias and show it decays. Stacked, the picture has three layers: a transient interpolation bias that vanishes (Lyu), convergence to the true minority density (Sakho), and—our contribution—the floor 1−V∞>01-V_∞>0 that the true minority density itself carries under overlap. The first two wash out; the third cannot, because it belongs to P. It is exactly what ERsplitER_split estimates, and the two-Gaussian control (Fig. 3) displays it in closed form: the floor rises from 0.33 to 0.95 as imbalance grows from 1:1 to 100:1 while the classical check reports a flat near-zero. The sharpest evidence is an identity control: verbatim real minority, scored through the same protocol, is itself judged invalid at the floor rate (ERsplitER_split 0.18–0.84 across the six datasets, equal within noise to the best generators) while the classical check calls it perfectly valid (ERnaive=0.00ER_naive=0.00)—the invalidity belongs to the data’s overlap, not to fabrication (Table S3). No escape through the gap. Can a method beat the floor—achieve V(G)>V∞(P)V(G)>V_∞(P)? Yes, trivially: emit points only from the minority’s safest core, far from the boundary. But that surplus is bought by unfaithfulness (g≠f1g≠ f_1), and it is the wrong purchase: the abandoned overlap region is where a classifier needed help, so information gain goes to zero even as measured validity improves; and by Lemma C the distortion g≠f1g≠ f_1 is the unrecoverable part of the model-level damage. A generator escapes the floor only by failing the other two criteria. Validity is necessary, not sufficient—our deep-generator track makes the dissociation concrete: variational autoencoders achieve better validity than SMOTE on near-separable data (ERsplitER_split 0.10–0.13 versus 0.22 on sylva) and still add nothing over a class weight. Two horns, one continuum. Fixing imbalance at 20:1 and sweeping class separation ties the theory in one picture (Fig. 4). As separation grows, ERsplitER_split falls monotonically from 0.79 to 0.02—the synthetic points become genuinely valid—while the baseline classifier’s F1 rises to 1.0 and information gain stays ≤0≤ 0 at every point, reaching exactly zero only at the valid end. In the (validity, information-gain) plane, the trajectory hugs the axes; the valid-and-informative corner is empty, and random oversampling traces the same path as SMOTE—the shape belongs to the problem geometry, not to any method. Real data supply the anchors: on shuttle_c0_vs_c4 (imbalance 14:1, separable), SMOTE’s points are perfectly valid (ERsplit=0.000ER_split=0.000) and perfectly useless (Δ 1=0.000=0.000, Δ =0.000=0.000, baseline F1 0.984); on page_blocks0 at comparable imbalance the same method is invalid (0.223) and calibration-harmful (+0.11+0.11 ECE). Same instrument, same method, opposite verdicts—chosen by the data. This forecloses the natural rebuttal “use oversampling where its points are valid”: there, they are valid and buy nothing. The contamination identity—the model-level ledger. Adding mass w of density g to the minority intensity shifts a calibrated learner’s target posterior by a logit gap δ(x)=log(1+wπ1g(x)f1(x))=logπ1+wπ1+r(x),r≡0⇔g=f1δ(x)= \! (1+ w _1 g(x)f_1(x) )= _1+w _1+r(x), r≡ 0 g=f_1 (2) (Lemma C). The first term is a constant prior-shift—exactly class-weighting, removable by a scalar offset or threshold move, ranking-invariant. The remainder r(x)r(x) is geometric distortion that no scalar correction (offset or temperature), and under mild conditions no univariate recalibration (Platt, temperature, isotonic), can remove. The dilemma at the model level: oversampling ≡ class-weighting ++ an uncontrolled, unrecoverable error term, and the term vanishes precisely where oversampling was redundant anyway. This turns the standard defence—“oversampling is just implicit cost-sensitive learning”—into our theorem, and sharpens it: cost-sensitive learning is a family (loss reweighting at training time; cost-optimal thresholds at decision time [16]; example-dependent costs), and the recoverable part of oversampling equals its simplest member—class weighting with a=(π1+w)/π1a=( _1+w)/ _1—not some richer cost structure. The defence is exactly true iff g=f1g=f_1, i.e. iff the method does nothing a class weight doesn’t. We test the identity. Fit models on oversampled data, then grant each its best possible scalar logit correction (an oracle upper bound on any honest recalibration). Class-weighted models return to baseline calibration under the analytic offset alone, as the g=f1g=f_1 case predicts. Oversampled models do not: on every overlapping dataset, 86% remain above baseline calibration error even under the oracle, with median residuals four to five times class-weighting’s; on near-separable data the residual collapses. The unremovable part of the harm—r(x)r(x)—is measurable, and it lives exactly where the validity floor does. 4 No information a threshold could not add Validity asks whether the synthetic points are real minority; information gain asks whether they help. We measure the second under an honest protocol—split first, resample the training half only, evaluate on untouched test data—against the three trivial baselines any practitioner has for free: no resampling, class-weighting, and a cross-validated decision threshold. Every comparison is per-dataset against the best of the three. The result is not that no method ever edges a baseline—a handful do, by hundredths of an F1 point—but that no gain exceeds what a decision threshold already supplies: the margins are noise-thin (median beat below 0.01 F1), they vanish or reverse under boosting, and they come with worse calibration. Paired with the validity floor, no method clears both bars at once. The margins are noise-thin, and the direction is consistent. Across six naturally-imbalanced datasets and 91 methods under logistic regression—all 91 on every set except fraud, where 76 run and 15 are omitted for runtime (SI)—the best oversampler beats the best trivial baseline by between +0.004+0.004 and +0.107+0.107 F1, with median beat below 0.01. A test-set bootstrap (2,000 resamples) settles significance: across all six datasets and three classifiers (17 cells, Table S7), not one of the best methods has a Δ 1 95% CI excluding zero—the largest margin anywhere, Pima’s +0.035+0.035, carries CI [−0.013,+0.079][-0.013,+0.079] (p=0.08p=0.08)—and on two boosted accidents cells the best margin is significantly negative. The largest apparent “gains” occur only where the no-resampling baseline degenerates outright (thoracic surgery, where unweighted training collapses to the majority class). Under XGBoost, pooled across the five real datasets: median Δ 1 +0.0007+0.0007 versus no-resampling, median Δ −0.0004-0.0004, median Δ 0.00000.0000, and 65% of pairs worsen calibration; 21% beat their best trivial baseline at all. Under LightGBM: 14%. One cell runs with the trend rather than against it—sylva under XGBoost, where 54 of 87 methods edge no-resampling—but by at most +0.014+0.014 F1, on a near-separable set whose plain model already scores F1 0.950.95, with 71 of 87 worsening calibration and none clearing validity: a majority of tiny, calibration-costly wins on an easy set, not new signal. On the largest real-world set (traffic-accident severity, n≈12,700n≈ 12,700; [17]), zero of 87 methods beat threshold-moving under either boosted model. The thesis is classifier-independent. The illusion, named. How has two decades of literature reported the opposite? Two mechanisms, both measurable. The first is evaluation leakage: oversampling before splitting, so near-copies of test minority appear in training—widespread in the applied literature and repaired by a one-line reordering. The second survives honest evaluation: F1 at the default threshold rises while nothing about the model’s ranking improves. Across 614 method-dataset points (Fig. 5; this pooled count spans every benchmarked dataset and classifier, including the two Parkinson sets, whereas the per-method ranking tables of the appendix report the 515 cells of the six logistic-regression datasets), median Δ 1 is +0.06+0.06 while median Δ is −0.0002-0.0002 and Δ −0.0026-0.0026; on the five real datasets the split is starker—median Δ 1 +0.139+0.139 against Δ −0.005-0.005, with 62% of points raising F1 while PR-AUC does not improve, and Brier worsening in 90%. A gain in F1 with flat AUCs is the signature of an operating-point shift: the model did not learn more, its threshold moved—reproducible for free, without fabricated data and without the calibration cost, by moving the threshold. The calibration cost grows with the apparent F1 gain, exactly as r(x)r(x) predicts; in a deployed risk model a systematically inflated minority probability is the harm. Deep generators do not change the verdict. Conditional VAEs, GANs, CTGAN, TVAE and a tabular diffusion model, through the identical three-tier audit: on high-overlap data their best ERsplitER_split hits the same floor as SMOTE’s (≈0.77≈ 0.77–0.800.80); on near-separable data they achieve better validity than any interpolator—and still no information gain (sylva: best deep F1 0.948 versus class-weight 0.950). A better generative model solves the wrong problem: the floor and the redundancy belong to the data. 5 Two capstone validations Data-side: credit-card fraud. The ULB fraud dataset [18] is everything our development sets are not: financial rather than clinical, PCA-transformed signed features, extreme natural imbalance (578:1; capped at 102:1 for tractability—conservative, since the floor grows with imbalance—for a working set of n≈50,000n≈ 50,000 rows). The findings transfer intact. The classical check certifies 56 of 69 methods; the de-biased check certifies 15, and methods scored perfect by the classical protocol carry ERsplitER_split up to 0.58. Because fraud is largely separable here, the plain classifier is already strong, and the redundancy horn shows in its purest form: under both logistic regression and XGBoost the best baseline is no resampling at all, only 3 of 75 methods exceed it, by at most +0.005+0.005 F1, and ∼ 95% worsen calibration. The ground-truth design pushes to imbalance 150–450—far beyond any benchmark in the battery—and the de-biased estimator stays within 0.037 of held-out truth (correlation 0.90) while the classical test underestimates in 96% of cells by a growing margin (Fig. 6). A new domain, a new geometry, the same three results. Method-side: a generator engineered to pass the old test. SMOTEFUNA [4]—from our own group—draws candidates in the hyper-cuboid between a minority seed and its furthest minority neighbour, then keeps a candidate only if its nearest real neighbour is minority. That rule is the classical validity check, moved inside the generator. It works exactly as designed: under its own metric, ERnaive=0.000ER_naive=0.000 on every dataset tested—not approximately, but by construction (Fig. 7). The de-biased test is unmoved: 31% of its certified minority is majority in truth on Pima, 49% on Framingham, 88% on thoracic surgery, and its information gain is nil (≤+0.01≤+0.01). A criterion a generator can saturate while producing majority points is not measuring validity; it is being gamed—Goodhart’s law [5] with an existence proof, and a construct-validity failure the withheld-data estimator repairs. That the counterexample is our own prior method is the point: the instrument convicts its makers’ work. Two sub-findings sharpen it. The built-in guarantee is metric-fragile—re-scored under a different distance, the same points show ERnaiveER_naive of 0.23 before any de-biasing—so “valid” was never a property of the synthetic data, only of a particular test against a particular sample. And SMOTEFUNA wins the classical comparison against SMOTE (lower ERnaiveER_naive) while losing the real one (higher ERsplitER_split on the hardest set): optimizing the biased criterion actively selects for hidden invalidity. 6 A deployable standard Because validity is data-dependent (Principle D), it cannot be certified on benchmarks and assumed in deployment; it must be measured where the model will live. We release the instrument as resample-audit (PyPI, ≥0.1.1≥ 0.1.1; concept DOI 10.5281/zenodo.21444930; MIT) [19], a dependency-light library whose single call audit(X, y, resampler) accepts anything exposing the standard resampling interface—the SMOTE family, deep tabular generators, or a user’s own method—and returns ERsplitER_split with a Wilson interval, the classical ERnaiveER_naive for contrast, the information gain against the three trivial baselines, ranking and calibration deltas, and a pass/fail verdict against the conjunctive standard. The audit that fills this paper’s tables is the shipped code path, not a private pipeline. For authors of new oversamplers the standard is constructive, not hostile: report V(G)V(G) and I(G)I(G) on your evaluation data, and the first synthetic-minority method to clear both bars will have shown something no member of the current family has. Is the standard passable? It is not vacuous. A method clears it by emitting synthetic minority that is both faithful against withheld data (ERsplit→0ER_split→ 0) and informative beyond a threshold (I(G)>0I(G)>0). The two bars pull in opposite directions for any method whose only input is the observed sample: on separable data faithfulness is easy but information is impossible (the plain model already suffices), while under overlap information lives in the boundary region, where faithfulness fails unless the generator supplies genuinely new knowledge of f1f_1 there—an informative prior, auxiliary data, a mechanistic model, or a measurement the training sample lacks. That is precisely the escape our results leave open: the standard is passable by a generator that injects real information about the minority law, and unpassable by interpolation or density-matching alone, because those only re-express the sample they were given. The bar is set where a genuine advance would clear it. 7 Scope and limitations Where the estimator is trustworthy—and where estimation is not. The de-biased estimator’s ground-truth tracking (corr 0.79–0.93 at the dataset level; 0.47–0.98 per imbalance-ratio cell, weakest near balance) spans datasets from a few hundred to fifty thousand rows. Its honest failure regime is d≫nd n, where SMOTE is known to degrade [20]: on a Spanish-speaker Parkinson’s speech dataset with 100 samples and 589 features [21, 22], it still recovers the level of invalidity five-fold better than the classical test (MAE 0.13 versus 0.63), but its cross-method ranking correlation collapses to 0.22. A k-nearest-neighbour vote targeting the hard validity V1/2V_1/2 removes the estimator-variance part—in a matched controlled model it restores ranking from 0.73 to 0.96, and on the real data it sharpens the level to MAE 0.029—whereupon it exposes the deeper fact: the true hard validity is saturated (0.98±0.040.98± 0.04, 93% of methods above 0.9). In that regime there is no ranking to recover because the entire family fails together. This is an estimation limit, not a counterexample: at d/n≈6d/n≈ 6 no distance-based quantity—including the ground truth itself, from ∼ 12 held-out points—is reliably measurable, and the regime’s lesson (a vast, under-sampled space in which fabricated points find no real support) is the thesis’s mechanism, not its refutation. Finite-reference bias on the smallest set. ERsplitER_split is asymptotic in the withheld reference (Proposition 1); with few withheld minority points the 1-N vote is minority-sparse and the estimate is biased upward—the more so the lower the true floor. We quantify this with the identity generator on two ground-truth sets (Table S4): at a 35-point minority reference the inflation is +0.28+0.28 on Pima (floor 0.490.49) and +0.53+0.53 on spambase (floor 0.120.12), decaying to ≤0.02≤ 0.02 once the reference reaches a few hundred points. Exactly one of our datasets sits in this regime—thoracic surgery, whose 70 minority leave a 35-point reference—so its absolute ERsplitER_split (0.830.83) is inflated and its true floor is uncertain (roughly 0.30.3–0.550.55 after correction). Every other real and ground-truth set withholds ≥134≥ 134 minority (Pima 134, fraud 246, Framingham 278, sylva 402, accidents 928; spambase and MAGIC in the thousands), where the bias is ≤0.02≤ 0.02, so the ground-truth tracking (corr 0.790.79–0.930.93) is measured entirely in the unbiased regime. The verdict is robust—even at the low end of the correction thoracic sits far above the 0.100.10 certification bar and certifies none, and the identity control inflates in lockstep, preserving the real-versus-generator comparison—but thoracic’s absolute magnitude is only an upper bound. Other boundaries. Two methods (E_SMOTE, ISOMAP-Hybrid) emit synthetic points in a transformed feature space; an original-space validity vote is undefined for them by construction, and they are excluded by design. A small set of method-dataset cells are degenerate no-ops—findings, not failures. One benchmark cell (ROSE × sylva × LightGBM) crashes inside LightGBM natively on both Windows and Linux and is footnoted. Our claims concern binary classification with tabular features; extending the validity functional to imbalanced regression requires redefining “invalid synthetic point” for continuous targets—the framework transfers, the instrument is future work. 8 Discussion Twenty years of synthetic oversampling rested on a check that could not fail, and the result was a literature optimizing an unfalsifiable criterion. The repair is not a better generator; it is a better measurement. Once validity is defined on the population and estimated against withheld reality, the phenomenon reorganizes: overlap sets a floor no faithful generator escapes; separability makes generation redundant; the model-level effect decomposes into free class-weighting plus unrecoverable distortion; and the reported gains of the field resolve into threshold shifts measured by a leaky protocol. Findings that circled this object from different directions—the SMOTE limit law [3], its density [7], its vanishing finite-sample bias [8], threshold-dominance [10], calibration harm in clinical models [9]—become facets of one account: we name the object, measure it, bound it, and ship the measurement. The practical prescription is estimation–decision separation, which costs nothing: estimate honest probabilities on the data as they are; encode asymmetric costs where they belong, in the decision rule. Scarcity is signal—the class prior is part of the data-generating process, and a model forced to unlearn it repays the favour with inflated risk estimates precisely for the cases that matter. Where deployment priors genuinely differ, explicit prior correction does what fabricated data does opaquely, without the geometric residue. We do not claim synthetic minority data can never help; we claim helping now has a test. The standard is conjunctive, per-dataset, and public: demonstrate validity against withheld reality, and information beyond a threshold. Nothing in 91 classical methods, five deep generators, or a method built to pass the old check clears it. The claim is falsifiable, and we make the target explicit: a counterexample is a single method that, on a given dataset under a pre-registered protocol, clears both bars at once—low ERsplitER_split against withheld reality and a ranking gain over the best trivial baseline (positive Δ -AUC or Δ -AUC, above noise and reproducible across seeds and classifiers), not merely a higher F1 at the default threshold. We tabulate every method’s per-cell ranking deltas in the Supplementary Information so that this search is fully auditable: across all method–dataset cells the median ranking gain is negative, and the isolated positives are neither valid nor reproducible. An F1F1 gain alone does not qualify, precisely because it is the operating-point shift a threshold reproduces for free. The burden of proof has changed hands. Methods Condensed; formal statements and proofs—Prop. 0/0′, Lemma 0L, Prop. 1, Thm. 1, Principle D, Lemma C—plus full protocol, dataset provenance, environments and the excluded-cell inventory are in the Supplementary Information. Validity protocol. ERnaiveER_naive: 1-N vote against the generator’s own training sample, all parents retained. ERsplitER_split: five random half-splits per class; generate on half A—so the generator is trained on n1/2n_1/2 minority points; because the floor is sample-size-independent (Theorem 1) this does not bias ERsplitER_split as an estimate of 1−V(G)1-V(G), though it modestly raises method-specific variance, which averaging over the five splits controls—then 1-N vote against half B (reference capped at 20,000, all minority kept); Wilson intervals; Hassanat scale-free distance by default [15, 23]; a k-N vote (with k cross-validated; the classical n n rule is dimension-suboptimal, [23]) targets the hard validity V1/2V_1/2 for d≫nd n. Deterministic per-method seeding. Ground truth. Remove real minority to a target ratio; the removed points form the ERtruthER_truth reference; per (method, ratio) cell report naive/split/truth. Benchmark. Stratified 70/30 split; standardize on train; resample train only; LogReg / XGBoost / LightGBM; baselines no-resample, class-weight (per-classifier mechanism), threshold-move (3-fold OOF F1-optimal); F1, ROC-AUC, PR-AUC, Brier, ECE. Per-cell 95% confidence intervals and one-sided significance for the deltas are obtained by bootstrapping the test rows (2,000 resamples; benchmark_ci.py). Data availability. All datasets used are publicly available: the KEEL imbalanced benchmarks [24], the oversampling methods and interfaces of the smote-variants library [25], the ULB credit-card fraud set [18], and the clinical, accident-severity and Parkinson’s speech-feature datasets described in the appendix, whose original sources are cited therein. The processed result CSVs underlying every table and figure are deposited in the paper repository. Code availability. The audit instrument is released as resample-audit (PyPI; Zenodo concept DOI 10.5281/zenodo.21444930; MIT licence). The full experimental harness, figure scripts and reproduction protocol are in the paper repository; every table regenerates via repro_tables.py and every figure via make_all_figures.py. Use of large language models. During the preparation of this manuscript the authors used a large language model-based assistant to support drafting and copy-editing of text, organisation of references, scaffolding and debugging of analysis and figure code, and formatting of tables. It was not used to generate data, experimental results, or scientific claims; all experiments, theoretical results, analyses, and conclusions were conceived, executed, and verified by the authors, who reviewed and edited every output and take full responsibility for the content. The large language model does not meet authorship criteria and is not credited as an author. Figure 2: The de-biased estimator tracks held-out truth across imbalance; the naive protocol’s underestimate grows with the stakes. Mean and median over methods on two ground-truth datasets; shaded band is the invalidity the classical test hides. Figure 3: Closed-form control. In a two-Gaussian model the de-biased estimator tracks the analytic 1−V∞1-V_∞ at every imbalance and reference size; ERnaiveER_naive undershoots by a growing margin. Figure 4: Redundant or harmful. Sweeping class separation at fixed imbalance: validity improves (ERsplit↓ER_split ) while information gain never does; the (validity, information-gain) plane has an empty valid-and-informative corner. Figure 5: The threshold-shift illusion. Oversampling moves the F1 operating point while ranking (AUROC, AUPRC) stays flat and calibration (Brier) worsens. Figure 6: Data-side capstone (credit-card fraud). At imbalance 150–450 the de-biased estimator tracks held-out real fraud; the classical test underestimates in 96% of cells. Figure 7: Method-side capstone (SMOTEFUNA). Its acceptance rule is the classical check, so ERnaive=0ER_naive=0 by construction; the de-biased test finds up to 88% of its certified “minority” to be majority in truth. Author contributions A.B.H. conceived the study, developed the data-dependent validity theory and the de-biased estimator, solely authored the resample-audit software, and led the writing. A.B.H. and A.S.T. designed the audit methodology and experiments, and A.S.T. implemented and executed the benchmark, ground-truth and deep-generator experiments. G.A.A. contributed to dataset curation and to the analysis and interpretation of the clinical and applied results. All authors discussed the findings and reviewed, edited and approved the manuscript. Competing interests The authors declare no competing interests. Supplementary Information Formal statements and proofs supporting the main text. Notation follows §2 of the main text. Results are labelled to match the main text rather than by running number: Propositions 0 and 0′ (impossibility of self-certification), Proposition 1 (consistency of the split estimator), Theorem 1 (the invalidity floor), Lemma 0L (parent leakage in the classical check), Lemma C (the contamination identity), and Principle D (the data-driven decomposition). Appendix A Formal framework Setup. A population P on ℝd×0,1R^d×\0,1\ has class priors π1=ℙ(Y=1) _1=P(Y=1), π0=1−π1 _0=1- _1 with π1≤π0 _1≤ _0, class-conditional densities f1,f0f_1,f_0 w.r.t. a common dominating measure, and posterior η(x)=π1f1(x)/(π1f1(x)+π0f0(x))η(x)= _1f_1(x)/( _1f_1(x)+ _0f_0(x)). Write ρ=π0/π1≥1ρ= _0/ _1≥ 1. A generator G trained on D=(Xi,Yi)i=1nD=\(X_i,Y_i)\_i=1^n produces synthetic minority points X~1,…,X~m∼g X_1,…, X_m g (the density g may depend on D). All “minority/majority” labels refer to the Bayes rule [η≥12]1[η≥ 12], i.e. to the population, never to training labels. Definition 1 (synthetic validity). V(G)=X~∼g[η(X~)]∈[0,1]V(G)=E_ X g[η( X)]∈[0,1]; the invalidity is 1−V(G)=X~∼g[1−η(X~)]1-V(G)=E_ X g[1-η( X)]. The hard invalidity is 1−V1/2(G)=X~[[η(X~)<12]]1-V_1/2(G)=E_ X[1[η( X)< 12]]. Definition 2 (information gain). For a learner ℓ and metric M, let Mtriv⋆(D)M _triv(D) be the best test-set M over \no-resample, class-weight, threshold-move\ fit on D, and M(G,D)M(G,D) the test-set M of ℓ trained on D augmented by G. Then I(G)=M(G,D)−Mtriv⋆(D)I(G)=M(G,D)-M _triv(D). The standard is the conjunction V(G)→1∧I(G)>0\V(G)→ 1\ \I(G)>0\ on the dataset at hand. Appendix B Unfalsifiability and the repair by withholding Proposition 0 (self-certification is impossible). Fix any n,mn,m and any statistic T=T(D,X~1:m)T=T(D, X_1:m). For every ε>0 >0 there exist populations P,P′P,P and a data-independent generator G such that P,P′P,P differ only on a region A with mass ≤ε≤ , carry opposite Bayes labels on A, yet TV(LawP(T),LawP′(T))≤nεTV(Law_P(T),Law_P (T))≤ n free of m, while |VP(G)−VP′(G)|=1|V_P(G)-V_P (G)|=1. Proof. Two-point (Le Cam) construction [13]. Fix a marginal law μ for X and a Borel region A with μ(A)≤εμ(A)≤ . Define P and P′P to share the marginal μ and the posterior η off A, and to differ only on A: put η≡1η≡ 1 on A under P (Bayes-minority) and η≡0η≡ 0 on A under P′P (Bayes-majority); for ε small the added minority mass keeps π1≤π0 _1≤ _0 in both populations. Take the generator G to be data-independent with law Unif(A)Unif(A), identical under P and P′P . Then VP(G)=X~[ηP(X~)]=1V_P(G)=E_ X[ _P( X)]=1 and VP′(G)=X~[ηP′(X~)]=0V_P (G)=E_ X[ _P ( X)]=0, so |VP(G)−VP′(G)|=1|V_P(G)-V_P (G)|=1. Couple the two experiments on a common probability space: draw X1,…,Xn∼iidμX_1,…,X_n μ (shared) and X~1:m∼Unif(A) X_1:m (A) (shared, drawn independently of the labels). Off A assign each YiY_i by the common conditional; on A set Yi=1Y_i=1 under P and Yi=0Y_i=0 under P′P . On the event E=Xi∉Afor all iE=\X_i∉ A\ for all i\ the pair (D,X~1:m)(D, X_1:m)—and hence any statistic T(D,X~1:m)T(D, X_1:m) of it—is identical under P and P′P . The coupling inequality gives TV(LawP(T),LawP′(T))≤ℙ(Ec)≤∑i=1nℙ(Xi∈A)=nμ(A)≤nε,TV (Law_P(T),Law_P (T) )\ ≤\ P(E^c)\ ≤\ _i=1^nP(X_i∈ A)\ =\ n\,μ(A)\ ≤\ n , free of m, since the synthetic points are coupled identically and their law does not depend on P versus P′P . Thus no statistic of the generator together with its own training data can separate two populations of maximally different validity; the discriminating signal is confined to the O(nε)O(n ) probability that a training point lands in A. ∎ Proposition 0′ (withholding restores identification). Fix (P,G)(P,G) under the regularity of Proposition 1. Let R be a reference sample of size r drawn from P and independent of the data used to fit G. Then ERsplit→ℙ1−V(G)ER_split \ P\ 1-V(G) as r→∞r→∞, and in the construction above the reference distinguishes P from P′P once r≳1/εr 1/ . Lemma 0L (parent retention is a non-vanishing bias). For SMOTE with fixed K, the nearest neighbour of X~ X in a reference that retains its own parents is a parent with probability ≥p⋆>0≥ p >0, with p⋆p depending only on (K,d,π1)(K,d, _1) and local densities and bounded below uniformly in n. Hence ERnaive→[(1−η(X~))(1−p(X~))]≤(1−p⋆)(1−V(G))ER_naive [(1-η( X))(1-p( X))]≤(1-p )(1-V(G)), a downward bias that is bounded away from zero uniformly in n (a constant-factor attenuation, not a vanishing rate). Proof. Write X~=Xi+U(Xj−Xi) X=X_i+U(X_j-X_i) with XiX_i a minority seed, XjX_j one of its K minority nearest neighbours, and U∼Unif[0,1]U [0,1]; the nearer parent lies at distance min(U,1−U)‖Xj−Xi‖≤12‖Xj−Xi‖ (U,1-U)\,\|X_j-X_i\|≤ 12\|X_j-X_i\|. Fix a Lebesgue point x of f0,f1f_0,f_1 with f(x)=π1f1(x)+π0f0(x)>0f(x)= _1f_1(x)+ _0f_0(x)>0 and condition on X~≈x X≈ x. Rescale space by the factor n−1/dn^-1/d about x. By the local (Poisson) limit for nearest-neighbour functionals of an i.i.d. sample whose density is continuous and positive at x [26], the rescaled training points converge in distribution to a homogeneous Poisson process Π of intensity f(x)f(x), within which the minority points are an independent thinning of intensity π1f1(x) _1f_1(x). In this limit the two parents Xi,XjX_i,X_j are points of the minority sub-process at the K-nearest-neighbour scale (K/(π1f1(x)))1/d(K/( _1f_1(x)))^1/d, with X~ X on the segment between them, while the nearest non-parent training point is the nearest point of Π at scale (1/f(x))1/d(1/f(x))^1/d. The two scales stand in the fixed ratio (Kf(x)/(π1f1(x)))1/d (Kf(x)/( _1f_1(x)) )^1/d, independent of n: the parent-versus-field contest is genuinely order one. Hence the event =a parent is the nearest of all training points to X~C=\a parent is the nearest of all training points to X\ has a strictly positive limiting probability p(x)=ℙ(a parent beats every point of Π)∈(0,1),p(x)\ =\ P (a parent beats every point of )\ ∈\ (0,1), a continuous functional of (K,d)(K,d) and the local ratio π1f1(x)/f(x) _1f_1(x)/f(x); on the support carrying g-mass it is bounded below by some p⋆>0p >0 depending only on (K,d,π1)(K,d, _1) and the local density bounds, uniformly in n. On C the vote is minority (a parent is a minority point); off C the nearest non-parent votes majority with probability →1−η(X~)→ 1-η( X) by nearest-neighbour consistency (as in Proposition 1). Therefore ERnaive→[(1−p(X~))(1−η(X~))]≤(1−p⋆)[1−η(X~)]=(1−p⋆)(1−V(G)),ER_naive\ →\ E [(1-p( X))\,(1-η( X)) ]\ ≤\ (1-p )\,E[1-η( X)]\ =\ (1-p )(1-V(G)), a downward bias of at least p⋆(1−V(G))p (1-V(G)): bounded away from zero uniformly in n whenever 1−V(G)>01-V(G)>0. ∎ Proposition 1 (consistency of the split estimator). Under (i) η continuous, (i) f0,f1f_0,f_1 with common support and locally bounded density ratios, (i) reference size →∞→∞ with the generator’s own sample fixed per split, ERsplit→ℙ1−V(G)ER_split \ P\ 1-V(G). Proof. Condition on X~=x X=x. As the withheld reference B grows, its nearest neighbour to x converges to x a.s. (N consistency), and the label of that neighbour is a Bernoulli draw with success probability η(x)η(x) [14]. Hence ℙ(nnB(x)∈majority)→1−η(x)P(n_B(x) )→ 1-η(x). Taking expectation over X~∼g X g and exchanging limit and integral by dominated convergence (integrand in [0,1][0,1]) gives X~[1−η(X~)]=1−V(G)E_ X[1-η( X)]=1-V(G). Averaging over splits preserves the limit. ∎ Remark (separable case). Assumption (i) (common support) is used only to place minority reference mass near synthetic points in the overlap region. Under separability the class supports are disjoint, the overlap mass ε∞=0 _∞=0, and both the floor 1−V∞=01-V_∞=0 (Theorem 1) and ERsplit→0ER_split→ 0 hold trivially: interpolated minority points stay in the minority support, where their nearest withheld neighbour is minority. The separable showcases (sylva, shuttle_c0_vs_c4, fraud) sit in this regime, and the estimator remains consistent by the argument above restricted to each class support. Appendix C The data-driven floor Assumption 1 (Overlap). ℙX∼f1(f1(X)/f0(X)<ρ)=ε∞>0P_X f_1(f_1(X)/f_0(X)<ρ)= _∞>0; a positive fraction of minority-typical points fall in the Bayes-majority region. Under separability ε∞=0 _∞=0. Theorem 1 (invalidity floor). For SMOTE with fixed K and n1→∞n_1→∞ (so K/n1→0K/n_1→ 0), Sakho et al. [3, Thm. 3.2] give convergence in distribution of the SMOTE-generated variable ZK,n1Z_K,n_1 to the minority law: ℙ[ZK,n1∈B]→∫Bf1P[Z_K,n_1∈ B]→ _Bf_1 for every Borel B (a convergence of the full synthetic-point law, not of a marginal statistic). With η bounded continuous the portmanteau theorem then gives V(SMOTEn1)=[η(ZK,n1)]→X∼f1[η(X)]=:V∞V(SMOTE_n_1)=E[η(Z_K,n_1)] _X f_1[η(X)]=:V_∞, so 1−V∞=X∼f1[1−η(X)]=∫(1−η)f1x≥12ε∞> 0under Overlap.1-V_∞=E_X f_1[1-η(X)]= (1-η)f_1\,dx\ ≥\ 12 _∞\ >\ 0 Overlap. Proof. The cited ZK,n1⇒f1Z_K,n_1 f_1 is convergence of the full SMOTE law, so with bounded-continuous η the portmanteau theorem gives the stated limit directly. On f1/f0<ρ\f_1/f_0<ρ\ we have π1f1<π0f0 _1f_1< _0f_0, hence η<12η< 12, hence 1−η>121-η> 12; integrating over that event (mass ε∞ _∞ under f1f_1) gives ∫(1−η)f1≥12ε∞ (1-η)f_1≥ 12 _∞. ∎ The floor is (i) independent of n1n_1 (bias, not variance); (i) inherited even by a perfect minority sampler; (i) exactly what ERsplitER_split estimates. Three literature layers: transient interpolation bias →0→ 0 [8]; limit is f1f_1 [3]; the non-vanishing floor (ours). Principle D. With V∞(P)=f1[η]V_∞(P)=E_f_1[η], 1−V(G)=[1−V∞(P)]+[V∞(P)−V(G)]1-V(G)=[1-V_∞(P)]+[V_∞(P)-V(G)] (add and subtract V∞V_∞). The first bracket depends only on P; the second is method-specific. Moreover V(G)>V∞(P)V(G)>V_∞(P) requires g≠f1g≠ f_1 with mass shifted toward η→1\η→ 1\: by Lemma C the surplus is the unrecoverable r(x)r(x), and mass moved off the overlap boundary reduces I(G)I(G). A generator beats the floor only by failing faithfulness and information gain. Appendix D The contamination identity Lemma C (contamination identity). Append synthetic minority of density g, weight w, to (π1f1,π0f0)( _1f_1, _0f_0) and renormalize; a population-calibrated learner (strictly-proper-loss ERM over a rich class, Gneiting and Raftery [27]) targets ηCM _CM with: (C1) logitηCM(x)=logitη(x)+δ(x)logit\, _CM(x)=logit\,η(x)+δ(x), δ(x)=log(1+wπ1g(x)f1(x))δ(x)= (1+ w _1 g(x)f_1(x)). (C2) δ≡const⇔g=f1δ g=f_1, whence δ≡logπ1+wπ1δ≡ _1+w _1: a scalar offset (ranking/ROC invariant, η recovered exactly), equal to class-weighting with a=(π1+w)/π1a=( _1+w)/ _1. (C3) g≠f1⇒δg≠ f_1 δ non-constant: no scalar offset or scalar temperature restores η off a null set, and if δ varies along an ηCM _CM-level set, no univariate recalibration—any map of ηCM _CM alone, scalar offset, scalar temperature, Platt and isotonic included—restores calibration. (C4) δ(x)=logπ1+wπ1+r(x)δ(x)= _1+w _1+r(x), r(x)=logπ1f1+wg(π1+w)f1r(x)= _1f_1+wg( _1+w)f_1, r≡0⇔g=f1r≡ 0 g=f_1. Hence oversampling ≡ class-weighting ++ geometric error r(x)r(x). Proof. (C1) Bayes’ rule on the contaminated intensities; the normalizer 1/(1+w)1/(1+w) cancels; subtract logits. (C2) δ≡c⇒g/f1≡(ec−1)π1/wδ≡ c g/f_1≡(e^c-1) _1/w on f1>0\f_1>0\, i.e. g=κf1g=κ f_1, and ∫g=∫f1=1 g= f_1=1 forces κ=1κ=1; converse by substitution; class-weight equivalence by the a-weighted posterior. (C3) a non-constant logit gap cannot be closed by a constant offset, nor by any scalar temperature, since a temperature rescaling logitηCM↦logitηCM/Tlogit\, _CM \, _CM/T is itself a function of ηCM _CM alone; more generally, if ηCM(x1)=ηCM(x2) _CM(x_1)= _CM(x_2) but η(x1)≠η(x2)η(x_1)≠η(x_2), every recalibration φ(ηCM) ( _CM)—offset, temperature, Platt or isotonic included—returns one value at the two points and so errs at one of them by ≥ half the gap. (C4) algebra from (C1)–(C2). ∎ Empirical signature. With empirical counts the analytic correction is −log(n1′/n1)- (n_1 /n_1) on the logit. Reporting ECE/Brier raw, after the analytic offset, and after an oracle scalar offset (best single logit shift by test-NLL): class-weight returns to baseline under the analytic offset; 86% of oversampled models (5 real datasets, LogReg, 386 points) remain above baseline even under the oracle, median residual 4–5× class-weight’s; the residual collapses on near-separable data—r lives where the floor does. Appendix E The k-N estimator and hard validity V1/2V_1/2 The default vote (k=1k=1) estimates [1−η]E[1-η] (Proposition 1). A k-N majority vote estimates 1−V1/2=ℙ(η<12)1-V_1/2=P(η< 12) as k→∞,k/n→0k→∞,\,k/n→ 0 (the vote converges to the Bayes label), with lower per-point variance—recommended when d/nd/n is large. In a controlled d=589d=589 model it restores cross-method ranking from ρ=0.73ρ=0.73 (k=1k=1) to 0.960.96 (k≈11k≈ 11–2121); on real high-dimensional data it sharpens the level (MAE 0.13→0.030.13→ 0.03) and reveals a saturated truth (0.98±0.040.98± 0.04), i.e. uniform failure of the family. Here k is a variance-reduction knob on an estimator, not a classifier, and is chosen by cross-validation—the strongest k-selector [23]. The textbook k≈Nk≈ N rule (N the withheld-reference size voted against per split, not the full sample n) is minimax-optimal only at d=4d=4 and is dimension-suboptimal otherwise; the dimension-aware default k≈⌊N4/(d+4)⌋k≈ N^4/(d+4) [23] is the principled non-cross-validated alternative. Our target, however, is the cross-method ranking of an averaged functional ℙ(η<12)P(η< 12) over synthetic points—not per-point 0/10/1 risk—so a moderate k suppresses label-vote variance without materially disturbing that ranking: in the controlled d=589d=589 study (a simulated model, not the 100-row data) the ranking plateaued over k≈11k≈ 11–2121, while on the real set the smaller reference shifts the useful band down. Appendix F Protocols, data, and excluded cells Datasets. Table S1 lists every dataset used in the paper, its domain, size, dimensionality, class split, imbalance ratio (IR == majority/minority), and source. Six real, naturally-imbalanced sets carry the validity gap and benchmark (Tables S2, S6): sylva, a forest-cover-type task from the Agnostic-Learning-vs-Prior-Knowledge challenge [28] (classifying Ponderosa pine against all other cover types, with half of its 216 features injected distractors); accidents, a traffic-accident-severity set collected by the authors in Jordan [17] (major vs. minor injury; one-hot encoded); the clinical trio Pima (diabetes onset in Pima women [29]), thoracic (one-year post-operative mortality after lung resection [30]), and Framingham (ten-year coronary-heart-disease risk, the widely-circulated modelling extract of the Framingham Heart Study [31]); and fraud, the ULB European credit-card set [18] (PCA-anonymised features, extreme 578:1 imbalance, capped at 102:1 for tractability). Two near-balanced sets serve as ground-truth base populations for the hide-the-minority design of §3—spambase [32] and MAGIC gamma telescope [33]—because their large minority mass supports removing real minority to synthesise imbalance while retaining a held-out oracle. The two-horn separation sweep is anchored on the KEEL imbalanced benchmarks shuttle_c0_vs_c4 (separable) and page_blocks0 (overlapping) [24]. The high-dimensional caveat (main-text Scope section) uses a balanced d=589d=589 feature set (100 recordings, 50/50): the 589 acoustic features of Hassanat et al. [22] computed on the Spanish Parkinson’s-disease speech corpus of Orozco-Arroyave et al. [21]. Table S1: Datasets. n rows after cleaning; d features after any one-hot encoding; minority/majority counts; IR == majority//minority. Source column gives the dataset origin. dataset domain n d min/maj IR source sylva forest cover type 13,086 212 805/12,281 15.3 [28] accidents road-accident severity 12,669 104 1,856/10,813 5.8 [17] Framingham 10-yr CHD risk 3,658 15 557/3,101 5.6 [31]a Pima diabetes onset 768 8 268/500 1.9 [29] thoracic post-op mortality 470 22 70/400 5.7 [30] fraud (ULB) credit-card fraud 284,807 30 492/284,315 578 [18] spambaseb spam e-mail 4,601 57 1,813/2,788 1.5 [32] MAGICb gamma/hadron shower 19,020 10 6,688/12,332 1.8 [33] Parkinson (Spanish) PD speech (high-d) 100 589 50/50 1.0 [21, 22] shuttle_c0_vs_c4 sensor (horn anchor) 1,829 9 123/1,706 13.9 KEEL [24] page_blocks0 doc. layout (horn anchor) 5,472 10 559/4,913 8.8 KEEL [24] a No single canonical citation exists for the circulated modelling subset; we cite the study’s historical reference. Counts are complete-case: 582 of the 4,240 rows carry missing values and are dropped. b Near-balanced; used only as a ground-truth base population (§3), not in the natural-imbalance benchmark. Environments. Experiment CSVs used a pinned stack (Python 3.10; numpy 2.2.6, scikit-learn 1.7.2, scipy 1.15.3, imbalanced-learn 0.14.2, smote_variants 1.0.1). Figures regenerate unchanged under current libraries. Historical raw rows predate the deterministic-seeding fix and reproduce within split-std (±0.01± 0.01–0.050.05); the current harness is bit-reproducible. Excluded cells (cross-platform-verified). (a) Degenerate no-ops (no synthetic points; ER undefined). (b) Feature-space-transforming methods (E_SMOTE, ISOMAP-Hybrid) emit points in a reduced space, so an original-space vote is undefined by construction—excluded by design. (c) ROSE × sylva × LightGBM: native LightGBM crash on both Windows (4.6.0) and Linux (4.7.0), clean data—a library bug. (d) DEAGO, MOT2LD recovered via TensorFlow and a TSNE compatibility shim for the validity run (hence a numeric ERsplitER_split in the split table), but the shim did not carry into the benchmark pipeline, where the cell is x; likewise ISOMAP_Hybrid on Pima is deg for validity (empty synthetic set under the split) and lib at benchmark (reduced-space output). These codes track the processing stage, not a contradiction. Reproduction. repro_tables.py regenerates every table with pass/fail checks; make_all_figures.py regenerates every figure with a checkpoint report; reproduction_protocol.md maps each artifact to its command. All 1,040 ground-truth cells and 614 benchmark points are in the result CSVs. Appendix G Extended results tables All values below are computed from the released result CSVs by code/si_tables.py and match the summary figures in the main text. SMOTE-family methods only (deep generators are a separate track); “ok” counts exclude the deterministic no-ops and feature-space-transforming methods of §6. Table S2: Validity gap per dataset. Median ERnaiveER_naive vs median ERsplitER_split, and the number of methods each protocol certifies (invalidity <0.10<0.10). The de-biased test certifies almost none. dataset nokn_ok med. ERnaiveER_naive #cert. naive med. ERsplitER_split #cert. split med. gap sylva 78 0.000 65 0.216 1 +0.216 accidents 78 0.043 46 0.845 0 +0.801 Framingham 82 0.181 19 0.788 0 +0.607 Pima 80 0.147 30 0.493 0 +0.347 thoracic 79 0.221 14 0.826 0 +0.606 fraud 69 0.031 56 0.177 15 +0.146 Table S3: Real minority scores at the floor (identity baseline). Verbatim real minority points scored through the identical protocol (the “generator” is the identity map). ERnaiveER_naive(real)≈0≈ 0—each real point self-matches in the parent-retaining reference, so the classical test certifies real data as perfectly valid—yet ERsplitER_split(real) sits at the floor 1−V∞1-V_∞, matching the median generator’s ERsplitER_split (Table S2) within noise. The invalidity the de-biased test reports is therefore the overlap floor that real minority itself carries, not an artefact of fabrication. dataset ERnaiveER_naive(real) ERsplitER_split(real) == floor median generator ERsplitER_split sylva 0.00 0.251 0.216 accidents 0.00 0.836 0.845 Framingham 0.00 0.794 0.788 Pima 0.00 0.510 0.493 thoracic 0.00 0.789 0.826 fraud 0.00 0.176 0.177 Table S4: Finite-reference bias of ERsplitER_split (identity generator). Real minority scored against a withheld minority reference of decreasing size (majority reference fixed), on two ground-truth sets with different true floors. The 1-N estimate is biased upward when the withheld minority is sparse, and the inflation is larger for a lower true floor (spambase). It decays to ≤0.02≤ 0.02 once the reference reaches a few hundred points. Among our datasets only thoracic surgery (35-point reference) sits in the biased regime; all others withhold ≥134≥ 134 minority. dataset true floor bias @ 35 ref. bias @ 100 ref. unbiased by Pima 0.49 +0.28+0.28 +0.09+0.09 ∼ 134 spambase 0.12 +0.53+0.53 +0.32+0.32 ∼ 900 Table S5: Ground truth by imbalance ratio. Mean absolute error and correlation of each protocol against the held-out-minority oracle ERtruthER_truth, per (dataset, ratio) cell. The de-biased estimator tracks truth; the classical test underestimates it in 95–100% of these individual (dataset, ratio) cells (96–99% when pooled per dataset, as reported in the main text), worsening with the ratio. dataset IR cells MAE naive MAE split corr naive/split naive << truth spambase 2 78 0.172 0.025 0.90 / 0.98 97% spambase 5 78 0.216 0.049 0.86 / 0.81 96% spambase 10 77 0.299 0.043 0.79 / 0.90 97% spambase 20 76 0.404 0.071 0.73 / 0.81 95% spambase 40 74 0.513 0.073 0.61 / 0.81 95% MagicTelescope 2 73 0.486 0.033 0.35 / 0.95 100% MagicTelescope 5 79 0.279 0.041 0.45 / 0.90 99% MagicTelescope 10 79 0.316 0.041 0.53 / 0.89 99% MagicTelescope 20 79 0.355 0.040 0.47 / 0.91 100% Pima 2 78 0.684 0.034 0.31 / 0.47 97% Pima 5 81 0.503 0.037 0.43 / 0.79 96% fraud 150 65 0.116 0.029 0.84 / 0.97 95% fraud 300 64 0.127 0.026 0.87 / 0.98 97% fraud 450 59 0.159 0.057 0.64 / 0.73 97% Table S6: Information gain is classifier-independent. Best trivial baseline (F1), number of oversamplers beating it, the single best margin, and how many worsen calibration (ECE), per dataset and classifier. Denominators (75–93) count the methods returning a valid benchmark result in each cell—the SMOTE-family and deep generators, less per-cell no-ops and failures; the fraud column is smaller owing to the runtime omissions of §6. The best margins are noise-thin and largest only where the unresampled baseline degenerates (thoracic); on the largest real-world set (accidents), boosting yields zero methods above threshold-moving. dataset clf best baseline (F1) #beat best margin worsen ECE sylva LogReg class_weight (0.950) 15/93 +0.006 87/93 sylva XGBoost no_resample (0.953) 54/87 +0.014 71/87 sylva LightGBM no_resample (0.962) 17/86 +0.006 68/86 accidents LogReg threshold_move (0.317) 25/93 +0.009 83/93 accidents XGBoost threshold_move (0.321) 0/87 −-0.040 23/87 accidents LightGBM threshold_move (0.319) 0/87 −-0.026 17/87 Pima LogReg threshold_move (0.678) 25/88 +0.026 84/88 Pima XGBoost class_weight (0.654) 28/88 +0.040 83/88 Pima LightGBM class_weight (0.650) 40/88 +0.048 79/88 thoracic LogReg class_weight (0.239) 26/88 +0.107 79/88 thoracic XGBoost threshold_move (0.281) 8/87 +0.069 63/87 thoracic LightGBM threshold_move (0.319) 1/87 +0.049 67/87 Framingham LogReg threshold_move (0.422) 2/93 +0.004 90/93 Framingham XGBoost threshold_move (0.339) 2/87 +0.021 44/87 Framingham LightGBM threshold_move (0.327) 2/87 +0.006 22/87 fraud LogReg no_resample (0.877) 3/75 +0.005 71/75 fraud XGBoost no_resample (0.885) 3/75 +0.005 72/75 Table S7: No benchmark margin is statistically significant. For each dataset × classifier cell we take the method with the largest F1 margin over the best trivial baseline and report Δ 1, its percentile bootstrap 95% CI (2,000 test-set resamples), and how many of the top-eight methods have a Δ 1 CI excluding zero (“sig”). Across all 17 cells, none do—not one oversampler significantly beats the best trivial baseline; on two boosted accidents cells the best margin is significantly negative. Because Δ 1 is largest for the highest-F1 method, the top eight bracket the best margin exactly, so 0/80/8 significant implies 0/910/91. dataset clf best method Δ 1 95% CI sig Pima LogReg Gaussian_SMOTE +0.035+0.035 [−0.013,+0.079][-0.013,+0.079] 0/8 Pima XGBoost SVM_balance +0.024+0.024 [−0.050,+0.069][-0.050,+0.069] 0/8 Pima LightGBM AHC +0.047+0.047 [−0.012,+0.083][-0.012,+0.083] 0/8 thoracic LogReg ISMOTE +0.082+0.082 [−0.045,+0.194][-0.045,+0.194] 0/7 thoracic XGBoost AHC +0.032+0.032 [−0.179,+0.183][-0.179,+0.183] 0/8 thoracic LightGBM Lee +0.059+0.059 [−0.132,+0.239][-0.132,+0.239] 0/8 Framingham LogReg Safe_Level_SMOTE +0.001+0.001 [−0.017,+0.018][-0.017,+0.018] 0/8 Framingham XGBoost IPADE_ID +0.025+0.025 [−0.008,+0.060][-0.008,+0.060] 0/8 Framingham LightGBM SVM_balance +0.014+0.014 [−0.040,+0.064][-0.040,+0.064] 0/8 sylva LogReg Stefanowski +0.006+0.006 [−0.012,+0.018][-0.012,+0.018] 0/8 sylva XGBoost SUNDO +0.013+0.013 [−0.001,+0.020][-0.001,+0.020] 0/8 sylva LightGBM SMOTE_AMSR +0.006+0.006 [−0.007,+0.017][-0.007,+0.017] 0/8 accidents LogReg SMOTE_AMSR +0.013+0.013 [−0.001,+0.022][-0.001,+0.022] 0/8 accidents XGBoost MCT −0.033-0.033 [−0.061,−0.007][-0.061,-0.007] 0/8 accidents LightGBM SMOTE_FRST_2T −0.028-0.028 [−0.050,−0.004][-0.050,-0.004] 0/8 fraud LogReg DBSMOTE +0.004+0.004 [−0.007,+0.017][-0.007,+0.017] 0/8 fraud XGBoost SMOTE_ENN +0.000+0.000 [−0.004,+0.000][-0.004,+0.000] 0/8 Table S8: Method-side capstone (SMOTEFUNA), under its own Manhattan metric. ERnaive=0ER_naive=0 by construction (its acceptance rule is the classical check); the de-biased test finds a large share of its certified minority to be majority in truth. z-scored features, as in the original paper. dataset ERnaiveER_naive (own metric) ERsplitER_split (de-biased) hidden bias Pima 0.000 0.305 +0.305 thoracic 0.000 0.875 +0.875 Framingham 0.000 0.492 +0.492 Appendix H Full per-method tables (all 91 methods) Complete per-method values for every smote_variants oversampler, read directly from the released CSVs (code/si_full_tables.py). Column headers: sylva, accid(ents), Fram(ingham), Pima, thor(acic), fraud. Deep generative oversamplers are a separate track and are omitted here. Justification of non-numeric cells. Every blank cell has a documented, non-arbitrary cause, and no excluded cell is ever counted toward validity or information gain: deg No synthetic points under the stated protocol: the generator produced no synthetic minority points under the half-split, so validity is undefined on an empty synthetic set. Several such methods—cleaning-based hybrids like SMOTE_ENN, and SMOBD, SOMO, VIS_RST—do generate on the full data (hence a numeric ERnaiveER_naive and a benchmark F1) but empty under the split; deg thus means “undefined under this protocol,” not “adds nothing.” Where such a method runs at benchmark time its downstream effect is reported in the F1/Δ tables (e.g. SMOTE_ENN lowers accidents F1 by 0.2200.220). lib Feature-space-transforming (E_SMOTE, ISOMAP_Hybrid): these emit synthetic points in a reduced feature space (a genetic-algorithm mask, d:8→5d:8→5; an Isomap embedding, 8→38→3), so a validity vote in the original space is undefined by construction (§6). Excluded by design—the generators run without error on both operating systems; the instrument correctly refuses the dimensionality mismatch. x Run failure: a numerical or library error on that dataset (recorded verbatim in the CSV status column). -- Omitted for runtime: appears only in the fraud column (76/91 methods run; all 91 run on the other five datasets). The 15 absent methods are the optimization-based and backend-dependent generators—SMOTE_PSO, SMOTE_PSOBAT, AMSCO, ADG, GASMOTE, DSRBF, IPADE_ID, SMOTE_FRST_2T, SSO, NEATER, KernelADASYN, Supervised_SMOTE (each of which can take hours to days at the fraud set’s scale, n≈50,000n\!≈\!50,000), plus DEAGO and MOT2LD (which require an optional TensorFlow / TSNE backend). They are omitted from the extreme-scale run for tractability and reported as omitted, never as valid; the other five datasets audit the full family. The one benchmark cell that crashes irreducibly (ROSE × sylva × LightGBM, a native LightGBM fault on both Windows and Linux; §6) is footnoted rather than tabulated. Table S9: De-biased invalidity ERsplitER_split per method. The headline table: no method achieves low ERsplitER_split on the overlapping sets. Read against Table S2 (per-dataset medians). method sylva accid Fram Pima thor fraud ADASYN 0.272 0.845 0.815 0.531 0.845 0.412 ADG 0.173 0.860 0.783 0.521 0.885 – ADOMS 0.244 0.830 0.800 0.460 0.836 0.204 AHC 0.989 0.879 0.872 0.744 0.876 0.998 AMSCO 0.219 0.853 0.804 0.485 0.846 – AND_SMOTE 0.201 0.824 0.779 0.409 0.778 0.039 ANS 0.206 0.848 0.800 0.541 0.762 0.078 ASMOBD deg deg 0.742 0.574 0.765 0.018 A_SUWO 0.257 0.822 0.761 0.477 0.822 0.461 Assembled_SMOTE 0.196 0.837 0.795 0.490 0.824 0.177 Borderline_SMOTE1 0.249 0.839 0.766 0.493 0.844 0.160 Borderline_SMOTE2 0.413 0.840 0.758 0.566 0.804 0.343 CBSO 0.222 0.841 0.810 0.502 0.793 0.333 CCR 0.360 0.831 0.778 0.504 0.833 0.195 CE_SMOTE 0.211 0.834 0.806 0.462 0.827 0.220 CURE_SMOTE 0.115 0.893 0.781 0.476 0.766 0.034 DBSMOTE 0.234 0.816 0.757 0.607 0.685 0.000 DEAGO 0.229 0.914 0.788 0.497 0.670 – DE_oversampling 0.258 0.836 0.788 0.487 0.812 0.239 DSMOTE 0.138 0.846 0.711 0.224 0.830 0.686 DSRBF 0.182 0.834 0.786 0.507 0.788 – E_SMOTE lib lib lib lib lib – Edge_Det_SMOTE 0.191 0.845 0.800 0.488 0.811 0.115 GASMOTE 0.211 0.840 0.820 0.475 0.826 – G_SMOTE 0.205 0.836 0.787 0.503 0.812 0.207 Gaussian_SMOTE 0.666 0.837 0.747 0.498 0.892 0.251 Gazzah 0.140 0.876 0.857 deg 0.763 0.164 IPADE_ID deg deg deg deg deg – ISMOTE deg deg deg deg deg deg ISOMAP_Hybrid lib lib lib deg lib lib KernelADASYN 0.600 0.851 0.800 0.600 0.844 – LLE_SMOTE 0.116 0.883 0.785 0.409 0.729 0.121 LN_SMOTE 0.176 0.823 0.755 0.421 0.821 0.063 LVQ_SMOTE 0.194 0.850 0.715 0.474 0.836 0.310 Lee 0.189 0.826 0.766 0.457 0.856 0.060 MCT 0.248 0.840 0.779 0.522 0.828 0.190 MDO 0.849 0.789 0.596 0.350 0.875 0.445 MOT2LD 0.173 0.824 0.743 0.407 0.885 – MSMOTE 0.371 0.837 0.766 0.502 0.819 0.097 MSYN 0.115 0.816 0.758 0.424 0.803 x MWMOTE 0.203 0.857 0.823 0.528 0.826 0.319 NDO_sampling 0.258 0.845 0.796 0.471 0.790 0.138 NEATER 0.216 0.856 0.791 0.488 0.830 – NRAS 0.195 0.785 0.728 0.417 0.882 0.051 NRSBoundary_SMOTE 0.222 0.845 0.793 0.471 0.790 0.177 NT_SMOTE 0.210 0.862 0.811 0.491 0.754 0.158 OUPS 0.218 0.854 0.784 0.559 0.810 0.304 PDFOS 0.635 0.831 0.730 0.476 0.845 0.447 ProWSyn 0.147 0.788 0.755 0.536 0.840 0.224 ROSE 0.267 0.829 0.776 0.510 0.855 0.356 RWO_sampling 0.237 0.836 0.814 0.515 0.819 0.198 Random_SMOTE 0.209 0.849 0.797 0.405 0.836 0.189 SDSMOTE 0.216 0.829 0.795 0.478 0.840 0.176 SL_graph_SMOTE 0.284 0.834 0.772 0.505 0.839 0.136 SMMO deg 0.928 0.843 0.641 deg 0.799 SMOBD deg deg deg deg deg deg SMOTE 0.215 0.841 0.790 0.472 0.795 0.183 SMOTEWB 0.248 0.820 0.791 0.505 0.771 0.167 SMOTE_AMSR 0.207 0.858 0.803 0.559 0.795 0.291 SMOTE_Cosine 0.200 0.842 0.804 0.555 0.830 0.173 SMOTE_D 0.225 0.837 0.776 0.440 0.849 0.293 SMOTE_ENN deg deg deg deg deg deg SMOTE_FRST_2T 0.229 0.846 0.787 0.494 0.786 – SMOTE_IPF 0.214 0.846 0.807 0.421 0.835 0.186 SMOTE_OUT 0.211 0.846 0.802 0.462 0.852 0.155 SMOTE_PSO 0.325 0.850 0.796 0.497 0.849 – SMOTE_PSOBAT 0.241 0.846 0.795 0.545 0.790 – SMOTE_RSB deg deg 0.630 0.240 0.813 0.011 SMOTE_TomekLinks 0.214 0.848 0.797 0.501 0.843 0.167 SN_SMOTE 0.221 0.854 0.767 0.397 0.795 0.157 SOI_CJ 0.243 0.826 0.743 0.534 deg 0.052 SOMO deg deg deg deg deg 0.011 SPY deg deg deg deg deg deg SSO 0.875 0.813 0.586 0.471 0.857 – SUNDO 0.986 0.869 0.856 deg 0.857 0.999 SVM_balance 0.202 0.854 0.803 0.526 0.815 0.188 SYMPROD deg deg 0.699 0.398 deg 0.041 Safe_Level_SMOTE 0.297 0.866 0.793 0.490 0.812 0.146 Selected_SMOTE 0.202 0.849 0.804 0.514 0.832 0.195 Stefanowski 0.328 0.836 0.805 0.666 0.860 0.575 Supervised_SMOTE 0.191 0.834 0.718 0.493 0.773 – TRIM_SMOTE 0.218 0.842 0.870 0.453 0.812 0.095 VIS_RST 0.283 deg deg deg deg 0.107 V_SYNTH 0.997 0.847 0.752 0.600 0.888 deg cluster_SMOTE 0.210 0.847 0.770 0.450 0.850 0.248 distance_SMOTE 0.174 0.860 0.789 0.460 0.811 0.159 kmeans_SMOTE deg deg 0.595 0.393 deg deg polynom_fit_SMOTE_bus 0.194 0.855 0.791 0.531 0.864 0.165 polynom_fit_SMOTE_mesh 0.193 0.861 0.799 0.526 0.832 0.173 polynom_fit_SMOTE_poly 0.044 0.919 0.838 0.688 0.830 0.012 polynom_fit_SMOTE_star 0.115 0.887 0.811 0.715 0.723 0.145 Codes: deg no-op (empty synthetic set), lib feature-space-transforming (vote undefined), x run failure, -- omitted for runtime (fraud only, 15 slow/backend methods; see justification above). No excluded cell counts toward validity or gain. Table S10: Classical invalidity ERnaiveER_naive per method. The same points scored against the parent-retaining reference; compare cell-by-cell with Table LABEL:tab:full_split to see the leakage bias (Lemma 0L). method sylva accid Fram Pima thor fraud ADASYN 0.000 0.014 0.181 0.151 0.194 0.107 ADG 0.159 0.822 0.774 0.498 0.658 – ADOMS 0.016 0.047 0.200 0.164 0.221 0.034 AHC 1.000 1.000 1.000 1.000 1.000 1.000 AMSCO 0.000 0.013 0.209 0.139 0.232 – AND_SMOTE 0.000 0.002 0.094 0.103 0.103 0.002 ANS 0.000 0.149 0.415 0.375 0.242 0.025 ASMOBD deg deg 0.052 0.099 0.297 0.000 A_SUWO 0.000 0.001 0.014 0.005 0.000 0.000 Assembled_SMOTE 0.000 0.011 0.147 0.086 0.139 0.047 Borderline_SMOTE1 0.000 0.006 0.181 0.185 0.142 0.010 Borderline_SMOTE2 0.005 0.001 0.067 0.060 0.045 0.014 CBSO 0.003 0.107 0.406 0.190 0.288 0.111 CCR 0.000 0.094 0.021 0.007 0.304 0.009 CE_SMOTE 0.000 0.004 0.153 0.082 0.158 0.068 CURE_SMOTE 0.002 0.402 0.226 0.233 0.482 0.014 DBSMOTE 0.000 0.009 0.000 0.000 0.124 0.000 DEAGO 0.196 0.896 0.850 0.591 0.751 – DE_oversampling 0.008 0.028 0.104 0.065 0.089 0.000 DSMOTE 0.051 0.859 0.824 0.190 0.918 0.656 DSRBF 0.001 0.092 0.120 0.069 0.221 – E_SMOTE lib lib lib lib lib – Edge_Det_SMOTE 0.000 0.013 0.158 0.125 0.194 0.018 GASMOTE 0.000 0.005 0.158 0.105 0.148 – G_SMOTE 0.000 0.005 0.101 0.099 0.154 0.048 Gaussian_SMOTE 0.444 0.477 0.682 0.496 0.700 0.138 Gazzah 0.003 0.425 0.535 deg 0.535 0.015 IPADE_ID deg deg deg deg deg – ISMOTE deg deg deg deg deg deg ISOMAP_Hybrid lib lib lib deg lib lib KernelADASYN 0.000 0.812 0.000 1.000 0.733 – LLE_SMOTE 0.061 0.622 0.714 0.353 0.694 0.089 LN_SMOTE 0.012 0.040 0.076 0.099 0.030 0.002 LVQ_SMOTE 0.001 0.251 0.516 0.397 0.482 0.148 Lee 0.000 0.003 0.122 0.060 0.209 0.001 MCT 0.000 0.000 0.000 0.000 0.000 0.000 MDO 0.852 0.768 0.524 0.349 0.321 0.441 MOT2LD 0.000 0.049 0.311 0.206 0.221 – MSMOTE 0.180 0.359 0.372 0.259 0.370 0.011 MSYN 0.000 0.002 0.072 0.066 0.052 x MWMOTE 0.000 0.126 0.419 0.280 0.191 0.116 NDO_sampling 0.004 0.001 0.069 0.060 0.049 0.005 NEATER 0.000 0.014 0.182 0.136 0.171 – NRAS 0.040 0.208 0.167 0.160 0.248 0.011 NRSBoundary_SMOTE 0.000 0.007 0.130 0.116 0.136 0.041 NT_SMOTE 0.000 0.050 0.252 0.198 0.315 0.065 OUPS 0.094 0.504 0.610 0.552 0.567 0.172 PDFOS 0.588 0.739 0.651 0.379 0.709 0.393 ProWSyn 0.002 0.173 0.417 0.289 0.303 0.087 ROSE 0.084 0.274 0.573 0.478 0.509 0.276 RWO_sampling 0.000 0.002 0.000 0.142 0.154 0.001 Random_SMOTE 0.000 0.247 0.306 0.228 0.442 0.065 SDSMOTE 0.000 0.008 0.163 0.082 0.197 0.036 SL_graph_SMOTE 0.127 0.012 0.153 0.362 0.142 0.059 SMMO deg 0.355 0.238 0.198 deg 0.289 SMOBD deg deg deg deg deg 0.028 SMOTE 0.000 0.009 0.155 0.082 0.197 0.036 SMOTEWB 0.000 0.001 0.018 0.022 0.000 0.000 SMOTE_AMSR 0.002 0.487 0.675 0.422 0.430 0.090 SMOTE_Cosine 0.000 0.096 0.367 0.353 0.188 0.026 SMOTE_D 0.000 0.005 0.162 0.114 0.167 0.002 SMOTE_ENN deg deg deg deg deg deg SMOTE_FRST_2T 0.000 0.034 0.153 0.054 0.225 – SMOTE_IPF 0.000 0.009 0.183 0.082 0.197 0.031 SMOTE_OUT 0.001 0.006 0.101 0.052 0.167 0.011 SMOTE_PSO 0.373 0.034 0.005 0.038 0.022 – SMOTE_PSOBAT 0.000 0.005 0.000 0.043 0.000 – SMOTE_RSB deg deg 0.296 0.000 0.083 0.000 SMOTE_TomekLinks 0.000 0.012 0.162 0.131 0.190 0.043 SN_SMOTE 0.000 0.003 0.127 0.090 0.127 0.036 SOI_CJ 0.060 0.010 0.128 0.129 deg 0.028 SOMO deg deg deg deg deg 0.000 SPY deg deg deg deg deg deg SSO 0.877 0.004 0.569 0.361 0.270 – SUNDO 1.000 1.000 1.000 deg 1.000 0.998 SVM_balance 0.000 0.010 0.179 0.095 0.167 0.043 SYMPROD deg deg 0.025 0.362 deg 0.000 Safe_Level_SMOTE 0.135 0.635 0.577 0.332 0.648 0.072 Selected_SMOTE 0.000 0.231 0.214 0.004 0.345 0.000 Stefanowski 0.000 0.000 0.000 0.000 0.000 0.000 Supervised_SMOTE 0.001 0.052 0.099 0.336 0.027 – TRIM_SMOTE 0.000 0.008 0.434 0.082 0.185 0.012 VIS_RST 0.064 deg deg deg deg 0.031 V_SYNTH 1.000 0.843 0.764 0.625 0.858 deg cluster_SMOTE 0.000 0.005 0.116 0.095 0.088 0.074 distance_SMOTE 0.001 0.100 0.238 0.155 0.291 0.054 kmeans_SMOTE deg deg 0.043 0.151 0.439 deg polynom_fit_SMOTE_bus 0.000 0.186 0.435 0.509 0.275 0.051 polynom_fit_SMOTE_mesh 0.004 0.370 0.636 0.448 0.430 0.085 polynom_fit_SMOTE_poly 0.028 0.926 0.824 0.763 0.782 0.000 polynom_fit_SMOTE_star 0.005 0.387 0.579 0.720 0.523 0.008 Codes: deg no-op (empty synthetic set), lib feature-space-transforming (vote undefined), x run failure, -- omitted for runtime (fraud only, 15 slow/backend methods; see justification above). No excluded cell counts toward validity or gain. Table S11: Honest-protocol test F1 per method (logistic regression). Every method’s F1 under the split-then-resample protocol; compare against the trivial-baseline F1 values in Table S6, or read the per-method deltas directly in Table LABEL:tab:full_df1. method sylva accid Fram Pima thor fraud ADASYN 0.946 0.310 0.399 0.670 0.242 0.152 ADG 0.946 0.313 0.105 0.685 0.157 – ADOMS 0.952 0.316 0.410 0.667 0.233 0.422 AHC 0.942 0.216 0.241 0.674 0.143 0.856 AMSCO 0.950 0.263 0.392 0.704 0.243 – AND_SMOTE 0.946 0.319 0.417 0.674 0.138 0.724 ANS 0.945 0.315 0.370 0.659 0.143 0.721 ASMOBD 0.946 0.197 0.281 0.674 0.129 0.882 A_SUWO 0.938 0.319 0.406 0.674 0.145 0.820 Assembled_SMOTE 0.947 0.316 0.405 0.663 0.254 0.418 Borderline_SMOTE1 0.935 0.317 0.406 0.663 0.182 0.688 Borderline_SMOTE2 0.908 0.326 0.398 0.698 0.167 0.626 CBSO 0.948 0.317 0.392 0.700 0.246 0.179 CCR 0.941 0.318 0.396 0.692 0.257 0.424 CE_SMOTE 0.952 0.317 0.412 0.663 0.226 0.428 CURE_SMOTE 0.947 0.317 0.307 0.630 0.214 0.869 DBSMOTE 0.950 0.229 0.324 0.654 0.127 0.882 DEAGO 0.940 0.124 0.388 0.691 0.346 – DE_oversampling 0.943 0.321 0.401 0.697 0.279 0.415 DSMOTE 0.901 0.108 0.317 0.623 0.145 0.738 DSRBF 0.948 0.315 0.401 0.682 0.226 – E_SMOTE lib lib lib lib lib – Edge_Det_SMOTE 0.946 0.313 0.421 0.682 0.215 0.556 GASMOTE 0.947 0.304 0.408 0.682 0.145 – G_SMOTE 0.949 0.323 0.403 0.659 0.230 0.425 Gaussian_SMOTE 0.899 0.308 0.406 0.696 0.176 0.468 Gazzah 0.871 0.085 0.381 0.681 0.301 0.548 IPADE_ID 0.849 0.180 0.355 0.674 0.164 – ISMOTE 0.819 0.284 0.405 0.684 0.317 0.163 ISOMAP_Hybrid lib lib lib lib lib lib KernelADASYN 0.930 0.108 0.394 0.688 0.314 – LLE_SMOTE 0.942 0.327 0.422 0.671 0.281 0.374 LN_SMOTE 0.948 0.321 0.416 0.674 0.148 0.738 LVQ_SMOTE 0.938 0.178 0.400 0.667 0.197 0.454 Lee 0.951 0.309 0.404 0.674 0.122 0.732 MCT 0.954 0.321 0.401 0.670 0.179 0.434 MDO 0.898 0.286 0.388 0.639 0.038 0.164 MOT2LD x x x x x – MSMOTE 0.896 0.319 0.407 0.670 0.140 0.722 MSYN 0.951 0.309 0.411 0.663 0.250 0.865 MWMOTE 0.947 0.314 0.383 0.663 0.265 0.167 NDO_sampling 0.912 0.315 0.411 0.663 0.188 0.505 NEATER 0.922 0.288 0.370 0.670 0.267 – NRAS 0.884 0.241 0.396 0.627 0.074 0.816 NRSBoundary_SMOTE 0.947 0.321 0.412 0.663 0.191 0.197 NT_SMOTE 0.943 0.312 0.405 0.674 0.167 0.408 OUPS 0.944 0.316 0.415 0.670 0.254 0.420 PDFOS 0.945 0.318 0.401 0.663 0.269 0.161 ProWSyn 0.947 0.324 0.410 0.674 0.218 0.435 ROSE 0.935 0.318 0.404 0.655 0.246 0.487 RWO_sampling 0.952 0.313 0.403 0.674 0.233 0.439 Random_SMOTE 0.954 0.315 0.401 0.670 0.188 0.436 SDSMOTE 0.952 0.316 0.404 0.689 0.226 0.423 SL_graph_SMOTE 0.908 0.317 0.406 0.663 0.121 0.547 SMMO 0.946 0.097 0.358 0.673 0.000 0.130 SMOBD 0.946 0.097 0.058 0.629 0.000 0.877 SMOTE 0.952 0.313 0.404 0.689 0.219 0.423 SMOTEWB 0.950 0.324 0.413 0.674 0.254 0.437 SMOTE_AMSR 0.950 0.324 0.403 0.685 0.194 0.624 SMOTE_Cosine 0.952 0.322 0.413 0.670 0.267 0.643 SMOTE_D 0.947 0.306 0.425 0.682 0.230 0.606 SMOTE_ENN 0.946 0.097 0.058 0.629 0.000 0.877 SMOTE_FRST_2T 0.950 0.301 0.396 0.659 0.145 – SMOTE_IPF 0.948 0.319 0.404 0.663 0.226 0.423 SMOTE_OUT 0.947 0.316 0.406 0.667 0.230 0.422 SMOTE_PSO 0.954 0.261 0.310 0.685 0.278 – SMOTE_PSOBAT 0.946 0.146 0.406 0.667 0.225 – SMOTE_RSB 0.950 0.097 0.080 0.615 0.000 0.874 SMOTE_TomekLinks 0.948 0.312 0.414 0.701 0.197 0.423 SN_SMOTE 0.947 0.324 0.405 0.659 0.254 0.412 SOI_CJ 0.954 0.205 0.294 0.628 0.000 0.878 SOMO 0.942 0.103 0.252 0.671 0.121 0.857 SPY 0.884 0.135 0.154 0.692 0.062 0.857 SSO 0.937 0.309 0.394 0.638 0.191 – SUNDO 0.941 0.281 0.421 0.623 0.219 0.632 SVM_balance 0.950 0.314 0.389 0.702 0.244 0.401 SYMPROD 0.946 0.097 0.294 0.658 0.046 0.875 Safe_Level_SMOTE 0.931 0.321 0.418 0.674 0.226 0.547 Selected_SMOTE 0.944 0.317 0.398 0.670 0.219 0.438 Stefanowski 0.956 0.277 0.348 0.670 0.269 0.839 Supervised_SMOTE 0.951 0.317 0.407 0.682 0.291 – TRIM_SMOTE 0.941 0.318 0.232 0.674 0.164 0.508 VIS_RST 0.835 0.097 0.058 0.629 0.000 0.455 V_SYNTH 0.674 0.317 0.403 0.652 0.308 0.335 cluster_SMOTE 0.944 0.315 0.419 0.663 0.231 0.562 distance_SMOTE 0.943 0.320 0.407 0.659 0.203 0.420 kmeans_SMOTE 0.945 0.097 0.131 0.640 0.121 0.875 polynom_fit_SMOTE_bus 0.946 0.318 0.405 0.678 0.230 0.645 polynom_fit_SMOTE_mesh 0.947 0.316 0.412 0.674 0.200 0.630 polynom_fit_SMOTE_poly 0.939 0.316 0.417 0.690 0.218 0.866 polynom_fit_SMOTE_star 0.941 0.285 0.406 0.682 0.258 0.834 Codes: deg no-op (empty synthetic set), lib feature-space-transforming (vote undefined), x run failure, -- omitted for runtime (fraud only, 15 slow/backend methods; see justification above). No excluded cell counts toward validity or gain. Table S12: Δ 1 per method vs. the best trivial baseline (logistic regression). The delta a reader would otherwise compute from Table LABEL:tab:full_f1 and the baselines of Table S6: method F1 minus the best of no-resample, class-weight and threshold-move on that dataset. Positive == improvement; the median is below 0.010.01 and the only sizeable entries fall on thoracic surgery, where the unresampled baseline collapses. method sylva accid Fram Pima thor fraud ADASYN -0.004 -0.007 -0.023 -0.008 +0.004 -0.725 ADG -0.004 -0.004 -0.317 +0.007 -0.082 – ADOMS +0.002 -0.001 -0.012 -0.012 -0.006 -0.455 AHC -0.008 -0.101 -0.181 -0.004 -0.096 -0.021 AMSCO 0.000 -0.054 -0.030 +0.026 +0.004 – AND_SMOTE -0.004 +0.002 -0.005 -0.004 -0.101 -0.153 ANS -0.005 -0.002 -0.052 -0.019 -0.096 -0.156 ASMOBD -0.004 -0.120 -0.141 -0.004 -0.110 +0.005 A_SUWO -0.012 +0.002 -0.016 -0.004 -0.093 -0.057 Assembled_SMOTE -0.002 -0.001 -0.017 -0.015 +0.015 -0.459 Borderline_SMOTE1 -0.014 -0.001 -0.015 -0.015 -0.057 -0.189 Borderline_SMOTE2 -0.041 +0.009 -0.024 +0.020 -0.072 -0.251 CBSO -0.002 0.000 -0.029 +0.021 +0.007 -0.698 CCR -0.009 +0.001 -0.025 +0.014 +0.018 -0.453 CE_SMOTE +0.002 0.000 -0.010 -0.015 -0.013 -0.449 CURE_SMOTE -0.003 -0.001 -0.115 -0.048 -0.025 -0.008 DBSMOTE 0.000 -0.088 -0.097 -0.024 -0.112 +0.005 DEAGO -0.010 -0.193 -0.034 +0.012 +0.107 – DE_oversampling -0.007 +0.004 -0.020 +0.018 +0.040 -0.462 DSMOTE -0.049 -0.209 -0.105 -0.056 -0.093 -0.139 DSRBF -0.002 -0.002 -0.021 +0.004 -0.013 – E_SMOTE lib lib lib lib lib – Edge_Det_SMOTE -0.004 -0.004 -0.001 +0.004 -0.023 -0.321 GASMOTE -0.003 -0.013 -0.014 +0.004 -0.093 – G_SMOTE -0.001 +0.005 -0.019 -0.019 -0.009 -0.451 Gaussian_SMOTE -0.051 -0.009 -0.016 +0.018 -0.062 -0.409 Gazzah -0.079 -0.232 -0.041 +0.003 +0.063 -0.329 IPADE_ID -0.101 -0.137 -0.067 -0.004 -0.075 – ISMOTE -0.131 -0.033 -0.016 +0.006 +0.078 -0.713 ISOMAP_Hybrid lib lib lib lib lib lib KernelADASYN -0.020 -0.209 -0.028 +0.009 +0.076 – LLE_SMOTE -0.007 +0.009 +0.001 -0.008 +0.042 -0.503 LN_SMOTE -0.002 +0.004 -0.006 -0.004 -0.091 -0.138 LVQ_SMOTE -0.012 -0.139 -0.022 -0.012 -0.042 -0.423 Lee +0.001 -0.008 -0.017 -0.004 -0.116 -0.145 MCT +0.004 +0.004 -0.020 -0.008 -0.060 -0.443 MDO -0.052 -0.031 -0.033 -0.039 -0.200 -0.713 MOT2LD x x x x x – MSMOTE -0.054 +0.002 -0.015 -0.008 -0.098 -0.155 MSYN +0.001 -0.008 -0.010 -0.015 +0.011 -0.012 MWMOTE -0.002 -0.003 -0.039 -0.015 +0.026 -0.710 NDO_sampling -0.037 -0.002 -0.010 -0.015 -0.051 -0.372 NEATER -0.028 -0.029 -0.052 -0.008 +0.028 – NRAS -0.066 -0.076 -0.026 -0.051 -0.165 -0.061 NRSBoundary_SMOTE -0.002 +0.004 -0.010 -0.015 -0.048 -0.679 NT_SMOTE -0.007 -0.005 -0.016 -0.004 -0.072 -0.468 OUPS -0.006 -0.001 -0.006 -0.008 +0.015 -0.457 PDFOS -0.005 +0.001 -0.021 -0.015 +0.030 -0.716 ProWSyn -0.002 +0.007 -0.011 -0.004 -0.021 -0.441 ROSE -0.015 +0.001 -0.017 -0.023 +0.007 -0.390 RWO_sampling +0.002 -0.004 -0.019 -0.004 -0.006 -0.438 Random_SMOTE +0.004 -0.002 -0.021 -0.008 -0.051 -0.441 SDSMOTE +0.002 -0.002 -0.017 +0.011 -0.013 -0.454 SL_graph_SMOTE -0.041 -0.001 -0.015 -0.015 -0.118 -0.330 SMMO -0.004 -0.220 -0.064 -0.005 -0.239 -0.747 SMOBD -0.004 -0.220 -0.364 -0.049 -0.239 0.000 SMOTE +0.002 -0.004 -0.017 +0.011 -0.020 -0.454 SMOTEWB 0.000 +0.007 -0.009 -0.004 +0.015 -0.440 SMOTE_AMSR 0.000 +0.006 -0.018 +0.007 -0.045 -0.252 SMOTE_Cosine +0.002 +0.005 -0.008 -0.008 +0.028 -0.233 SMOTE_D -0.003 -0.011 +0.004 +0.004 -0.009 -0.271 SMOTE_ENN -0.004 -0.220 -0.364 -0.049 -0.239 0.000 SMOTE_FRST_2T 0.000 -0.016 -0.026 -0.019 -0.094 – SMOTE_IPF -0.002 +0.002 -0.017 -0.015 -0.013 -0.454 SMOTE_OUT -0.003 -0.001 -0.016 -0.012 -0.009 -0.455 SMOTE_PSO +0.004 -0.056 -0.111 +0.007 +0.039 – SMOTE_PSOBAT -0.004 -0.171 -0.016 -0.012 -0.014 – SMOTE_RSB +0.001 -0.220 -0.342 -0.063 -0.239 -0.003 SMOTE_TomekLinks -0.002 -0.005 -0.008 +0.023 -0.042 -0.454 SN_SMOTE -0.002 +0.007 -0.017 -0.019 +0.015 -0.465 SOI_CJ +0.004 -0.112 -0.128 -0.050 -0.239 +0.001 SOMO -0.007 -0.214 -0.170 -0.008 -0.118 -0.020 SPY -0.066 -0.182 -0.268 +0.014 -0.176 -0.020 SSO -0.013 -0.008 -0.028 -0.040 -0.048 – SUNDO -0.009 -0.036 0.000 -0.055 -0.020 -0.244 SVM_balance 0.000 -0.004 -0.033 +0.024 +0.005 -0.476 SYMPROD -0.004 -0.220 -0.128 -0.020 -0.192 -0.002 Safe_Level_SMOTE -0.018 +0.004 -0.003 -0.004 -0.013 -0.330 Selected_SMOTE -0.005 0.000 -0.024 -0.008 -0.020 -0.439 Stefanowski +0.006 -0.041 -0.073 -0.008 +0.030 -0.038 Supervised_SMOTE +0.001 0.000 -0.014 +0.004 +0.052 – TRIM_SMOTE -0.009 +0.001 -0.190 -0.004 -0.075 -0.369 VIS_RST -0.115 -0.220 -0.364 -0.049 -0.239 -0.422 V_SYNTH -0.276 0.000 -0.019 -0.026 +0.069 -0.542 cluster_SMOTE -0.006 -0.002 -0.002 -0.015 -0.008 -0.315 distance_SMOTE -0.007 +0.003 -0.014 -0.019 -0.035 -0.457 kmeans_SMOTE -0.005 -0.220 -0.291 -0.038 -0.118 -0.002 polynom_fit_SMOTE_bus -0.004 +0.001 -0.017 0.000 -0.009 -0.232 polynom_fit_SMOTE_mesh -0.002 -0.002 -0.010 -0.004 -0.039 -0.246 polynom_fit_SMOTE_poly -0.011 -0.001 -0.005 +0.012 -0.021 -0.011 polynom_fit_SMOTE_star -0.009 -0.032 -0.015 +0.004 +0.019 -0.042 Codes: deg no-op, lib feature-space-transforming, x run failure, -- omitted for runtime (fraud only). Δ is the method’s F1 minus the best trivial baseline’s on that dataset. Per-method ranking metrics (the threshold-shift claim, made auditable). Tables LABEL:tab:full_dauprc–LABEL:tab:full_dauroc report each method’s change in PR-AUC and ROC-AUC relative to the best trivial baseline, under logistic regression—the ranking counterpart to the F1 table above, and the check a reviewer needs to test the operating-point-shift claim cell by cell. Across the 515 evaluated method–dataset cells the median Δ -AUC is −0.005-0.005 and the median Δ -AUC −0.003-0.003; only 11 and 6 cells respectively exceed +0.02+0.02, and those concentrate on thoracic surgery—the one set where the unresampled baseline degenerates. Where a method raises F1 (Table LABEL:tab:full_f1) its ranking almost never follows: the signature of a moved threshold, not new information. A method that genuinely learned more would show a reproducible positive Δ here; none does. Table S13: Δ -AUC per method vs. the best trivial baseline (logistic regression). Positive == ranking improvement over the best of no-resample, class-weight and threshold-move on that dataset; near-universally ≤0≤ 0. Read against the F1 gains of Table LABEL:tab:full_f1—F1 rises where PR-AUC does not. method sylva accid Fram Pima thor fraud ADASYN -0.004 -0.010 -0.023 0.000 -0.012 -0.027 ADG -0.003 -0.016 -0.176 -0.010 -0.017 – ADOMS +0.001 -0.007 -0.017 -0.009 -0.023 -0.018 AHC -0.003 +0.001 -0.005 -0.002 -0.011 -0.002 AMSCO -0.001 -0.013 -0.040 +0.002 -0.026 – AND_SMOTE -0.001 -0.006 -0.025 -0.003 -0.033 -0.014 ANS -0.002 +0.001 -0.063 -0.008 -0.048 +0.001 ASMOBD -0.003 -0.095 -0.131 +0.009 -0.043 0.000 A_SUWO -0.008 -0.007 -0.023 -0.001 -0.042 -0.032 Assembled_SMOTE -0.001 -0.006 -0.032 +0.003 -0.015 0.000 Borderline_SMOTE1 -0.005 -0.006 -0.035 -0.008 -0.046 -0.029 Borderline_SMOTE2 -0.012 -0.005 -0.034 +0.004 -0.043 -0.022 CBSO -0.005 -0.005 -0.008 0.000 +0.006 -0.018 CCR +0.001 -0.004 -0.007 -0.004 -0.006 -0.012 CE_SMOTE -0.002 -0.007 -0.028 +0.002 -0.025 -0.001 CURE_SMOTE -0.004 -0.006 -0.015 +0.002 -0.025 +0.003 DBSMOTE -0.001 -0.089 -0.107 -0.029 -0.045 +0.001 DEAGO -0.008 0.000 -0.008 +0.005 +0.049 – DE_oversampling +0.001 -0.008 -0.003 +0.008 +0.015 -0.038 DSMOTE -0.012 -0.006 -0.054 -0.015 -0.037 -0.020 DSRBF -0.003 -0.013 -0.017 -0.004 -0.013 – E_SMOTE lib lib lib lib lib – Edge_Det_SMOTE -0.002 -0.012 -0.024 +0.002 -0.016 -0.002 GASMOTE -0.003 -0.013 -0.010 -0.012 -0.036 – G_SMOTE -0.003 -0.006 -0.010 -0.004 -0.021 -0.001 Gaussian_SMOTE +0.006 -0.019 -0.005 +0.011 -0.032 -0.014 Gazzah -0.051 -0.072 -0.046 -0.038 +0.035 -0.061 IPADE_ID -0.049 -0.037 -0.068 -0.003 -0.043 – ISMOTE -0.058 -0.052 -0.013 -0.003 +0.055 -0.432 ISOMAP_Hybrid lib lib lib lib lib lib KernelADASYN -0.005 -0.063 -0.033 -0.011 +0.009 – LLE_SMOTE -0.004 -0.020 +0.015 +0.005 +0.009 -0.013 LN_SMOTE -0.001 -0.005 -0.020 0.000 -0.036 -0.010 LVQ_SMOTE -0.008 -0.064 -0.008 -0.006 -0.026 -0.080 Lee -0.001 -0.018 -0.021 +0.001 -0.034 -0.010 MCT -0.001 +0.001 +0.005 -0.001 -0.024 -0.001 MDO -0.023 -0.048 -0.057 +0.005 -0.063 -0.309 MOT2LD x x x x x – MSMOTE -0.026 -0.004 -0.021 +0.009 -0.026 -0.012 MSYN -0.003 -0.011 +0.027 -0.004 -0.020 +0.006 MWMOTE -0.003 -0.002 -0.047 -0.001 -0.027 -0.018 NDO_sampling -0.008 -0.011 -0.036 -0.010 -0.007 -0.005 NEATER -0.051 -0.012 -0.032 -0.003 -0.021 – NRAS -0.015 -0.073 -0.031 +0.004 -0.035 -0.007 NRSBoundary_SMOTE -0.006 -0.009 -0.021 -0.003 -0.027 -0.028 NT_SMOTE -0.003 -0.018 -0.025 +0.001 -0.038 +0.001 OUPS -0.003 -0.002 -0.008 +0.003 -0.001 -0.001 PDFOS -0.003 -0.023 -0.033 +0.006 -0.014 -0.380 ProWSyn -0.004 +0.002 +0.015 -0.005 -0.013 0.000 ROSE +0.001 -0.012 -0.017 -0.011 -0.014 -0.024 RWO_sampling 0.000 -0.005 +0.005 -0.001 -0.010 -0.003 Random_SMOTE +0.002 -0.008 -0.026 +0.001 -0.037 -0.002 SDSMOTE -0.002 -0.010 -0.020 +0.004 -0.015 +0.001 SL_graph_SMOTE -0.006 -0.006 -0.035 -0.002 -0.052 -0.022 SMMO -0.003 0.000 -0.070 -0.017 0.000 -0.049 SMOBD -0.003 0.000 0.000 0.000 0.000 0.000 SMOTE -0.003 -0.007 -0.020 +0.003 -0.029 +0.001 SMOTEWB -0.002 -0.001 -0.036 -0.001 -0.011 -0.002 SMOTE_AMSR +0.002 -0.005 -0.015 -0.002 -0.026 -0.008 SMOTE_Cosine 0.000 +0.002 -0.003 0.000 -0.006 +0.002 SMOTE_D -0.004 -0.019 +0.022 +0.004 -0.036 -0.003 SMOTE_ENN -0.003 0.000 0.000 0.000 0.000 0.000 SMOTE_FRST_2T -0.001 -0.036 -0.022 -0.003 -0.045 – SMOTE_IPF -0.002 -0.009 -0.020 -0.006 -0.020 +0.001 SMOTE_OUT -0.001 -0.012 -0.018 -0.003 -0.034 -0.001 SMOTE_PSO -0.004 -0.015 -0.033 -0.001 -0.004 – SMOTE_PSOBAT -0.003 -0.002 +0.002 +0.003 -0.027 – SMOTE_RSB -0.003 0.000 +0.006 0.000 +0.015 0.000 SMOTE_TomekLinks -0.002 -0.008 -0.018 +0.005 -0.032 +0.001 SN_SMOTE -0.002 -0.011 -0.011 -0.002 -0.022 0.000 SOI_CJ -0.003 -0.063 -0.031 -0.006 0.000 -0.003 SOMO -0.005 -0.006 -0.086 -0.003 +0.034 -0.004 SPY -0.027 0.000 -0.002 +0.010 +0.005 +0.003 SSO +0.004 -0.014 -0.007 -0.002 +0.033 – SUNDO +0.002 -0.050 -0.030 -0.015 -0.035 -0.017 SVM_balance -0.003 -0.008 -0.049 +0.011 -0.030 +0.002 SYMPROD -0.003 0.000 -0.058 -0.001 -0.036 +0.002 Safe_Level_SMOTE -0.002 -0.005 +0.012 -0.004 -0.023 -0.023 Selected_SMOTE +0.001 -0.010 -0.021 +0.003 -0.027 0.000 Stefanowski -0.005 -0.002 -0.008 -0.011 +0.028 +0.004 Supervised_SMOTE -0.001 -0.003 +0.012 -0.001 -0.001 – TRIM_SMOTE -0.002 -0.018 -0.193 -0.003 -0.041 -0.003 VIS_RST -0.075 0.000 0.000 0.000 0.000 -0.018 V_SYNTH -0.018 -0.002 +0.007 -0.013 +0.041 -0.068 cluster_SMOTE -0.003 -0.001 -0.003 +0.003 -0.025 +0.001 distance_SMOTE -0.003 -0.010 -0.022 -0.004 -0.035 +0.001 kmeans_SMOTE -0.004 0.000 -0.014 +0.004 +0.031 -0.002 polynom_fit_SMOTE_bus -0.003 0.000 +0.010 -0.004 -0.006 +0.002 polynom_fit_SMOTE_mesh -0.003 -0.003 +0.015 +0.002 -0.009 +0.002 polynom_fit_SMOTE_poly -0.007 -0.007 -0.009 +0.002 +0.023 -0.006 polynom_fit_SMOTE_star -0.004 +0.002 +0.007 -0.001 +0.005 +0.004 Codes: deg no-op, lib feature-space-transforming, x run failure, -- omitted for runtime (fraud only). Δ is the method’s PR-AUC minus the best trivial baseline’s on that dataset. Table S14: Δ -AUC per method vs. the best trivial baseline (logistic regression). As Table LABEL:tab:full_dauprc, for ROC-AUC; the largest positive entries sit on thoracic surgery, where the unresampled baseline collapses. method sylva accid Fram Pima thor fraud ADASYN 0.000 -0.013 -0.003 -0.001 -0.026 -0.022 ADG 0.000 -0.018 -0.267 -0.003 -0.069 – ADOMS 0.000 -0.005 -0.005 -0.005 -0.041 +0.001 AHC 0.000 -0.005 -0.003 -0.002 -0.022 -0.001 AMSCO 0.000 -0.014 -0.017 +0.001 -0.058 – AND_SMOTE 0.000 -0.015 -0.004 -0.003 -0.075 -0.017 ANS 0.000 -0.006 -0.048 -0.006 -0.131 -0.001 ASMOBD 0.000 -0.112 -0.129 +0.004 -0.151 0.000 A_SUWO -0.001 -0.013 -0.032 +0.001 -0.119 -0.026 Assembled_SMOTE 0.000 -0.008 -0.006 0.000 -0.020 -0.001 Borderline_SMOTE1 0.000 -0.016 -0.016 -0.007 -0.125 -0.023 Borderline_SMOTE2 -0.001 -0.010 -0.019 +0.005 -0.110 -0.022 CBSO 0.000 0.000 -0.001 +0.003 +0.001 -0.008 CCR 0.000 +0.001 0.000 +0.001 -0.016 +0.001 CE_SMOTE 0.000 -0.014 -0.005 -0.001 -0.060 -0.002 CURE_SMOTE 0.000 -0.006 -0.019 -0.008 -0.059 -0.001 DBSMOTE 0.000 -0.101 -0.123 -0.005 -0.154 0.000 DEAGO -0.004 -0.003 -0.020 +0.010 +0.077 – DE_oversampling 0.000 -0.003 -0.001 +0.006 +0.028 -0.012 DSMOTE -0.001 -0.005 -0.029 -0.002 -0.155 -0.016 DSRBF 0.000 -0.014 -0.002 -0.002 -0.020 – E_SMOTE lib lib lib lib lib – Edge_Det_SMOTE 0.000 -0.017 -0.004 +0.002 -0.047 +0.002 GASMOTE 0.000 -0.017 0.000 -0.010 -0.088 – G_SMOTE 0.000 -0.013 +0.001 -0.005 -0.050 -0.005 Gaussian_SMOTE 0.000 -0.019 -0.003 +0.009 -0.093 +0.004 Gazzah -0.003 -0.031 -0.031 -0.004 +0.043 -0.005 IPADE_ID -0.004 -0.042 -0.040 +0.004 -0.117 – ISMOTE -0.003 -0.047 -0.023 +0.004 +0.066 -0.010 ISOMAP_Hybrid lib lib lib lib lib lib KernelADASYN 0.000 -0.050 -0.020 +0.004 +0.005 – LLE_SMOTE 0.000 -0.008 +0.004 0.000 +0.019 -0.001 LN_SMOTE 0.000 -0.012 -0.012 +0.002 -0.084 -0.013 LVQ_SMOTE -0.001 -0.102 -0.013 -0.003 -0.054 -0.039 Lee 0.000 -0.019 -0.012 +0.002 -0.073 -0.014 MCT 0.000 +0.004 +0.001 +0.001 -0.051 0.000 MDO -0.001 -0.055 -0.028 +0.003 -0.192 -0.033 MOT2LD x x x x x – MSMOTE -0.001 -0.012 -0.013 +0.004 -0.064 -0.016 MSYN -0.001 -0.012 +0.004 -0.001 -0.041 0.000 MWMOTE 0.000 0.000 -0.029 -0.004 -0.056 -0.008 NDO_sampling 0.000 -0.009 -0.009 -0.003 -0.002 -0.001 NEATER -0.002 -0.011 -0.005 -0.003 -0.037 – NRAS -0.001 -0.086 -0.021 -0.001 -0.132 -0.009 NRSBoundary_SMOTE 0.000 -0.015 -0.002 -0.003 -0.061 -0.017 NT_SMOTE 0.000 -0.021 -0.005 0.000 -0.083 -0.001 OUPS 0.000 -0.007 -0.004 0.000 -0.010 0.000 PDFOS -0.001 -0.008 -0.006 +0.005 -0.033 -0.025 ProWSyn 0.000 -0.001 -0.004 +0.003 -0.021 0.000 ROSE 0.000 -0.003 -0.004 -0.006 -0.064 +0.004 RWO_sampling 0.000 -0.001 +0.001 +0.002 -0.019 0.000 Random_SMOTE 0.000 -0.013 -0.008 0.000 -0.087 +0.001 SDSMOTE 0.000 -0.013 -0.002 +0.002 -0.033 0.000 SL_graph_SMOTE 0.000 -0.016 -0.016 +0.001 -0.149 -0.017 SMMO 0.000 -0.003 -0.060 -0.015 0.000 -0.025 SMOBD 0.000 -0.003 -0.002 0.000 0.000 0.000 SMOTE 0.000 -0.014 -0.002 0.000 -0.068 0.000 SMOTEWB 0.000 +0.005 -0.023 0.000 -0.026 0.000 SMOTE_AMSR 0.000 -0.008 -0.002 0.000 -0.054 -0.001 SMOTE_Cosine 0.000 +0.002 0.000 0.000 -0.016 +0.001 SMOTE_D 0.000 -0.022 +0.007 +0.001 -0.083 -0.002 SMOTE_ENN 0.000 -0.003 -0.002 0.000 0.000 0.000 SMOTE_FRST_2T 0.000 -0.038 -0.005 -0.004 -0.113 – SMOTE_IPF 0.000 -0.012 -0.002 -0.006 -0.041 0.000 SMOTE_OUT 0.000 -0.022 -0.001 -0.003 -0.074 -0.001 SMOTE_PSO 0.000 -0.007 -0.004 +0.003 -0.015 – SMOTE_PSOBAT 0.000 -0.008 -0.001 0.000 -0.056 – SMOTE_RSB 0.000 -0.003 -0.002 +0.001 +0.032 -0.001 SMOTE_TomekLinks 0.000 -0.010 -0.005 +0.003 -0.078 0.000 SN_SMOTE 0.000 -0.013 -0.002 -0.003 -0.045 -0.001 SOI_CJ 0.000 -0.068 -0.029 -0.014 0.000 0.000 SOMO 0.000 -0.002 -0.101 -0.004 +0.007 -0.004 SPY -0.002 -0.003 -0.004 +0.004 0.000 0.000 SSO 0.000 -0.008 -0.012 -0.004 -0.040 – SUNDO 0.000 -0.066 -0.007 -0.012 -0.114 +0.002 SVM_balance 0.000 -0.009 -0.016 +0.011 -0.066 0.000 SYMPROD 0.000 -0.003 -0.039 -0.005 -0.087 0.000 Safe_Level_SMOTE 0.000 -0.012 +0.001 -0.003 -0.059 -0.017 Selected_SMOTE 0.000 -0.012 -0.006 -0.001 -0.054 -0.002 Stefanowski 0.000 +0.001 -0.003 -0.007 +0.017 -0.001 Supervised_SMOTE 0.000 +0.002 -0.001 0.000 +0.007 – TRIM_SMOTE 0.000 -0.018 -0.238 -0.003 -0.095 +0.002 VIS_RST -0.004 -0.003 -0.002 0.000 0.000 -0.027 V_SYNTH -0.001 -0.003 -0.006 -0.011 +0.054 -0.014 cluster_SMOTE 0.000 -0.012 -0.001 0.000 -0.063 0.000 distance_SMOTE 0.000 -0.011 -0.008 -0.003 -0.084 -0.001 kmeans_SMOTE 0.000 -0.003 -0.007 +0.002 +0.012 -0.001 polynom_fit_SMOTE_bus 0.000 0.000 0.000 -0.002 -0.009 -0.005 polynom_fit_SMOTE_mesh 0.000 0.000 +0.001 0.000 -0.033 -0.002 polynom_fit_SMOTE_poly -0.001 +0.001 -0.003 +0.003 +0.011 0.000 polynom_fit_SMOTE_star 0.000 0.000 -0.002 -0.001 +0.007 -0.002 Codes: as Table LABEL:tab:full_dauprc. 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