Count the Missing, Weight the Rare: A Better Bargain for Cardiac Phenotyping

TL;DR for operators

CW-B is not interesting because it discovers a novel model architecture. It is interesting because it treats three routinely neglected design decisions as one system:

1. Rare classes receive more influence during training. Class weights are computed separately inside each training fold, preventing common phenotypes from dominating the tree-building process.
2. Missing values retain their provenance. The pipeline imputes a numerical value but also adds an indicator showing that the original measurement was absent.
3. Clinical priorities are audited separately from aggregate performance. Stable coronary artery disease, acute coronary syndrome, and non-obstructive coronary disease are grouped into a predefined evaluation set because missing them can alter follow-up and treatment pathways.

On a five-class dataset containing 4,354 patient records and 57 structured features, CW-B records the strongest accuracy, Macro-F1, balanced accuracy, and prioritized F1 among the tested tree, ensemble, and neural baselines. Its balanced accuracy reaches 0.73, compared with 0.66 for a larger XGBoost baseline. Its prioritized F1 is 0.69, compared with 0.67 for that baseline.

The result is not a universal case for XGBoost, nor proof that the pipeline is ready to classify hospital discharges autonomously. The evidence comes from five-fold cross-validation on one cohort. Acute coronary syndrome recall remains only 0.46, and a stacking ensemble produces a lower prioritized miss rate than CW-B, though with worse overall accuracy and class balance.

The practical lesson is narrower and more useful: on structured operational data, performance can depend less on buying a more complicated model than on deciding what the model is allowed to ignore.

Discharge is where a classification error becomes somebody else’s workflow

A hospital discharge label is not merely a tidy summary placed at the bottom of a record. It can determine whether a patient enters a secondary-prevention program, receives medication review, returns for intensified follow-up, or is referred for further assessment.

That makes discharge phenotyping an awkward machine-learning problem. The model must distinguish several related cardiac presentations using incomplete structured records, while the available classes are distributed unevenly and the consequences of confusing them are not equal.

The natural response is usually to improve the classifier. Add capacity. Tune more parameters. Replace the trees with a neural network. Assemble several models and let them vote.

The paper introducing CW-B, a class-weighted boosting framework for five-class cardiac discharge phenotyping, takes a less theatrical route.¹ It keeps XGBoost and redesigns the conditions under which XGBoost learns.

That distinction is the paper’s real contribution. The model is familiar. The learning environment is not.

CW-B links three mechanisms that are frequently handled as unrelated implementation details:

• class-frequency weighting;
• missingness-aware feature construction;
• risk-oriented classwise evaluation.

The paper’s experiments suggest that the combination matters more than simply making the base learner larger. This is inconvenient for anyone hoping model capacity will compensate for a vaguely specified data pipeline. It usually does not. The expensive model merely learns the vague specification more confidently.

The model is only the middle of the pipeline

CW-B predicts one of five discharge phenotypes:

The dataset contains 4,354 records. The largest classes are stableCAD with 1,675 cases and nonCAD with 1,469. OldMI has only 266. ACS and CAS contain 483 and 461 cases respectively.

A standard multiclass learner can achieve respectable accuracy by concentrating on the classes it sees most often. This is not malice. It is optimization working exactly as instructed.

CW-B changes the instruction before it changes the model.

Its pipeline can be simplified as:

Raw patient record
        ↓
Fold-specific preprocessing
        ↓
Imputed values + missingness indicators
        ↓
Class-weighted XGBoost training
        ↓
Five-class probability output
        ↓
Global metrics + prioritized class audit

Each step protects against a different form of silent information loss.

Class weighting protects minority labels from being numerically drowned out. Missingness indicators protect the distinction between an observed value and an imputed substitute. Prioritized auditing protects clinically consequential errors from disappearing inside a pleasant aggregate score.

None of the mechanisms is exotic. Their coordination is the point.

Class weighting changes what the trees are allowed to ignore

For each cross-validation training fold, CW-B counts how many examples belong to each class and assigns an inverse-frequency weight:

where $N_{\mathrm{tr}}$ is the number of training records, $C$ is the number of classes, and $n_c$ is the number of training records in class $c$. The weights are then normalized, and each training example receives the weight associated with its label.

This is more than multiplying the final loss by a decorative coefficient. In gradient boosting, instance weights affect the gradients and curvatures used to choose splits and estimate leaf values. A rare-class record therefore exerts more influence over the structure of subsequent trees.

Without weighting, a split that improves stableCAD or nonCAD performance can look more valuable simply because those classes supply more observations. With weighting, improvements involving oldMI, ACS, or CAS receive a larger voice in the optimization process.

The weights are computed inside each training fold. That detail matters. Class counts and preprocessing parameters are learned without consulting the evaluation fold, preserving the intended separation between fitting and testing.

The higher-capacity XGBoost baseline makes the paper’s mechanism easier to interpret. It uses 1,200 boosting iterations and depth-seven trees, compared with CW-B’s 600 iterations and depth-five trees. If CW-B’s gains came merely from having a stronger learner, the larger baseline should have closed the gap.

It did not.

CW-B reaches a Macro-F1 of 0.72 and balanced accuracy of 0.73. The higher-capacity XGBoost baseline reaches 0.69 and 0.66. Accuracy differs by only one percentage point, 0.81 versus 0.80, but the seven-point balanced-accuracy gap indicates a much larger difference in how evenly the model recalls the five classes.

That is precisely why accuracy is insufficient here. A model can classify the dominant categories well enough to look competent while repeatedly failing the phenotypes that justified building the system.

Imputation fills the cell; an indicator preserves what happened

Missing data are often discussed as though they were holes that must be filled before the real modeling begins. Insert a median, move on, and allow everyone to return to the more glamorous matter of neural architectures.

CW-B treats that view as incomplete.

Of the dataset’s 57 features, 55 contain missing values. Across all feature entries, 15.54% are missing. The pipeline standardizes the variables and imputes each missing entry using a median estimated from the relevant training fold.

It then adds a binary indicator for every feature, recording whether the original value was missing.

The resulting representation contains both:

• the imputed numerical feature vector; and
• a parallel vector of missingness flags.

This allows the model to distinguish two superficially identical values:

Observed measurement = median value
Imputed measurement  = median value + missingness flag

Numerically, the imputed entries may be equal. Operationally, they are not.

A missing laboratory measurement can reflect clinical judgment, workflow sequencing, test availability, patient condition, or documentation practice. The model may learn useful associations from those recording patterns. It may also learn brittle institutional habits, which is one reason external validation matters. But erasing the distinction in advance guarantees that the model cannot even examine it.

The paper’s ablations make missingness indicators look more consequential than a routine preprocessing enhancement.

Removing the indicators reduces:

• Macro-F1 to 0.6804;
• balanced accuracy to 0.6666;
• prioritized F1 to 0.6444.

Using XGBoost’s native missing-value handling performs better than removing the indicators entirely, reaching 0.7082 Macro-F1, 0.6909 balanced accuracy, and 0.6780 prioritized F1. It still trails the complete pipeline.

K-nearest-neighbor imputation combined with indicators also underperforms the full design, producing 0.7008 Macro-F1, 0.6791 balanced accuracy, and 0.6703 prioritized F1.

The likely conclusion is not that median imputation has suddenly become a universal clinical standard. The experiment is narrower: for this cohort and model configuration, retaining an explicit missingness channel contributes information that neither plain imputation nor native tree handling fully recovers.

Clinical priority enters through the audit, not the training objective

The paper defines stableCAD, ACS, and CAS as a clinically prioritized set. These categories connect to established diagnostic, therapeutic, follow-up, or risk-management pathways.

The set is selected before evaluation based on clinical actionability. It is then used to compute:

• prioritized recall;
• prioritized F1;
• prioritized miss rate.

This is a sound governance choice because it prevents the researchers from choosing whichever classes happen to make the model look impressive after seeing the results.

It is also important to understand what the prioritized set does not do.

It does not change the labels. It does not alter the prediction rule. It does not directly assign higher training costs according to clinical severity. The model’s training weights are based on class frequency, while clinical actionability enters through evaluation.

Those are two different forms of alignment:

This distinction matters for deployment.

CW-B is balanced against class frequency, but it is not an explicit economic or clinical cost model. It does not encode that missing ACS may be more harmful than confusing one lower-risk phenotype with another. It evaluates selected classes together, using an unweighted average across stableCAD, ACS, and CAS.

That is a reasonable research design. It should not be mistaken for a complete decision policy.

An organization adapting the pipeline would still need to decide whether different false negatives warrant different thresholds, escalation rules, or human-review requirements. Averages are useful for comparing models. They do not settle operational trade-offs.

The experiments are testing mechanisms, not merely collecting baselines

The baseline suite is most useful when read as a set of targeted questions.

The main comparison table establishes overall relative performance. The ablations explain why the full method performs as it does. The confusion matrices then reveal where each model pays for its aggregate score.

That hierarchy matters. A leaderboard tells us who won this experiment. An ablation tells us what the winner appears to depend on.

The strongest evidence is what breaks when components are removed

Removing class-balanced instance weighting reduces Macro-F1 to 0.6968, balanced accuracy to 0.6621, and prioritized F1 to 0.6631.

The balanced-accuracy decline is especially informative. It suggests that without reweighting, the model returns to favoring classes that are easier or more frequent, even if overall accuracy remains superficially acceptable.

Removing missingness indicators produces an even lower Macro-F1 and prioritized F1 than removing weighting. This does not prove that missingness is universally more important than imbalance. It shows that, in this dataset, documentation patterns contain enough predictive information that erasing them materially weakens the pipeline.

The complete method therefore appears to benefit from two distinct corrections:

1. The weighting mechanism changes how strongly each class influences learning.
2. The indicator mechanism changes what information is available to learn from.

One adjusts the optimization pressure. The other expands the representation.

This is why the paper is better understood as a pipeline-design study than as an XGBoost study. The base algorithm remains recognizable throughout. What changes is the accounting system around it: which observations count more, which absences remain visible, and which errors are inspected separately.

The confusion matrix exposes the bargain behind the headline metrics

CW-B’s aggregate scores are strong, but the classwise results are more revealing.

Its approximate recalls are:

The comparison with the larger XGBoost model explains much of the balanced-accuracy gain. The baseline recalls only 0.44 of oldMI cases and 0.62 of CAS cases, while CW-B reaches 0.69 and 0.68. StableCAD and nonCAD recall remain broadly similar.

The model is not improving every class uniformly. It is recovering performance where the unweighted baseline is weakest.

ACS remains the uncomfortable exception. CW-B recalls 0.46 of ACS cases, compared with 0.45 for the larger XGBoost model. Almost half is not an operating point that should encourage unattended deployment for a time-sensitive acute phenotype.

The paper’s prioritized metrics average stableCAD, ACS, and CAS. CW-B reaches prioritized recall of 0.67 and therefore a prioritized miss rate of 0.33. That is the best bargain among several metrics, not the disappearance of clinically consequential errors.

The stacking ensemble makes the trade-off explicit. It reaches prioritized recall of 0.69 and a miss rate of 0.31, both better than CW-B. Its recall is higher for ACS and CAS—0.61 and 0.77—but stableCAD recall falls to 0.70, nonCAD recall falls to 0.88, and overall accuracy declines to 0.75.

Its prioritized F1 is only 0.66, compared with CW-B’s 0.69, indicating that its extra sensitivity comes with weaker precision or a less favorable balance between precision and recall.

There is no universally correct winner between these operating profiles. The choice depends on what happens after a positive or negative prediction.

If every flagged case receives an expensive specialist review, precision matters. If missing a case creates substantially greater harm than reviewing an additional false positive, sensitivity may deserve more weight. The paper surfaces the trade-off but does not price it.

That pricing exercise belongs to the operator.

The business value is more consistent routing, not autonomous diagnosis

The direct result is a cross-validated improvement in five-class classification. The business relevance emerges through the workflows attached to those classes.

More reliable discharge phenotyping could support:

• follow-up scheduling;
• referral routing;
• medication-review queues;
• secondary-prevention enrollment;
• retrospective coding and quality audits;
• prioritization of records for clinician verification.

The safest initial use is not autonomous replacement of clinical judgment. It is workflow triage with visible error monitoring.

A hospital could use model outputs to identify records requiring verification, detect inconsistent discharge classifications, or prioritize manual review for selected phenotypes. The classwise audit already points toward this model-assurance layer.

The operational value would come from reducing variation in what happens after discharge. That could mean fewer patients omitted from a follow-up queue, faster review of ambiguous cases, or more consistent application of care pathways across shifts and teams.

The paper does not measure any of those outcomes. They are business inferences, not experimental findings.

A practical adaptation would therefore separate the evidence into three levels:

This separation is less exciting than announcing “AI transforms cardiac care.” It is also more likely to survive contact with a hospital.

A deployment team should copy the controls before copying the model

The most transferable part of CW-B is not its exact hyperparameter configuration. It is the sequence of controls embedded around training and evaluation.

1. Define the operational classes before optimizing

The paper uses a unified five-class task rather than collapsing the problem into a simpler binary target. An adopter should first verify that every class corresponds to a meaningful downstream action and that clinicians agree on the label definitions.

A mathematically separable class with no operational consequence is mostly an elegant way to create maintenance work.

2. Compute weights only from the training partition

Class weighting should be treated as part of model fitting. Any cross-validation or temporal validation workflow must estimate class frequencies independently within its training data.

The same rule applies to normalization, imputation, and feature selection.

3. Preserve missingness as a feature with governance attached

Missingness indicators can add signal, but the signal may come from local workflow habits. A hospital should examine whether predictions depend heavily on who orders a test, which unit records a field, or whether a measurement becomes available only after a clinical decision has already been made.

The indicator is informative precisely because the data-generation process is informative. That process can change.

4. Predefine priority metrics

Clinical or business priority groups should be chosen before comparing models. Otherwise, teams can always discover a subgroup on which their preferred model looks unusually competent.

The priorities should also be more granular than a single average when the costs differ materially across classes.

5. Select thresholds using workflow capacity and error cost

CW-B uses an argmax multiclass decision rule. A production system might instead require class-specific thresholds, abstention, or mandatory review when probabilities are close.

That choice cannot be inferred from Macro-F1 alone.

6. Monitor classwise error after deployment

Aggregate accuracy should be accompanied by confusion matrices, recall, precision, and miss rates for every operationally important class. Monitoring should also be stratified by site, time period, and relevant patient groups.

An auditable model without an audit process is merely a model with well-organized potential.

Deployment-oriented is not deployment-validated

The study has several boundaries that materially affect interpretation.

First, all reported evidence comes from stratified five-fold cross-validation on one cohort of 4,354 records. There is no external hospital test, prospective evaluation, temporal holdout, or silent production trial.

Second, the paper does not report whether the missingness patterns are stable across institutions. A model that learns documentation behavior at one hospital may encounter a different recording culture elsewhere.

Third, the classwise results still include substantial clinically important error. ACS recall of 0.46 is an obvious concern. The model may improve the average across prioritized categories while remaining unsuitable for autonomous use in the category with the clearest urgency.

Fourth, the study does not evaluate probability calibration, class-specific thresholding, abstention, or human-model collaboration. These mechanisms often determine whether a classifier becomes a usable decision-support system.

Fifth, the paper argues that tree structure supports interpretability and auditing, but it does not present a clinician-facing explanation study, feature-attribution analysis, or evidence that reviewers can reliably understand and act on individual predictions. Architectural inspectability is useful. Demonstrated interpretability is a higher bar.

Finally, there is no workflow-impact or economic evaluation. The paper does not measure time saved, reviews triggered, referrals corrected, adverse events avoided, or implementation cost.

These limitations do not erase the experimental result. They define its proper scale.

CW-B is evidence that disciplined treatment of imbalance and missingness can improve a structured clinical classifier. It is not evidence that the resulting classifier can safely own the discharge decision.

Better models sometimes begin with better bookkeeping

CW-B’s lesson is almost disappointingly practical.

The pipeline does not win by replacing the clinical dataset with a foundation model, embedding every field into an enormous latent space, or adding enough parameters to make the methods section require a financing round.

It wins by keeping three accounting questions visible:

• Which classes dominate the learning signal?
• Which values were genuinely observed?
• Which errors matter enough to inspect separately?

The paper shows that answers to those questions can improve performance more than adding capacity to the same base model. Its ablations support the role of both class weighting and explicit missingness representation. Its classwise evaluation also reveals that no aggregate victory removes the need to choose among sensitivity, precision, and operational cost.

For clinical analytics teams, that is the useful takeaway. Before searching for a more impressive algorithm, inspect the pipeline that tells the existing algorithm what counts.

The rare cases may need more weight. The blank cells may need to remain visible. And the errors may need names rather than averages.

Cognaptus: Automate the Present, Incubate the Future.