When a Missing Lab Test Means the Drug Worked

In hospital records, a lab test that was never ordered is rarely an accident. Prior work has documented two opposite meanings for an empty cell. Sometimes the patient was too sick for anyone to chart, so the sparsest records belong to the patients who die fastest. Other times the clinician saw no reason to test, often because the patient looked stable. Treatment adds a third meaning that current methods ignore. After a drug that acts on several biological pathways at once, clinicians stop ordering a whole group of related tests together, because the problems those tests track have resolved. A model that cannot tell "untested because improved" from "untested because nobody had time" will misjudge which patients a treatment helps. That error matters most for multi-target drugs, whose benefit is already thought to vary across patient subgroups.

We propose a disease-progression model that learns three things jointly from incomplete records. It learns the patient's latent subtype and stage. It learns how a multi-target treatment shifts several biomarkers together. And it learns a separate model of the clinician's decision to order each test, with that decision allowed to depend on the treatment and on the biomarker's unseen current value. The output we care about is not a better risk score. It is a less biased estimate of how the treatment's effect differs across subtypes when the evidence for improvement is mostly empty cells.

Core Claim

Current methods for missing values that carry information treat missingness as a function of how severe the illness is. Treatment-induced normalization has a different statistical signature. Ordering of several tests on the same biological axis stops at the same time, shortly after treatment begins, and the stop follows a trend toward normal in the last observed values. Severity-driven gaps look different: ordering of unrelated tests stops together, and the last values were worsening. We claim this difference in signature is enough to separate the two mechanisms. Separating them should give lower error in subtype-specific treatment-effect estimates than either assuming values are missing at random or using a severity-only model of missingness. The gain should appear exactly where treatments act on several axes, and it should vanish for a single-target control treatment.

Grounding in Prior Work

The motivating evidence comes from three places.

The first is the missing-data literature. Hripcsak et al. documented the "documentation paradox": the healthiest-looking records carry the highest mortality. Williams et al. showed that tests are ordered on clinical suspicion, which distorts retrospective severity scores. Both frame missingness purely as observation bias. Neither considers that treatment changes why tests stop.

The second is evidence that multi-target drug effects are heterogeneous and touch several pathways. The Danhong injection trial ran in 920 patients across 31 centers. Clinical response was 52.41% versus 39.62% for placebo at Day 30. Responders showed a gene module that coordinates anticoagulation and cholesterol handling. The analysis, however, kept only complete-case high responders measured on fixed study days. The Xuebijing meta-analysis pooled trials in kidney injury from sepsis. It reports a mortality risk ratio of 0.82 alongside lower creatinine and urea, with evidence certainty graded "moderate to very low." Neither study models trajectories or missing data. These are exactly the questions the proposed model would put to observational records.

The third is progression models that separate subtype from stage. These supply our method. Missing-data SuStaIn, from Estarellas et al., integrates a missing biomarker out under a uniform distribution. This lets it recover five Alzheimer's subtypes in the Alzheimer's Disease Neuroimaging Initiative (ADNI) cohort with up to 40% missing data. Its uniform assumption is exactly the "uninformative" choice we replace, and it has no treatment term. PATNet learns patient-, feature- and time-varying probabilities that each feature gets observed, using a tensor factorization. It works only on binary codes and has no operator through which treatment changes those probabilities.

Two further papers constrain the design. TD-HNODE models continuous-time complication cascades on MIMIC-IV, reaching 85.7% recall. It needs expert-specified pathways, and it does not model treatment or missingness. The review by Sow and Oxtoby notes that progression models assume untreated, monotone curves. That is the assumption a normalizing treatment breaks.

The ADCB simulator is a semi-synthetic benchmark fitted to ADNI with treatment effects that differ across subtypes. It supplies our controlled testbed. Its stylized interventions are single-target, and its missingness is not modeled.

Research Program

The model has three parts that share a latent state.

The first part is the latent state itself. A patient has a discrete subtype $z$ and a continuous disease stage, following a continuous-time trajectory model. The stage determines the expected value of each biomarker $m$.

The second part is a treatment operator. Treatment $a_t$ shifts the expected values of a set of biomarkers. The shift's size is specific to each subtype, and its direction is learned. A multi-target treatment is one whose shift is supported on several pathway axes. A single-target treatment shifts only one.

The third part is an ordering model. Here the indicator $R_{m,t}$ records whether test $m$ was ordered at time $t$:

$$\Pr(R_{m,t}=1 \mid x_{m,t}, a_t, u_t) = \sigma\big(\alpha_m + \beta_m\, |x_{m,t} - \mu_m| + \gamma_m a_t + \delta_m u_t\big)$$

The symbols are defined as follows. $x_{m,t}$ is the true, possibly unseen value. $\mu_m$ is its normal reference value. $u_t$ is an acuity signal built from always-recorded variables such as vital signs and the intensity of interventions. $\sigma$ is the logistic function. The parameter $\beta_m$ captures "order when abnormal," which makes the missingness depend on the unseen value itself (missing not at random). The parameter $\gamma_m$ captures protocol effects of treatment. The parameter $\delta_m$ captures severity-driven gaps, including the documentation paradox through a sign that is allowed to be negative at extreme acuity.

Training maximizes the joint likelihood of observed values and ordering indicators, with missing values integrated out. Integration is by variational inference over $x$ and enumeration over $z$.

Identifiability is the central risk, because a model whose missingness depends on unseen values is not identified in general. We rely on two anchors and test both.

The first anchor is a set of "routine" markers drawn in standard panels almost regardless of state, such as creatinine in a basic metabolic panel. These serve as shadow variables: they are informative about the latent stage but barely affect ordering.

The second anchor is "gap-closing" observations, where a test is ordered again after a gap. These reveal what the value was trending toward during the gap.

We will report results with and without each anchor. We will also show, on simulated data, where the parameter $\beta_m$ becomes unrecoverable.

Baselines

The naive reference is a complete-case analysis that keeps only patient-times with full panels. It is paired with last-observation-carried-forward, which is what clinical retrospective analyses typically do. This reference shows how large the bias is that we claim to fix.

The first principled baseline is missing-data SuStaIn (Estarellas et al.), extended with the same treatment operator but keeping its uniform, uninformative treatment of missing values. No numeric subtype-recovery figure is reported in the file. The paper reports only that it was most accurate up to 40% missingness against deletion, mean imputation and nearest-neighbor imputation. We will rerun it rather than quote it. It is the strongest competitor for subtype and stage recovery. Beating it on effect estimation would show that informative missingness, not the treatment term, drives the gain.

The second principled baseline is PATNet (PATNet). We adapt it to continuous values by replacing its binary reconstruction loss with a Gaussian one, and we give it treatment indicators as inputs. It is the strongest existing model of observation bias. The file reports gains of up to 23% relative mean Average Precision for progression and up to 12% relative PR-AUC for mortality over HiTANet and LogPar on MIMIC-III and eICU. No absolute values are given, so those numbers are not a target we can match directly.

The third principled baseline is multiple imputation by chained equations conditioned on treatment history, followed by a T-learner. A T-learner fits separate outcome models for treated and untreated patients and differences them. It performed better than S-learners on ADCB, though no numeric PEHE is reported on Lacuna for ADCB.

All baselines receive the same patients, features, folds and number of hyperparameter configurations, which is a fixed budget of 30. Results are averaged over five seeds.

The key ablation removes the dependence of ordering on treatment, so that $\gamma_m = 0$ and the treatment acts only on values, not on test ordering. A second ablation removes the dependence on the unseen value, so that $\beta_m = 0$. Beating these ablations means a lower error in the heterogeneous effect per subtype (PEHE) with non-overlapping seed intervals, in the normalization-driven regime.

Why not just…?

Why not just feed missingness masks and treatment indicators into a flexible sequence model? A recurrent network with masks can learn ordering patterns well enough to predict outcomes. This is a real threat for prediction, and the TADPOLE findings (TADPOLE) show that simple ensembles of such predictors are hard to beat. Our target is different, though. We want an estimate of how much the treatment changed unseen marker values in each subtype. A mask-aware predictor can exploit "tests stopped" as a cue for good outcomes without attributing the change to biology versus protocol. We include such a model, a gated recurrent network with masks plus a T-learner, as an additional baseline. If it matches our effect-estimation error on the simulator, the structured ordering model is unnecessary, and we will say so.

Why not just assume values are missing at random given treatment and history? If the reasons for ordering are fully captured by recorded vital signs and treatments, conditional imputation is unbiased, and our model should collapse to it with $\beta_m \approx 0$. We include a missing-at-random simulator regime precisely to check that our method does not lose there. The real-data test of whether that assumption holds is the gap-closing check below.

Why not just stratify a missing-data subtype model by treatment arm? Stratification avoids modeling the treatment, but it halves the data per subtype. It still reads a post-treatment gap as uninformative, which biases the treated arm toward its last abnormal values and shrinks apparent benefit. The SuStaIn-with-treatment baseline quantifies this bias directly.

Proposed Experiments

The first experiment is semi-synthetic. We extend ADCB so that a "multi-component" treatment shifts three biomarker axes with effects that differ by subtype. A matched single-target treatment shifts one axis. We cross these with three ordering regimes: missing at random, severity-driven (including a documentation-paradox arm), and normalization-driven. We vary missingness from 10% to 60%. The metrics are PEHE, adjusted Rand index for subtype recovery, error in the inferred stage, and RMSE on masked values. The decisive prediction is that our model beats all baselines only in the normalization-driven regime for the multi-target treatment. Over-claiming would appear as gains under missing-at-random or for the single-target control.

The second experiment uses real data from MIMIC-IV and the multi-center eICU database. The cohort is sepsis with kidney involvement. The continuous panels cover kidney function (creatinine, urea), coagulation (platelets, INR, fibrinogen; this mirrors the inflammation–coagulation axis of Wang et al.) and inflammation and metabolism (lactate, white count). The exposure is a pleiotropic agent recorded in these databases. Systemic corticosteroids are an example, since they act on inflammatory, hemodynamic and metabolic axes. A narrow agent serves as the negative control. Real data has no true effects, so the decisive check is predictive validity during gaps. For every gap that later closes, we score how well each model's distribution for the closing value, inferred from data before the gap, predicts the value. We also check whether the inferred "normalized" label anticipates later recovery outcomes better than the "neglect" label does. eICU sites with protocolized daily labs provide a second check, because ordering there is nearly uninformative: our model should find $\beta_m$ and $\gamma_m$ near zero at those sites. We will also report whether the inferred subtype-by-treatment interaction is stable across MIMIC-IV and eICU. If it is unstable, the method's clinical claims fail, regardless of simulator performance.