Placebo Decision Curves: Testing Whether a Clinical Model's Utility Survives Open-Label Care

When a hospital model raises an alert ("this patient may be septic"), clinicians who see it change what they do. They order more tests, look at the chart sooner, and treat earlier. The outcomes recorded afterward are therefore partly the effect of attention, not of what the model knows. The standard way to decide whether a model is clinically worth deploying is decision curve analysis, a method that scores a model by its net benefit: correct alerts minus false alarms, with false alarms weighted by how much harm a clinician is willing to accept per caught case. That method silently assumes outcomes are fixed facts about patients. In open-label deployments, where everyone knows who was flagged, they are not. Randomized Clinical Trials or Convenient Controls: TREWS or FALSE? made this concrete. Completely random alerts, grouped by whether clinicians then ordered a lactate test, produced an apparent mortality drop from 6.4% to 3.3%.

We propose a simple, assumption-light test for any utility evaluation pipeline. Run the identical pipeline on a placebo score, an alert that carries no patient information beyond what clinicians already see, and compare its net benefit to the value it must have by construction. Any excess is bias that the pipeline would also credit to a real model. Subtracting the placebo curve gives a model's net benefit beyond attention. A deployment threshold then has to clear that corrected bar, not the usual "treat everyone / treat no one" reference lines.

Core Claim

Net benefit at a risk threshold $t$ is $\mathrm{NB}(t) = \mathrm{TP}/n - (\mathrm{FP}/n)\cdot t/(1-t)$. Here TP and FP count correct and false alerts among $n$ patients, and $t/(1-t)$ is the harm-to-benefit ratio implied by the threshold. Suppose an alert fires on a fraction $r$ of patients independently of their outcome, and $\pi$ is the outcome rate. Then its net benefit is exactly

$$\mathrm{NB}_{\text{rand}}(r,t) = r\left[\pi - (1-\pi)\frac{t}{1-t}\right].$$

An honest evaluation pipeline must reproduce this line when fed random scores. Some pipelines estimate outcomes from clinician-dependent quantities: confirmed versus unconfirmed alerts, outcomes reweighted for intervening treatment, or features built on test-ordering patterns. If such a pipeline gives a placebo net benefit $\widehat{\mathrm{NB}}_{\text{plac}}(r,t)$ above this line, the gap measures its open-label bias at that alert rate.

We define the attention-corrected net benefit of a model $m$ at threshold $t$, where $r_m(t)$ is the model's alert rate at that threshold:

$$\Delta\mathrm{NB}_m(t) = \widehat{\mathrm{NB}}_m(t) - \left[\widehat{\mathrm{NB}}_{\text{plac}}(r_m(t),t) - \mathrm{NB}_{\text{rand}}(r_m(t),t)\right].$$

The claim is that this correction is not zero for evaluation pipelines currently used to justify deployment, even after standard confounder adjustment. We also claim it can change which model a hospital should deploy, in particular whether a complex model beats a simple bedside score.

Each prior strand does part of this. Complex models, marginal benefits combines inverse probability weighting with decision curves. That weighting reweights patients to mimic outcomes "as if no intervening treatment had happened." The paper finds an 85-feature boosted model adds only 1.8 correct mortality identifications per 10,000 patients over the 7-parameter National Early Warning Score (NEWS). But it assumes every intervening intervention is recorded, and it never checks that assumption. Randomized Clinical Trials or Convenient Controls: TREWS or FALSE? supplies the coin-flip idea. It applies it to a single mortality contrast, not to threshold-dependent net benefit, and it does not turn it into a reusable test. Our contribution is to make the coin flip a calibration standard for decision curves.

Research Program

The first component is the placebo family. A pure random placebo fires at rate $r$ uniformly; it tests whether a pipeline reproduces the analytic line. The harder case is a visible-severity placebo. It fires with probability proportional to a score built only from information clinicians see at triage, such as vital signs and age, plus noise. It then matches the model's alert rate.

This second placebo matters because the bias described in TREWS or FALSE arises when clinicians act on visibly sick patients. A real model correlates with visible sickness, so the right null is a score that also does, while adding nothing beyond it. The adoption study of the same sepsis system, Evaluating Adoption, Impact, and Factors Driving Adoption for TREWS, motivates this. It found that whether providers confirmed alerts depended on provider factors and on textbook symptoms like fever, not on physiology alone. Confirmation is therefore partly a response to visible cues.

The second component is a set of evaluation pipelines to audit. Each one runs unchanged on real models and on placebos:

  1. Naive decision curve on recorded outcomes.
  2. Confirmed-versus-unconfirmed comparison, the "convenient control" design.
  3. Backdoor-adjusted comparison, adjusting for lactate ordering and similar process-of-care variables as in TREWS or FALSE.
  4. Intervention-weighted decision curve, in the style of Complex models, marginal benefits.
  5. Representation learning under informative missingness, whose features encode which tests were ordered. This follows Causal Representation Learning from Multimodal EHRs under Non-Random Modality Missingness, which reports gains of up to 13.8% partly by treating missingness patterns as signal. The TREWS or FALSE analysis suggests that same ordering behavior is a backdoor path. Our placebo test can show whether those gains survive as decision value.

The third component is data. Primary analyses use the public MIMIC-IV and eICU cohorts already used by Causal Representation Learning from Multimodal EHRs. We construct alert-response proxies from timestamped events: lactate or blood-culture orders and antibiotic starts within a window after a score crosses threshold. Models are NEWS computed from charted vitals, a reduced NEWS without blood pressure and temperature (mirroring NEWS-Light), and a gradient-boosted model over labs, vitals, and ordering features. Outcomes are in-hospital mortality and sepsis onset.

We will seek collaborations to rerun the analysis on the Danish multi-centre admissions data of Complex models, marginal benefits and the UC San Diego and Emory cohorts of TREWS or FALSE. These are not public, so the core results cannot depend on them.

The fourth component is a prospective protocol that the retrospective work justifies and sizes. It has three arms, randomized per encounter:

  1. Silent: the model runs but clinicians do not see it, as in The silent trial.
  2. Visible sham: a rate-matched visible-severity placebo is displayed.
  3. Visible model: the real model is displayed.

Comparing model against sham estimates algorithmic utility. Comparing sham against silent estimates the attention effect. The silent trial work showed that blinded prospective running catches technical drift, with AUC falling from 0.90 to 0.50 and recovering to 0.85–0.91 after fixes. By design, though, it cannot measure what happens once clinicians can see the output. The sham arm is the missing piece. It also directly answers the operator-vigilance concern raised by the AI-assisted esophageal dissection cohort. There, novices with an on-screen AI matched experts (90.0% vs 92.1% complete lateral resection) while taking far longer (82 vs 49 minutes), and the authors themselves called for a sham display.

The sham arm only adds alerts and never withholds standard care. Its main ethical cost is extra workup and alert burden, which the retrospective placebo curves let us estimate in advance.

Baselines

The do-nothing reference is ordinary decision curve analysis with its usual comparators, treat-all and treat-none, applied to recorded outcomes. Many deployment decisions are still justified this way. Any corrected curve that differs from it by less than the bootstrap interval would mean the correction is practically irrelevant.

The strongest existing method is the intervention-weighted decision curve of Complex models, marginal benefits. Its reported results are a mortality AUC of 0.932 for XGB-EWS against 0.902 for NEWS, and a net benefit gain of 1.8 correct identifications per 10,000 patients over NEWS. It is the strongest competitor because it is the one published pipeline that already tries to remove treatment effects from net benefit. We will reimplement it on MIMIC-IV and eICU with the same treatment definitions, propensity models, and cross-fitting folds used for every other pipeline, and with the same tuning budget for its propensity model as for the outcome models. Beating it means one of two findings. Either its placebo excess is significantly above the analytic random line at clinically used thresholds, or the attention-corrected comparison of the boosted model against NEWS changes sign or loses significance where its uncorrected comparison does not.

The second strong baseline is backdoor regression adjustment, as in TREWS or FALSE. That paper reports that adjusting for lactate measurement erased the spurious effect, leaving adjusted mortality odds ratios of 2.21 and 1.6 in its two cohorts. We give it the same covariate set the placebo construction uses. If adjusted placebo curves sit on the analytic line, adjustment is sufficient for that pipeline and we will say so.

The simple-rule baseline is NEWS itself. The reduced NEWS without blood pressure and temperature is included because Complex models, marginal benefits shows it loses only 1.7 net benefit per 10,000 patients while saving about 3 minutes of nursing time per encounter.

The key ablation swaps the visible-severity placebo for the pure random placebo. If both give the same excess, the bias comes from the pipeline mechanics rather than from clinicians responding to visible sickness, and the simpler placebo suffices.

Why not just…?

Why not just adjust for the confounders you can measure? This is the most serious alternative, and it may partly work: TREWS or FALSE shows one backdoor adjustment removing a coin-flip artifact. But adjustment is only as good as the recorded covariates. That paper and Reliable Decision Support using Counterfactual Models both note that clinicians act on unrecorded cues and at irregular times. The latter shows that a standard model's risk scores shifted by 0.083 between treatment policies, against 0.001 for a counterfactual model. The placebo test does not compete with adjustment; it checks whether adjustment succeeded. If adjusted placebo curves consistently match the analytic line, the honest conclusion is that adjustment is adequate, and the placebo curve becomes a cheap validation step rather than a new estimator.

Why not just run a cluster-randomized trial of alert versus no alert? Such a trial removes selection bias, but it still bundles the model's information with the attention any alert attracts. It therefore cannot tell a hospital whether a cheaper, less accurate score would deliver the same benefit. Only a sham-alert arm separates the two. The retrospective placebo curves are what let us size that arm and argue it is worth its ethical cost.

Why not just deploy the simple score and skip the complex model? Complex models, marginal benefits and Evaluation of clinical utility in emulated clinical trials both support this. In the latter, guideline-based rules beat a learned "optimal" treatment rule against standard care in rheumatoid arthritis. We treat this as a likely outcome, not a straw man. The value of the placebo correction is that it decides the question with bias accounted for. Complex models lean more on ordering-derived features, so we expect them to carry more placebo excess, which would make the case for simple scores stronger.

Why not just recalibrate the model post hoc? Recalibration repairs a model's probability scale against recorded outcomes. Here the recorded outcomes themselves are distorted by clinician response, so recalibrating to them builds the distortion in. Net benefit, calibration, threshold selection, and training objectives for algorithmic fairness in healthcare shows how strongly net benefit at a fixed clinical threshold depends on calibration. That makes calibrating to biased labels a direct route to a biased threshold.

Proposed Experiments

The first decisive check replicates the coin flip in net benefit units. On MIMIC-IV and eICU, we compute placebo curves under the confirmed-versus-unconfirmed pipeline across thresholds from 2% to 30%, with bootstrap intervals over patients. We test whether the excess over the analytic random line is clearly positive, as the 6.4% versus 3.3% mortality contrast in TREWS or FALSE predicts. If it is not, the alert-response proxies are too weak, and we will report that rather than proceed.

The second check measures what remains after adjustment. We feed both placebos through the backdoor-adjusted pipeline and the intervention-weighted pipeline. A residual excess with a bootstrap interval excluding zero, especially for the visible-severity placebo, supports the claim that current adjusted pipelines still credit attention to models. A residual consistent with zero falsifies that claim for that pipeline.

The third check asks whether the correction changes decisions. We compare the boosted model, NEWS, and reduced NEWS by attention-corrected net benefit, and by the threshold range over which each beats treat-all and treat-none. The outcome of interest is whether rankings or the recommended threshold range shift relative to the uncorrected intervention-weighted analysis. This mirrors the rank reversals that A Consequentialist Critique of Binary Classification Evaluation found when moving from AUC to bounded-threshold scoring. We will also report the bounded Brier score form of the same comparison using that paper's released tools. There is no reported result on Lacuna for net benefit with a placebo-corrected reference, so these are new measurements, not comparisons against a published number.

The fourth check targets missingness-aware learning. We train a representation model that uses test-ordering patterns, in the spirit of Causal Representation Learning from Multimodal EHRs, and test whether its net benefit gain over a physiology-only model survives subtraction of the placebo excess. If it does, ordering features carry genuine decision value. If it vanishes, its retrospective gains are the kind that would collapse once clinicians act on its alerts.

Finally, the measured attention excess becomes the effect size for powering the three-arm prospective protocol. A small excess means the sham arm is not worth its burden. A large one means no open-label deployment of that model should be judged without it.