Attributable Deaths from a Continuous Risk Factor When Hazards Are Not Proportional

Public health agencies rank risk factors by asking how many deaths would be avoided if a population's exposure, such as blood pressure, body mass index, or a serum marker, were moved to the level with the lowest risk. The answer is a population attributable fraction: the share of deaths that would disappear under that counterfactual. In practice it is usually computed by taking a hazard ratio from a Cox model and inserting it into a formula built for simple risk ratios. The low-risk exposure level is often picked as the minimum of a curve fitted to the same data. Both shortcuts are biased in ways that matter most where survival data are richest. When cumulative mortality is high, a hazard ratio no longer approximates a risk ratio. When hazards change over follow-up, there is no single hazard ratio to insert. And the lowest point of a noisy fitted curve sits below the true minimum, which inflates every fraction measured against it.

We propose to estimate attributable fractions directly on the survival scale, as a function of follow-up time. Each person's predicted cumulative mortality under their observed exposure is compared with their predicted mortality under a shifted exposure, and the results are averaged over the real population. The low-risk level is chosen on one half of the data and evaluated on the other, so the noise that picks the minimum cannot also flatter the estimate. The deliverables are an estimator with valid confidence intervals, a simulation study showing when the usual shortcut fails, and reanalyses of public survival cohorts.

Core Claim

Two distinct errors enter the standard way of turning a fitted survival model into an attributable fraction. Their size can be predicted from quantities an analyst already has.

The first error is a scale mismatch. Under proportional hazards, a constant hazard ratio implies a risk ratio that shrinks toward one as cumulative risk grows. The hazard-ratio plug-in therefore overstates attributable burden when mortality over the horizon is substantial. This is the case in haemodialysis, where the MBD-5D cohort recorded 5.7 deaths per 100 person-years over three years, and in critically ill cohorts such as SUPPORT. When hazards cross over time, as Deep Cox Mixtures for Survival Regression documents on SUPPORT, the plug-in has no well-defined input at all.

The second error is optimism in the choice of the low-risk level, which the burden literature calls the theoretical minimum risk exposure level (TMREL). When the TMREL is the argmin of an estimated curve, its estimated risk is biased downward. The resulting fraction is biased upward, and the bias grows with model flexibility and shrinks with sample size.

The estimand we target is the time-indexed attributable fraction

$$ \mathrm{AF}(t) = \frac{F_{\text{obs}}(t) - F_{g}(t)}{F_{\text{obs}}(t)}, \qquad F_{g}(t) = \mathbb{E}_{W}\big[\,1 - S\big(t \mid g(X, W), W\big)\big]. $$

Here $t$ is the follow-up horizon. $X$ is the continuous exposure and $W$ the confounders. $S(t \mid x, w)$ is the conditional survival function. $F_{\text{obs}}(t)$ is cumulative mortality under the exposures people actually have. $g$ is the counterfactual policy, either "set exposure to the TMREL $x^*$" or the more realistic "move exposure at most $\delta$ toward $x^*$." The usual continuous plug-in instead computes $1 - 1/\int \mathrm{HR}(x)\,p(x)\,dx$ against the fitted nadir. We claim the two quantities diverge by an amount that grows with $F_{\text{obs}}(t)$ and with time variation in the hazard ratio.

Research Program

We build the estimator in three layers. Each layer can be switched off for ablation.

The first layer is the outcome model. Its default is a Cox model with restricted cubic splines in the exposure and an interaction with a pre-specified effect modifier. This mirrors the model that Hypertension modifies the associations of body mass index and waist circumference with all-cause mortality among older Chinese used to show that the BMI nadir shifts with hypertension status. That study stopped at hazard ratios and never integrated over the exposure distribution, and it motivates our subgroup-specific TMRELs. Where diagnostics show non-proportional hazards, we replace the outcome model with Deep Cox Mixtures, a mixture of Cox models with neural gating that permits crossing survival curves and improved calibration on FLCHAIN. We use it purely as a survival-curve estimator, which is a role its authors did not consider. DeepSurv, a neural network trained on the Cox partial likelihood, is a second flexible option, but it retains proportional hazards.

The second layer is standardization. We predict $S(t \mid x, w)$ for every person at their observed exposure and at $g(X, W)$, then average the predictions to obtain $\mathrm{AF}(t)$ over a grid of horizons. When flexible learners are used, we add a one-step correction based on the efficient influence function of the standardized survival contrast, with cross-fitting. This follows the double machine learning logic of Time-Varying Causal Survival Learning, which supplies the technique but targets individual hazard effects rather than population burden. It also follows the targeted estimation that Causes and consequences of child growth faltering in low-resource settings used for population intervention effects. That study applied the approach to continuous growth outcomes and modelled mortality separately through hazard ratios. We fuse those two stages into one survival-scale estimand.

The third layer separates nadir selection from evaluation. We split the data in two. On half A we fit the curve and choose $x^*$, overall or within effect-modifier strata. On half B we refit the outcome model and estimate $\mathrm{AF}(t)$ at that fixed $x^*$. We then swap the halves and average. Because the noise in B is independent of the noise that selected $x^*$ in A, the optimism disappears, at a cost in variance that we quantify. We also report the bounded-shift policy, which avoids extrapolating to exposure levels few people actually occupy.

Baselines

The naive reference point is the dichotomized approach of the MBD-5D case-cohort study. That study discretized continuous marker splines into "target achieved or not," took adjusted Cox hazard ratios, and applied the binary prevalence formula. It reported a PAF of 16.8% (95% CI 4.3–27.7) for jointly achieving calcium, phosphorus, and intact-PTH targets, and 8.8% (95% CI 1.1–16.0) for calcium plus phosphorus. We run it on each benchmark using clinically conventional cutpoints and the same confounder set. It is beaten if our estimator has lower bias and nominal coverage against simulated truth.

The strongest existing competitor is the burden-study plug-in for continuous exposures, applied to a spline Cox model. This integrates the fitted hazard ratio curve over the empirical exposure distribution relative to the fitted nadir, as continuous comparative risk assessment does in the Global Burden of Disease laryngeal cancer analysis. It is strongest because it already uses the full continuous exposure and is what a careful epidemiologist would do today. It receives the same spline basis, knots, confounders, and data as our estimator. We found no reported attributable-fraction result on Lacuna for this method on FLCHAIN, SUPPORT, or SEER, so the comparison is new and run by us. It is beaten if, in simulations with known truth, its bias grows with cumulative mortality and with hazard-ratio drift while ours stays near zero. We also expect its intervals to undercover.

The second strong competitor is plain standardization with the same spline Cox model, using an in-sample nadir and no influence-function correction. It isolates our key ingredients. A version with split-sample nadir selection but no correction isolates the debiasing step. A version with the correction but in-sample nadir isolates the optimism fix. Swapping in Deep Cox Mixtures isolates the value of relaxing proportional hazards. For the flexible models, the bar is calibration. Deep Cox Mixtures reports an expected calibration error of 0.0200 on FLCHAIN against 0.0992 for the standard Cox model, and we require our refits to land near those values before trusting the downstream fractions. All variants share identical folds, hyperparameter grids, and compute.

Why not just…?

Why not just plug spline Cox hazard ratios into the continuous PAF formula, as burden studies do? It is a good approximation when the outcome is rare over the horizon and hazards are proportional, and we expect it to agree with our estimator in that regime. The problem appears where survival data are most useful. In MBD-5D, roughly a sixth of the cohort dies over three years at the reported rate. In SUPPORT, hazards cross, and a single hazard ratio does not summarize the exposure's effect. The simulations vary cumulative mortality and hazard-ratio drift precisely to map where the plug-in becomes unacceptable. If the gap stays small across realistic settings, that is itself a useful negative result, and we will report it as such.

Why not just do ordinary standardization with a spline Cox model and stop? This is the real threat. In large samples with a pre-specified TMREL it may perform as well as our full estimator. Our contribution then reduces to the nadir-optimism correction, plus the move to Deep Cox Mixtures where proportional hazards fail. The ablations are designed to settle this directly. If the correction and the split-sample nadir change neither bias nor coverage at the sample sizes of FLCHAIN and SUPPORT, we will narrow the claim to the scale-mismatch and non-proportional-hazards findings.

Why not just use logistic regression at a fixed horizon with Levin's formula? This approach discards censoring. Anyone lost before the horizon must either be dropped or counted as a survivor, and each choice biases cumulative incidence. It also cannot produce $\mathrm{AF}(t)$ as a curve over time. Time-Varying Causal Survival Learning further shows that ignoring when exposure begins can manufacture effects: a naive interaction coefficient of −2.191 (p < 0.01) on Stanford heart transplant data shrank to −0.557 (p = 0.47) once timing was handled. We include the horizon-logistic estimator in the simulations with informative censoring to show the size of this bias.

Proposed Experiments

The first experiment is a fully synthetic simulation, where the true $\mathrm{AF}(t)$ can be computed exactly. We generate a continuous exposure with U-shaped and reverse-J-shaped log-hazards, borrowing the shape documented in the older-adult BMI cohort. We generate confounders that shift exposure and risk, and an optional modifier that moves the nadir. We vary sample size from 1,000 to 50,000, three-year cumulative mortality from 2% to 40%, and hazard-ratio drift from none to curves that cross. The metrics are bias, root mean squared error, and 95% interval coverage of $\mathrm{AF}(t)$ at several horizons, along with bias in the estimated TMREL.

The second experiment is semi-synthetic. We keep the real covariate distributions of FLCHAIN and SUPPORT, using free light chain and creatinine in FLCHAIN and physiological measures such as mean arterial pressure in SUPPORT. We simulate outcomes from known hazard surfaces with realistic censoring, so the true fractions are known but the covariate geometry is real.

The third experiment reanalyzes real cohorts. On FLCHAIN, SUPPORT, and SEER, we report $\mathrm{AF}(t)$ curves for selected continuous exposures under full-shift and bounded-shift policies, and document where the methods disagree. Without known truth, these analyses are descriptive and report agreement only. If access to MBD-5D can be arranged through its investigators, the most informative real-world check is whether the published 16.8% shrinks once the continuous counterfactual, the survival scale, and split-sample targets are applied.

Three decisive checks determine whether the claim holds. First, the plug-in's bias should rise roughly in proportion to cumulative mortality and to hazard-ratio drift, while our estimator's bias stays flat. Second, the in-sample-nadir variants should show upward bias that shrinks with $n$ and grows with spline flexibility, and the split-sample version should remove it at a quantified cost in variance. Third, interval coverage should be close to 95% for the corrected estimator and visibly below it for the plug-in. If the second check fails, meaning nadir optimism is negligible in practice, we drop that component and present the work as a survival-scale replacement for hazard-ratio plug-ins.