Anchor-and-Shrink: Fair Forecasting for Small Subgroups

When a hospital or health agency forecasts something from only a few past observations, it usually fits one model to the pooled total. Examples include next year's cases of a rare heart disease, next month's ICU deaths, or a patient's blood pressure over the next hours from the first few readings. Subgroups such as women, older patients or minority racial groups then receive whatever share the pooled model implies, or they get their own model fitted to even fewer, noisier points. Neither choice has been audited for who it fails. Bai et al. fitted a single grey forecasting model to Beijing-wide hypertrophic cardiomyopathy counts and projected cases to double by 2029. The same data show women dying at a far higher rate (4.20% vs. 2.70%), a difference the aggregate projection cannot represent (Prevalence, incidence and mortality of hypertrophic cardiomyopathy based on a population cohort of 21.9 million in China).

This note proposes two things. The first is an audit that separates a small subgroup's forecast error into noise that no model could remove and bias that a model introduced. The second is a cheap correction layer, called anchor-and-shrink, that removes the bias without retraining the underlying forecaster. The working hypothesis is that, in sparse forecasting, most of the apparent subgroup disparity is either irreducible small-count noise or a level offset. A level offset means a systematic gap between the forecast level and the subgroup's true level, which is the forecasting analogue of the "mean discrepancy" that Tan et al. found drives subgroup failure in ICU risk models. Disparity in the shape of the trend should be a smaller part. If that is right, the fix is to re-anchor each subgroup's level on its most recent observation and borrow the trend from the pooled series, with the amount of borrowing set by how noisy that subgroup is.

Core Claim

Fairness audits of clinical models have so far covered classifiers. MIMIC-IF audited deep mortality predictors on MIMIC-IV and found that groups with higher baseline mortality get lower discrimination (MIMIC-IF: Interpretability and Fairness Evaluation of Deep Learning Models on MIMIC-IV Dataset). Tan et al. showed that subgroup failure in ICU risk models is driven mostly by the gap between predicted and true subgroup mean risk, and is fixed best by targeted data selection plus isotonic recalibration (Investigating Data Interventions for Subgroup Fairness: An ICU Case Study). Both papers motivate this work. Neither addresses forecasting, and Tan et al.'s calibration step assumes a dense validation cohort that a small subgroup's short series cannot provide.

The forecasting side has the opposite blind spot. Grey models, ForecastPFN and multi-output transformers are all evaluated on aggregate series only. Grey models are small differential-equation forecasters fitted to the cumulative sum of a handful of observations. ForecastPFN is a transformer pretrained on synthetic series that forecasts new series with no fitting (ForecastPFN: Universal Forecasting for Healthcare). The multi-output transformer is TFT-multi (Simultaneous forecasting of vital sign trajectories in the ICU).

We claim three things are new. The first is the noise-adjusted decomposition of subgroup forecast error. The second is the empirical finding about which component dominates in sparse regimes. The third is a model-agnostic post-hoc layer that closes the bias component even for zero-shot forecasters, which cannot be fine-tuned per subgroup.

The audit matters because raw error comparisons are misleading here. A subgroup with a tenth of the events has relatively larger count noise. A raw mean squared error comparison will therefore show that group "disadvantaged" even under a perfect model. The MIMIC-IF correlation between baseline rate and performance may partly reflect this effect. We test that directly.

Research Program

The audit works as follows. For a subgroup $g$ and horizon $h$, we compute the forecast error. We then subtract an estimated noise floor $\nu_g$, the error a perfect forecaster of the true underlying rate would still incur. For count series, the noise floor is the Poisson variance at the observed rate. For vital signs, it is estimated from the variance between repeated measurements taken minutes apart.

What remains after subtracting the floor is split into three parts. Level bias is the mean residual. Trend bias is the slope of the residual over the horizon. The leftover is shape error. We report each part by subgroup, together with the excess-error disparity, defined as the worst subgroup's excess error divided by the best subgroup's. Raw-error disparity is reported alongside for comparison.

The correction works on top of any pooled forecaster $f$ that produces a forecast $f(t+h)$ for the total series. For subgroup $g$, it outputs

$$\hat y_g(t+h) = s_g\, f(t+h) + \delta_g + \lambda_g\, \tau_g\, h,$$

where the terms are defined as follows:

  • $s_g$ is the subgroup's recent share of the total.
  • $\delta_g$ is the subgroup residual at the latest observation. This applies the "new information priority" idea, which re-anchors on the newest point instead of the oldest (Desserts sales forecast based on the new information improved gray model), but here it is applied to the gap between subgroup and pool rather than to the raw series.
  • $\tau_g$ is the subgroup's own residual trend.
  • $\lambda_g = \sigma_\tau^2/(\sigma_\tau^2 + v_g)$ is an empirical-Bayes shrinkage weight. Here $\sigma_\tau^2$ is the spread of true trend deviations across subgroups, and $v_g$ is the sampling variance of $\tau_g$. The form comes from the standard normal-normal posterior mean.

Noisy groups therefore inherit the pooled trend, and well-measured groups keep their own. This gating follows the spirit of FairDSR, which applies fairness constraints only where its uncertainty estimate is low and shows that applying them everywhere on noisy proxies hurts (Fairness Under Demographic Scarce Regime). In our case the uncertainty concerns the subgroup's trend rather than its demographic label. A second, label-scarce variant uses FairDSR-style proxy groups with MC-dropout filtering, for sites where race is often unrecorded.

We deliberately do not build a new hybrid grey architecture. The wavelet-grey-neural model cut error by 76.5% over plain GM(1,1) on a 15-point settlement series (Integrated Wavelet-Grey-Neural Network Model for Heritage Structure Settlement Prediction). That is one series with hand-tuned wavelet depth, and it says nothing about subgroups. We include it only as a candidate pooled forecaster.

Baselines

The do-nothing reference is the pooled forecast split proportionally, $s_g f(t+h)$. This is what Bai et al. effectively did, and it is what any subgroup claim must beat. Next to it sits last-observation carried forward per subgroup, the simplest local forecaster. Pooled forecasters $f$ will include GM(1,1), new-information GM(1,1), ForecastPFN run zero-shot, and, for vital signs, TFT-multi trained on the full MIMIC-IV training split.

The strongest existing method for dense vital-sign forecasting is TFT-multi. It reports mean absolute error of 7.4 for mean blood pressure, 9.0 for pulse and 0.7 for temperature on the MIMIC-IV v2.2 test set of 9,638 patients (Simultaneous forecasting of vital sign trajectories in the ICU). No subgroup-stratified result was found on Lacuna for TFT-multi, and none for ForecastPFN on any clinical subgroup series. For short count series, no reported result was found on Lacuna, so we establish all reference numbers ourselves. To keep comparisons fair, every method sees the same history window, the same subgroup labels and the same test horizons. Any learned component gets the same hyperparameter search budget of 20 configurations on a validation fold.

The strongest competitor on our actual question is a jointly fitted hierarchical Bayesian forecaster. It has subgroup-specific level and trend random effects with separately learned variances, fitted by full posterior inference on all subgroups at once. This is the textbook small-area answer. Running it is the honest test of whether anchor-and-shrink adds anything beyond convenience.

We also run the Tan et al. recipe adapted to forecasting, which applies isotonic recalibration of forecasts per subgroup using held-out residuals. We run fully separate per-subgroup models as well.

Two ablations isolate the key ingredients. In the first, we remove the anchor ($\delta_g=0$, level offset estimated from the full-history mean residual instead). In the second, we remove the shrinkage ($\lambda_g=1$). Beating a baseline means lower worst-subgroup excess error at matched or better average error, with a paired bootstrap interval over hospitals or patients that excludes zero.

Why not just…?

Why not just fit a separate model to each subgroup? With four to twenty points per subgroup, a separate fit doubles down on noise. Grey models in particular extrapolate the fitted growth rate, and on fluctuating series they lose accuracy badly (Integrated Wavelet-Grey-Neural Network Model for Heritage Structure Settlement Prediction). We expect separate fits to win for large subgroups and lose for the smallest. The $\lambda_g$-free ablation and the separate-model baseline, plotted against subgroup size, will show where the crossover lies.

Why not just fit a hierarchical Bayesian model? This is the real threat, and it may match us on count series. If it does, the contribution narrows. The audit and its finding about where disparity lives still stand. The correction's remaining value is that it attaches post hoc to forecasters that cannot be made hierarchical, such as zero-shot ForecastPFN or a frozen TFT-multi. The re-anchoring step may also help under abrupt level shifts, where a hierarchical model fitted to the full history adapts slowly. We will report this head-to-head result plainly, including the case where we lose.

Why not just recalibrate per subgroup as Tan et al. did? Isotonic regression needs many held-out pairs per subgroup. A short series supplies a handful, so the calibration map will be close to arbitrary for exactly the groups that need it. The adapted-isotonic baseline tests this, and we expect it to underperform for the smallest subgroups.

Why not just add more data from other hospitals? Tan et al. found that naive multi-site addition often worsens subgroup performance, and Zhou et al. report that scaling skewed data entrenches majority patterns (Yukun Zhou et al.). More fundamentally, the setting of interest is a single small site that has no other data to add.

Proposed Experiments

The study has two regimes.

The first regime is short subgroup count series built from the eICU Collaborative Research Database. For each hospital, we form monthly ICU admission and in-hospital death counts split by sex, age band and self-reported race. Each series spans roughly the database's two years. We forecast one to three months ahead from the preceding six to twelve months, using rolling origins.

The second regime is per-patient sparse vital-sign forecasting in MIMIC-IV, following the TFT-multi setup but restricted to the first few hours of each stay. Each patient therefore contributes only a few observations, and errors are scored only on observed values. Subgroups here are race, sex, age band and insurance type, as in MIMIC-IF. "Pooled" means the population model, and the anchor is the patient's own latest reading minus the population forecast for that time.

The first decisive check is the audit itself. We test whether the raw-error disparity across subgroups shrinks substantially once the noise floor is subtracted. We also test whether the MIMIC-IF-style correlation between baseline rate and error survives that subtraction. If most of the disparity is noise, that is itself an important corrective finding for fairness auditing of forecasts.

The second check is whether level bias makes up the largest share of excess error for the smallest subgroups under the pooled forecasters. This is the premise of the correction. If shape error dominates instead, the method is not justified and we will say so.

The third check is the comparison of anchor-and-shrink against the hierarchical model and against TFT-multi. On worst-subgroup excess error, it should match the hierarchical model on count series and beat it on series with level shifts. It should also reduce subgroup excess-error disparity for frozen TFT-multi and zero-shot ForecastPFN without raising their average error above the reported TFT-multi figures on the full test set.

The fourth check covers the label-scarce variant. We hide 80% of race labels, as in FairDSR's protocol, and test whether gating corrections by proxy-label uncertainty preserves most of the gain obtained with true labels.