Reluctant Weather Normalization for Auditable Clean-Air Policy Attribution

When a city's air gets cleaner after a clean-air law, how much of the improvement came from the law and how much from luckier weather? Weather can mask a real decline or inflate it. Stagnant winters trap smoke, and windy, rainy years wash it out. The standard answer is to fit a flexible model of pollution as a function of weather and read the leftover slow trend as the policy effect.

This proposal argues that the main risk in that recipe is flexibility itself. Meteorology also drifts over years, so an over-flexible weather model can absorb part of the policy signal into its weather terms, or invent nonlinear weather effects out of noise. The resulting attribution is then biased in a way nobody can audit. We borrow two ideas from clinical machine learning, where auditable decisions on observational data are a hard requirement. The first is "reluctant" model building: a nonlinear term enters only if it beats a simpler linear one by a margin. The second is case-based matching: each counterfactual is backed by concrete, similar historical cases. We combine them into a weather-normalization method whose policy estimate comes with an audit trail.

The method is then tested in a way current air-quality attribution never is. We inject policy effects of known size into real pollution records and check which methods recover them.

Core Claim

Weather-adjusted policy estimates are only as trustworthy as the model's restraint about weather. Our first claim is that a reluctant additive weather model, paired with matching on "meteorological twin days," recovers known injected policy effects with less bias and better calibrated uncertainty than three current methods: frequency filtering, cross-validated generalized additive models, and boosted-tree normalization. Our second claim is that the matched twin days give a regulator something no current method gives. For a post-policy day, they show the specific pre-policy days with the same weather and how much dirtier those days were.

The novelty is not "apply clinical tools to air quality." It has three concrete parts. One is a selection discipline that targets a specific failure mode, policy signal leaking into weather terms. Another is an audit object, the matched analog set. The last is a semi-synthetic benchmark that turns attribution from an unverifiable number into a measurable estimation problem.

Where the Two Directions Meet

The atmospheric literature shows both that attribution matters and that it rests on unchecked modeling choices.

For Beijing's 2013–2017 action plan, The control of anthropogenic emissions contributed to 80 % of the decrease in PM2.5 concentrations in Beijing from 2013 to 2017 reports two estimates of the emission-control share of the decline. Kolmogorov–Zurbenko (KZ) filtering, a repeated moving average that separates slow trends from seasonal and day-to-day swings, gives 80.6%. The full-physics WRF-CMAQ chemical transport model gives 78.6%.

Over eastern China, Separating emission and meteorological contributions to long-term PM2.5 trends over eastern China during 2000–2018 uses a generalized additive model (GAM: a sum of smooth one-variable curves) alongside CMAQ. It finds that the 2013–2018 decline was "8.4% weaker when adjusted for meteorology," though the GAM and CMAQ meteorological contributions correlate only "0.53–0.72" monthly. In India, LongPMInd reconstructs four decades of daily particulate matter with LightGBM, a gradient-boosted tree model. It reads a 2018 turning point, from +0.34 to −0.78 µg m⁻³ yr⁻¹, as the signature of the National Clean Air Programme, while attributing about 64% of predictive power to meteorology.

These studies motivate the work. None of them tests whether its own decomposition would recover a known policy effect. The modest 0.53–0.72 agreement between two respected methods suggests that the choice of method moves the answer.

The clinical papers supply the method. A reluctant additive model framework for interpretable nonlinear individualized treatment rules fits linear effects first, lets spline terms enter only under heavier penalties, and selects with a concordance-based information criterion. In its simulations, K-fold cross-validation over-selected nonlinear terms where this criterion did not. Safe and Interpretable Estimation of Optimal Treatment Regimes learns a distance metric weighted by outcome-relevant variables and estimates counterfactuals from matched historical patients. That paper reports outperforming deep reinforcement learning baselines, especially when much of the data is missing.

Interpreting Sepsis Prediction through Positional Explanation shows that sequence models confuse what a measurement is with when it appears. It separates the two with swaps of time positions. We reuse that swap as a diagnostic for whether a model's "trend" is genuinely tied to the calendar or leaks through weather variables.

One constraint applies throughout: the matching approach assumes no hidden confounders. In our setting the hidden confounders are unmeasured emission changes unrelated to the policy. We return to this below.

Research Program

The core model, for station $s$ and day $t$, is

$$\log y_{s,t} = \tau_s(t) + \sum_j \beta_j m_{j,s,t} + \sum_{j \in S} g_j(m_{j,s,t}) + \varepsilon_{s,t},$$

where:

  • $y_{s,t}$ is the measured concentration of fine particulate matter (PM2.5) or nitrogen dioxide (NO2).
  • $m_{j,s,t}$ are reanalysis meteorological variables: boundary-layer height, wind components, temperature, humidity and precipitation.
  • $\tau_s(t)$ is a slowly varying trend that carries the policy effect.
  • $\beta_j$ are linear weather effects.
  • $g_j$ are spline corrections admitted only for variables in a selected set $S$.

Selection follows the reluctant recipe. A sparse linear fit comes first. Splines are then fit to its residuals, and a final fit penalizes spline terms more heavily than linear ones.

The trend term $\tau_s(t)$ is constrained to vary slowly, for example piecewise linear with knots at most every six months. This keeps it from soaking up weather variation.

The concordance criterion in the RAITR paper was designed for treatment rules, not concentration regression. We will therefore adapt it as a rank-concordance criterion between predicted and observed daily concentrations, and test it head-to-head against cross-validation. We treat this adaptation as an open empirical question, not a given.

The audit layer comes second. For each post-policy day, we find its nearest pre-policy days under a learned weather metric whose weights come from the variable importances of the fitted weather model, following the variable-importance-matching recipe. The matched-difference estimate of the policy effect is then reported next to the additive model's $\tau$. Disagreement between the two flags days where the additive structure is likely wrong. These are often the extreme haze episodes that tree models smooth away. Each reported effect then comes with its evidence: the set of twin days and how much dirtier they were.

The third component is the position-swap diagnostic. For any normalization model that includes calendar time, we permute calendar time while holding weather fixed, and permute weather while holding time fixed. If the model's attribution to time changes when weather is permuted, the trend is entangled with weather.

Baselines

The naive reference is the raw before-versus-after change in mean concentration, with no weather adjustment. Any method that fails to beat it on injected effects under adverse weather has no reason to exist.

KZ filtering, as used in the Beijing study, is the classic low-cost method. Its reported number is the 80.6% emission share for Beijing 2013–2017 in the Beijing attribution paper. We will run it with the standard window settings on identical station series.

The cross-validated GAM, following Xiao et al., is the closest structural competitor because it is also additive and transparent. It shares our covariates and trend specification and differs only in using unrestricted splines tuned by 10-fold cross-validation. This comparison isolates the effect of reluctance.

Boosted-tree normalization is, we expect, the strongest competitor. It uses LightGBM in the LongPMInd style, with calendar time as a feature, and estimates the trend by repeatedly resampling meteorology and averaging predictions. It is flexible and widely used, and it captures interactions our additive model may miss. On real data, the closest reported generalization figure is LongPMInd's out-of-year R² of 0.66 in LongPMInd. That is a reconstruction metric, not an attribution error. No reported result was found on Lacuna for any method's error in recovering a known policy effect. Producing that number is part of the contribution.

All learned methods receive the same ERA5 meteorology, the same station records and an equal hyperparameter search budget of 50 configurations each.

WRF-CMAQ is not rerun. Its published 78.6% Beijing share serves as an external physical reference.

Ablations remove matching (additive only), replace reluctant selection with cross-validation, and replace the learned matching metric with plain Euclidean distance. Together they establish which ingredient carries any gain.

Beating the field means two things on the semi-synthetic benchmark. The first is lower absolute bias in the recovered effect than both the GAM and the boosted tree, by a margin outside seed-to-seed variation. The second is 90% intervals with near-nominal coverage.

Why not just…?

Why not just use KZ filtering, which already matched CMAQ to within two points in Beijing? Agreement in one city and one period does not show that it recovers effects in general. KZ only separates frequencies, so a multi-year drift in boundary-layer height lands in the "trend" exactly like a policy. The Beijing paper itself needed CMAQ to separate local from regional and sectoral contributions. The semi-synthetic runs that inject an effect timed to coincide with an adverse weather drift will show directly whether KZ attributes that drift to policy.

Why not just use a standard GAM? A standard GAM is the method we modify, so the question is whether reluctance matters. The RAITR simulations show cross-validation over-selecting nonlinear terms in a different setting. Our ablation that swaps only the selection rule answers the question for air quality. If cross-validation matches reluctant selection on bias and coverage, we will report that the GAM is sufficient and that the matching audit is the remaining contribution.

Why not just run WRF-CMAQ counterfactuals? Where the budget and an up-to-date emission inventory exist, CMAQ remains the physical reference, and we use it that way. It costs millions of core-hours and depends on emission inventories that are often delayed by years. It cannot be rerun interactively by a city agency evaluating a policy from last year. Our method targets that setting, and Beijing is where we check that it agrees with CMAQ.

Why not just use boosted-tree normalization with meteorology resampling? This is a real threat. It handles weather interactions that our additive model approximates, and it may simply win. The semi-synthetic benchmark settles the question. We inject effects that multiply concentrations, which creates realistic weather interactions, and compare recovered against true effects. If the boosted tree is as accurate, the proposal narrows to two things. One is the matched-analog audit, attached to the tree's weather importances instead of our additive model. The other is the position-swap diagnostic, which tests whether the tree's calendar-time feature is leaking weather.

Proposed Experiments

The decisive experiment is a semi-synthetic injection benchmark. We take hourly station records from Air Quality Arena, which covers six national monitoring networks from 2022 to 2025. That benchmark provides no meteorology, so we join ERA5 reanalysis to each station.

Into each station series we inject a known policy effect $y'_{s,t} = y_{s,t}\,(1 - r(t))$. Here $r(t)$ is a step or ramp starting at a randomly chosen date, sized from 5% to 30%. The true effect is defined relative to whatever happened anyway: it is the difference between each method's estimate on the injected series and on the original series. Unknown background policies therefore cancel out.

We stratify injections by whether the onset coincides with a favorable or an adverse weather drift. That split is where leakage should show.

Placebo runs with $r=0$ at fake dates measure how often each method reports an effect that does not exist. The India network, where the Arena paper reports that supervised models struggle to beat a seasonal-naive forecast, is a deliberately hard case.

The real-world checks are narrower. On Beijing 2013–2017, assembled from the national monitoring network archive and ERA5, we compare each method's emission share with the published 80.6% (KZ) and 78.6% (CMAQ). On eastern China 2013–2018, we test whether each method reproduces the finding that weather adjustment weakens the decline by about 8.4%. These real cases cannot rank methods by themselves because the truth is unknown. They can expose a method whose benchmark accuracy fails to carry over to a documented policy period.

The proposal fails if reluctant selection yields no bias reduction over the cross-validated GAM on the adverse-drift stratum. It also fails if matched-day estimates disagree with the additive trend everywhere, not just on extreme episodes. In that case, the audit layer would be measuring model error rather than finding it.