Machine learning cannot settle what bank deregulation caused

A sophisticated prediction algorithm cannot decide what would have happened without a policy change. That distinction anchors a new study of the 2018 US banking reform by Ali Habibnia, Esfandiar Maasoumi and Gaurav Shah. Their paper, posted to arXiv on November 4, 2026, is a preprint; its versioned landing page lists no journal publication.

The authors revisit an earlier banking study using double, or debiased, machine learning. They reproduce a positive relationship between regulatory exposure and risk-weighted-asset growth, but show that its magnitude changes substantially with sample construction and adjustment for banks’ earlier growth. The evidence does not identify one specification as the correct causal answer.

A comparison between different kinds of relief

The analysis follows 91 US bank holding companies from the second quarter of 2015 through the first quarter of 2020. Twenty had assets of $50–250 billion in early 2018; the other 71 held $10–50 billion. The design compares changes around enactment of the Economic Growth, Regulatory Relief, and Consumer Protection Act in May 2018.

Crucially, both groups received regulatory relief, although through different provisions. The comparison therefore concerns differential regulatory exposure, not deregulation versus no deregulation. Coding the reform as beginning in the same quarter also simplifies a rollout whose statutory timing differed across banks.

The outcome is quarterly growth in risk-weighted assets, with extreme observations capped. Those assets can grow because a bank expands its balance sheet, because its regulatory risk density changes, or both. Faster growth is not a pure measure of greater portfolio risk.

The replicated conventional regression gives a coefficient of 0.0193—approximately a 1.93-percentage-point quarterly growth differential. A random-forest implementation using the same two-way-demeaned inputs gives 0.0181. Yet excluding banks whose asset bands differed between early 2015 and early 2018 reduces the conventional coefficient to 0.0122. That restriction changes the population being compared; it does not reveal a corrected policy effect.

What machine learning can—and cannot—remove

Double machine learning predicts the outcome and treatment from other characteristics, then relates the unexplained portions. Its estimating equation is designed to limit sensitivity to small prediction errors. Cross-fitting trains on some banks and evaluates on others, keeping each bank’s quarterly history together to avoid treating repeated observations as independent training and validation cases.

The paper combines mathematical results, synthetic-data experiments and empirical comparisons. A central warning concerns transformations used to remove persistent bank differences. Subtracting a bank’s average from a nonlinear function is generally not equivalent to applying that function after subtracting the average from its inputs. Squaring a change, for example, loses information retained by the change in a square. A flexible algorithm cannot recover information its inputs discard.

In one constructed simulation, the true effect is 0.2. Correctly transforming quadratic terms produces an average estimate of 0.203 with 91 banks; reversing the order produces 0.602. This illustrates a specified failure mechanism, not proof that the banking estimates suffer that exact bias.

More adjustment can also remove the comparison itself. Under common treatment timing, treatment averages together with calendar information can reveal exposure perfectly. Unrestricted adjustment then leaves no residual treatment variation to identify the coefficient. Restricting the model can preserve variation, but requires a defensible outcome-model restriction.

Different procedures may also answer different questions. Under stated assumptions, specified first-difference scores target the adoption-quarter effect, while within-bank scores target an average post-reform effect. The paper’s bank-level overlap estimator emphasizes larger-bank profiles with more comparable smaller banks; a separate doubly robust estimator targets the average effect among larger banks. These averages need not coincide.

Earlier growth changes the picture

Using pre-reform characteristics, the forest overlap estimate is 0.0107 and the doubly robust estimate 0.0125. Adding average prior growth reduces them to 0.0015 and 0.0026. Their nominal 95% intervals then include zero. The overlap estimate falls across all four fitting families examined: linear/logistic models, forests, polynomial LASSO and boosted trees.

This does not establish that regulation had no effect. Conditioning on prior growth changes the identifying assumption and can change the overlap-weighted target. The authors describe competing growth dynamics under which that adjustment either removes a discrepancy or introduces one; earlier-period comparisons do not resolve which explanation applies.

Causal interpretation still requires comparable counterfactual growth trends conditional on the chosen characteristics, no anticipation, no spillovers between banks and suitable comparison-bank support. Inference additionally relies on sampling and prediction-quality conditions not established for these banking data. Original upstream data construction remains incompletely documented.

Weighting adds another vulnerability: loss-minimizing polynomial LASSO places roughly 87% of normalized comparison-bank weight on one bank. In a separate weaker-overlap simulation, nominal 95% doubly robust intervals cover their target only 89.5% of the time. Neither result validates the banking intervals. The study’s lesson is not to abandon machine learning, but to separate predictive robustness from credible policy identification.