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Machine learning the first stage in 2SLS: Practical guidance from bias decomposition and simulation

T0 review · 3 major / 5 minor · reviewed 2026-08-15 · deepseek-v4-flash

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Pith's one-line read The paper claims that putting nonlinear machine-learning methods in the first stage of 2SLS can generate more bias in causal estimates than ignoring endogeneity altogether.

desk verdict A solid, internally consistent simulation study warning against naive ML first stages in 2SLS, with a genuinely useful bias decomposition--but every DGP has a linear first stage, so the headline about nonlinear methods is narrower than the abstract claims. read the letter →

arxiv 2505.13422 v1 pith:FDTA5BZ6 submitted 2025-05-19 econ.EM cs.LGstat.APstat.ML

Connor Lennon , Edward Rubin , Glen Waddell This is my paper · ORCID
classification econ.EMcs.LGstat.APstat.ML
keywords machinelearninginstrumentalvariablestwo-stageleastsquaresfirststagebiasdecompositionrandomforestpost-Lassoforbiddenregression
verification ladder T0 review T1 audit T2 compute T3 formal

The pith

A machine-rendered reading of the paper's core claim, the machinery that carries it, and where it could break.

The reading

The paper asks whether using machine learning to predict the endogenous regressor in the first stage of two-stage least squares improves or degrades causal estimates, and it answers with a decomposition plus Monte Carlo evidence. It claims that linear machine-curated first stages, such as post-Lasso and principal-component analysis, perform at least as well as traditional 2SLS, while nonlinear methods such as random forests, boosted trees, and neural networks generate substantial second-stage bias. In the simulated designs, random-forest-based 2SLS produces more bias in the causal parameter than plain OLS that ignores endogeneity altogether. The practical stakes: a researcher who inserts a flexible predictor into the first stage can end up farther from the truth than one who makes no endogeneity correction at all.

What carries the argument

The load-bearing object is the bias decomposition. For any first-stage prediction $\hat{x}$, the wedge between the 2SLS estimate and the true effect is \[\hat\$beta_1^{{\mathrm{2SLS}}$} - \beta_1 = \frac{\beta_1\, \widehat{\mathrm{Cov}}(\hat{x}, e) + \widehat{\mathrm{Cov}}(\hat{x}, u)}{\widehat{\mathrm{Var}}(\hat{x})}.\] Here $e = x - \hat{x}$ is the first-stage residual and $u$ is the structural error; the identity is derived by substituting $y = \beta_0 + \beta_1 x + u$ into the second-stage OLS formula. The three terms isolate the forbidden-regression correlation, the exclusion-restriction violation, and the variance-reduction amplifier, and the paper uses the decomposition to attribute the simulated bias of each estimator across the four designs.

What would settle it

Re-run the high-complexity simulation with a genuinely nonlinear first stage, for example $x = z_1^2 + z_2 + z_3^3 + \varepsilon$, and compare random-forest and boosted-tree 2SLS against naive OLS and post-Lasso; if the flexible methods show less bias than naive OLS in that design, the paper's across-the-board warning about nonlinear ML first stages would need a boundary.

Watch

Extended reading notes

Core claim

The paper establishes, in its simulations, a mechanical explanation of when ML-assisted 2SLS fails. Writing the second-stage estimate as the true effect plus a wedge that depends on the first-stage predictions, the paper shows three channels: nonlinear predictors can correlate with their own residuals, flexible algorithms can recover endogenous variation in the regressor even from valid instruments, and variance reduction in predictions amplifies whichever covariance bias exists. Across a low-complexity design and three high-complexity designs with 100 instruments, post-Lasso and PCA first stages match or beat OLS-based 2SLS, whereas Lasso, boosted trees, neural networks, and especially random forests shift the distribution of estimates away from the true effect. Random-forest 2SLS is worse on average than naive OLS in every design the paper simulates.

Load-bearing premise

The premise the results depend on is that the first-stage relationship between the instruments and the endogenous regressor is linear in every simulated design, so the nonlinear methods are never given a chance to improve on the true model.

Editorial extensions

If this is right

  • Post-Lasso and PCA first stages preserve linearity and deliver estimates whose bias is at least as low as standard 2SLS in the simulated designs, making them the safe ML-assisted choices.
  • Random-forest and boosted-tree first stages can produce second-stage bias exceeding that of naive OLS, so using them off the shelf can make endogeneity problems worse rather than better.
  • Because the first bias component is multiplied by $\beta_1$, larger true treatment effects produce larger absolute bias from the same nonlinear first-stage procedure.
  • Variance reduction, normally a virtue in prediction, inflates ML-in-2SLS bias whenever the covariance terms are nonzero, so prediction-optimal tuning is not causal-estimation-optimal tuning.
  • Remedies such as out-of-sample predictions or using ML output as a synthesized instrument can shut down some bias channels but require strengthening the exclusion restriction to all learnable functions of the instruments.

Reading between the lines

Editorial extensions of the paper, not claims the author makes directly.

  • Editorial inference: all simulated first stages are linear in the instruments, so nonlinear methods are never evaluated in a regime where their flexibility could capture genuine nonlinear signal; a nonlinear first-stage DGP could reverse the ranking between flexible and linear methods.
  • Editorial inference: the decomposition suggests a practical diagnostic, since the first and third components, $\widehat{\mathrm{Cov}}(\hat{x}, e)$ and $\widehat{\mathrm{Var}}(\hat{x})$, can be computed from a researcher's own first-stage fit and used to detect the forbidden-regression and amplifier channels before trusting an ML-in-2SLS estimate.
  • Editorial inference: because the second bias channel depends on the algorithm recovering the endogenous part of $x$, the paper's guidance may shift with instrument strength and the degree of endogeneity; varying the concentration parameter and the endogeneity correlation would map where the bias ranking flips.
  • Editorial inference: the appendix's discussion of monotonicity and heterogeneous treatment effects suggests that with varying effects, nonlinear first stages may estimate a different weighted average of effects than linear 2SLS, a possibility the main text does not quantify.
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Editorial analysis

A structured set of objections, weighed in public.

Desk editor's note, referee report, and a circularity audit.

Referee Report

3 major / 5 minor

Summary. The paper studies what happens when a researcher replaces the linear first stage of 2SLS with an off-the-shelf machine learning predictor. It derives an exact finite-sample decomposition of the bias of the resulting second-stage estimator into three components: a term proportional to Cov(ẋ,e), where ẋ are first-stage fitted values and e are first-stage residuals; a term Cov(ẋ,u), where u is the structural disturbance; and a scaling factor 1/Var(ẋ). It then reports Monte Carlo results for two families of DGPs, one with seven strong instruments and a linear first stage, and one with one hundred instruments of varying strength and a linear first stage in three subcases. The headline finding is that linear machine-curated procedures (post-Lasso, PCA) perform as well as or better than OLS-based 2SLS, while nonlinear procedures (random forests, boosted trees, neural networks) can be substantially biased, in some cases more biased than an OLS regression that ignores endogeneity entirely. The paper also discusses the forbidden-regression interpretation, the need for strengthened exclusion restrictions when nonlinear functions of instruments are used, and the relationship to split-sample and synthetic-instrument estimators such as MLSS.

Significance. The bias decomposition in Eq. (11) is algebraically correct and useful: it isolates mechanisms that are often conflated in discussions of ML-based 2SLS, and it makes the forbidden-regression bias explicit. The simulation infrastructure is substantial: 1,000 iterations, several estimators, three high-complexity subcases, and an auxiliary set of exclusion-restriction-violation simulations in Figure 3. If the empirical ranking were robust, the practical guidance would be valuable, since applied researchers frequently consider whether to use ML first-stage predictions. The paper is also appropriately careful in several places, such as distinguishing the plug-in first-stage approach from split-sample and synthetic-instrument alternatives. However, the external validity of the central ranking is weakened by the fact that every simulated first-stage regression is linear, and there is at least one internal inconsistency between the summary statistics in Table 1 and the component decomposition in Table 2. These issues need to be addressed before the practical guidance can be taken at face value.

major comments (3)
  1. [3.1-3.2 and Abstract] All simulated DGPs have a linear first-stage conditional expectation: in the low-complexity case g_x(z) = Σ z_i, and in the high-complexity case x1 = πz + ε_v. Nonlinear methods are therefore evaluated only in settings where they cannot improve the true first-stage model, so their flexibility can only add variance or recover endogenous variation. Figure 3 and Appendix A.2 vary the structural error by adding k-way interactions of the instruments to u, but the first stage remains linear in every case. Consequently, the abstract's unqualified claim that 'nonlinear methods generate substantial bias in second-stage estimates, potentially exceeding the bias of endogenous OLS' is not supported as a general practical regularity. It is supported only for linear-first-stage worlds. To make the practical guidance robust, the paper should either simulate genuinely nonlinear first-stage DGPs (e.g., quadratic, threshold, or interaction terms) where flexible methods could in principle capture useful exogenous variation, or explicitly qualify the conclusions to the linear-first-stage setting.
  2. [Table 2 vs. Table 1] The component-decomposition table is internally inconsistent with the main results table for high-complexity case 1. In Table 1, column B reports means of 1.335 for naive OLS (bias 0.335), 1.058 for first-stage OLS (bias 0.058), and 1.562 for random forest with cross-validation (bias 0.562). Table 2, panel B reports corresponding bias entries of 0.22, 0.02, and 0.32. Since both tables are described as means over the same 1,000 iterations, these should agree to Monte Carlo error. The discrepancy is not a minor rounding issue; it is roughly 30-100 percent of the reported bias. This undermines the component-level claims for case 1 and needs to be reconciled, either by correcting the tables or by clarifying whether the 'Bias' column in Table 2 is a ratio of means rather than the mean of the per-iteration ratio.
  3. [3.2] The high-complexity DGP is internally inconsistent in its definitions of the concentration parameter and the variance of x1. The paper states that σ²_v = π′Σ_zπ and that this 'forces Var(x1)=1'. But with Var(z_j)=1 for all j, Var(x1) = Var(πz) + σ²_v = π′Σ_zπ + π′Σ_zπ = 2π′Σ_zπ, so imposing Var(x1)=1 requires π′Σ_zπ = 0.5, not σ²_v = π′Σ_zπ. Moreover, under the stated definitions the concentration parameter is μ² = nπ′Σ_zπ/σ²_v = n, so it cannot be set to 180 independently of the sample size. Because the high-complexity simulations are designed around a particular concentration parameter and a particular sparsity pattern, this definitional inconsistency affects the interpretation of all three high-complexity subcases. The authors should correct the definitions and verify that the implemented DGP matches the reported μ².
minor comments (5)
  1. [4.1] In Section 4.1, Lasso is listed among 'all four nonlinear ML-in-the-first-stage methods', but Lasso predictions are linear in the instruments; this is inconsistent with the abstract's classification of post-Lasso as a linear method and with the paper's own description of Class 3 in Section 2.2.
  2. [Eq. (5)] Equation (5) writes the wedge as f(β1Cov(ẋ,e), Cov(ẋ,u), 1/Var(ẋ)) with f non-decreasing in each argument, but the explicit formula in Eq. (11) shows that f is the product (a+b)c. It would be clearer to replace the informal f notation with the explicit expression.
  3. [Section 4.2] The sentence 'The knife-edge case where a=0 appears unlikely...' uses the symbol a before it has been defined in that subsection; the reader has to infer that a refers to β1Cov(ẋ,e).
  4. [3.2] There is a typo: 'Belloni et al. (2012)'s DPG' should be 'DGP'.
  5. [Table 2 caption] The caption says each cell is the mean across 1,000 iterations, but the discrepancy between the 'Bias' column in panel B and Table 1 column B suggests that the decomposition entries may not be computed on the same iterations or may summarize a nonlinear function of per-iteration components. The caption should state exactly how each column is aggregated.

Circularity Check

0 steps flagged · score 0.0 of 10

No significant circularity: the bias decomposition is an exact algebraic identity and the simulation results are self-contained, not fitted to the conclusions.

full rationale

The paper's central derivation, Eq. (11), is an exact algebraic identity: substituting the second-stage residual decomposition w = beta1 e + u into the OLS formula for the 2SLS estimator yields beta_hat = beta1 + (beta1 Cov(xhat,e) + Cov(xhat,u))/Var(xhat). This is a rearrangement of definitions, not an assumption about which estimators will perform well. The simulation results are generated from explicit DGPs with fixed structural parameters; no parameter is fitted to reproduce the bias ranking, and the reported bias components are measured outcomes of those simulations, not inputs that define the conclusions. The main limitation is external validity: every simulated first stage is linear in the instruments, so nonlinear learners are never tested in a regime where a nonlinear first stage would be correctly specified. The paper even acknowledges this bookending intent in Section 3, and the issue is a generalizability concern rather than a circular derivation. The paper also contains no load-bearing self-citations: the Belloni et al. DGP, the post-Lasso procedure, and the Chen et al. MLSS estimator are all external references, and the authors do not invoke any prior work of their own as the basis for their claims. The only notable labeling inconsistency is that Section 4.1 calls Lasso a 'nonlinear' method even though Lasso's first-stage predictions are linear in the instruments, but this mislabel does not reduce any derivation to its inputs. Overall, the derivation chain is self-contained and the conclusions are not equivalent to the assumptions by construction.

Assumptions & free parameters 5 free parameters · 4 assumptions · 0 invented entities

The central claims rest on simulation design choices: linear first-stage DGPs, strong instruments (mu^2=180), AR(1) correlation 0.6, a 0.7 coefficient decay, and 7 or 100 instruments. These settings are hand-chosen and not fitted to data. The bias decomposition itself is a pure algebraic identity and requires no free parameters. No new entities are introduced.

free parameters (5)
  • Concentration parameter mu^2 = 180
    Chosen by hand to create a strong but sparse first stage; results may depend on this value (Section 3.2).
  • AR(1) correlation rho = 0.6
    Chosen for the instrument covariance matrix in both DGPs; affects instrument collinearity (Section 3.1 and 3.2).
  • Coefficient decay factor = 0.7
    High-complexity DGP first-stage coefficients follow 0.7^0, 0.7^1, ... as in Belloni et al. (2012); chosen to set instrument strength pattern (Section 3.2).
  • Number of instruments = 7 (low), 100 (high)
    Chosen to represent low- and high-complexity settings; results may depend on this choice (Section 3).
  • True causal effect beta1 = 1
    Set to 1 across all simulations; affects the scale and sign of the beta1 * Cov(xhat, e) bias component (Section 3).
assumptions (4)
  • domain assumption The instruments z are valid: E[epsilon_y | z] = 0 and E[x1 | z] != 0.
    Validity is assumed in both DGPs; the simulations operate under ideal IV conditions, so the results concern bias from the estimation procedure, not instrument invalidity (Section 3).
  • domain assumption The first-stage conditional expectation is linear in z in both DGPs (gx(z) = sum z_i and x1 = pi z + epsilon_v).
    Both simulated first stages are linear; this drives the comparison and is the weakest assumption, since nonlinear ML methods are tested only where they cannot improve the true model.
  • domain assumption Homogeneous treatment effects (beta1 constant), removing LATE and monotonicity complications.
    Stated in Section 2.1 footnote 6; ensures differences across estimators are not due to different local average treatment effects.
  • standard math Standard probability and OLS algebra used in the decomposition.
    The decomposition in Equations (8) through (11) uses only algebraic manipulation of OLS formulas.

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Pith. "Pith review of Machine learning the first stage in 2SLS: Practical guidance from bias decomposition and simulation." pith.science (2026). https://pith.science/paper/FDTA5BZ6

@misc{pith2026250513422,
  author       = {Pith},
  title        = {Pith review of: Machine learning the first stage in 2SLS: Practical guidance from bias decomposition and simulation},
  year         = {2026},
  howpublished = {\url{https://pith.science/paper/FDTA5BZ6}},
  note         = {Machine review of arXiv:2505.13422}
}
abstract

Machine learning (ML) primarily evolved to solve "prediction problems." The first stage of two-stage least squares (2SLS) is a prediction problem, suggesting potential gains from ML first-stage assistance. However, little guidance exists on when ML helps 2SLS$\unicode{x2014}$or when it hurts. We investigate the implications of inserting ML into 2SLS, decomposing the bias into three informative components. Mechanically, ML-in-2SLS procedures face issues common to prediction and causal-inference settings$\unicode{x2014}$and their interaction. Through simulation, we show linear ML methods (e.g., post-Lasso) work well, while nonlinear methods (e.g., random forests, neural nets) generate substantial bias in second-stage estimates$\unicode{x2014}$potentially exceeding the bias of endogenous OLS.

Figures

Figures reproduced from arXiv: 2505.13422 by the authors.

Figure 1
Figure 1. The “high-complexity” DGP: 100 instruments of varying strength Order of instruments’ coefficients (π) (A) Subcase 1: ‘Shuffled’ coefficients 0.00 0.25 0.50 1 25 50 75 100 Instrument number (z i ) Coefficient (πi) (B) Subcase 2: Coefficients decline from z1 0.00 0.25 0.50 1 25 50 75 100 Instrument number (z i ) Coefficient (πi) (C) Subcase 3: Coefficients decline from z50 0.00 0.25 0.50 1 25 50 75 100 Instrument numb… view at source ↗
Figure 2
Figure 2. Main results—βˆ distributions across competing two-stage methods (A) Low-complexity case: 7 strong instruments "Oracle" model Naive OLS First stage: OLS LIML (Fuller) Split-sample IV Jackknife IV (JIVE) First stage: PCA First stage: Post-Lasso selection First stage: Lasso selection First stage: Neural net, shallow First stage: Neural net, narrow First stage: Neural net, unrest. First stage: Boosted trees First stage… view at source ↗
Figure 3
Figure 3. Exclusion-restriction violations via higher-order interactions among instruments (‘low-complexity case’ of 7 strong instruments) (A) ‘Standard’ linear estimators: OLS, LIML, SSIV, and JIVE 0.5 1.0 1.5 2.0 2.5 1 2 3 4 5 6 7 Level of interaction of instruments in structural error term Estimate Naive OLS LIML (Fuller) Split-sample IV Jackknife IV (JIVE) (B) ‘Selection’ methods: Lasso, post-Lasso, and PCA 0.5 1.0 1.5 2.… view at source ↗

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Pith tools

Reviewed August 15, 2026 · model on record in the stance chip above.