When a bank turns down a small firm's application for a green loan, it never learns what that firm would have done with the money. The firm drops out of the bank's records, and its later environmental performance is never written down anywhere the lender looks. A model trained on past approvals therefore learns only from firms that already looked safe, which are mostly large, well-documented ones. It goes on to reject similar small firms, and the gap in green financing between large firms and small and medium-sized enterprises (SMEs) widens. That gap is well documented in Chinese panel studies (Enhancing Sustainability Through Regional Integration; Can Agriculture-Related Enterprises' Green Technological Innovation Ride the "Digital Inclusive Finance" Wave?). Machine learning calls this the selective labels problem: the decision itself controls whether the outcome is ever seen. Administrative data linkage offers an obvious fix. Rejected firms still pay taxes, draw grid power, and appear in business registries, so their outcomes can be looked up in records held by other agencies.
The fix is not as clean as it looks, and this proposal is built around the reason. The linked record is a proxy, a convenient stand-in for the quantity we actually care about. Tax arrears are not loan default, and electricity use is not emissions. The linkage also fails unevenly. Matches miss or go wrong more often for informal, small, or recently relocated firms, which are exactly the resource-constrained firms whose exclusion we want to measure. Linkage therefore brings back two problems the field treats separately: proxy bias, and a second selection step. Our claim is that the right target is an estimator that treats the external record as a second, imperfect measurement channel. It would calibrate that channel on approved firms, where both the bank's own outcome and the linked trace are observed. It would model link failure explicitly, and it would spend a small audit budget on the strata where linkage is weakest. Where the calibration cannot be trusted to carry over to rejected firms, the estimator should report honest bounds instead of a single number.
Core Claim
Suppose an applicant has covariates $X$ and approval decision $D$. The bank-observed outcome $Y$, which might be repayment or a verified retrofit, is seen only when $D=1$. A linked external trace $W$, such as registry survival, tax filings, or grid consumption, is seen only when linkage succeeds ($L=1$), and $L$ may depend on firm size and formality. The identifying idea is that among firms with a successful link, the trace carries the same information about the true outcome whether or not the firm was approved:
$$P(Y \mid X, W, D=0, L=1) = P(Y \mid X, W, D=1, L=1).$$
This is a bridge assumption. It is weaker than "selection on observables" because the trace $W$ is allowed to absorb the unrecorded factors that drove the loan officer's decision. It is still not free, and Gap 4 of the file warns that this kind of transfer fails when resource strata behave differently. Our estimator has three parts. First, it fits the calibration $m(X,W) \approx E[Y \mid X,W]$ on the overlap set ($D=1$, $L=1$). Second, it reweights by an estimated probability of correct linkage, built from record-linkage match weights, so that firms that failed to link are not silently dropped. Third, it corrects any remaining bias with a design-based residual term on a small audit sample of rejected firms whose sampling probabilities are known:
$$\tilde{Y}_i = \hat m(X_i, W_i) + \frac{R_i}{\pi_i}\big(Y_i - \hat m(X_i, W_i)\big).$$
Here $R_i$ indicates that firm $i$ was audited and $\pi_i$ is its known audit probability. The final estimates are population averages or policy values computed from these pseudo-outcomes. When the audit budget is zero, we drop the point estimate and report partial-identification bounds whose width shows how far the bridge assumption is being stretched.
What is new is the combination: linkage as a source of labels for rejected units, with the linkage itself treated as biased and selective. Section 2 of the file finds no work that uses linkage to address selective labels, and none in corporate sustainability.
Relation to Prior Work
Several papers motivate the problem. Algorithmic Censoring in Dynamic Learning Systems shows that repeatedly retraining on one-sided feedback traps excluded groups. Long-term Fairness with Selective Labels proves that equality of opportunity computed only on accepted cases is identically zero. Adaptation and Challenges argues qualitatively that ESG scores track compliance staffing more than stewardship. Its argument is the reason we refuse to use disclosures as $Y$. The linkage literature shows how much single-source data can miss: more than 70% of trauma deaths occur before a patient reaches hospital (Differences in the epidemiology of out-of-hospital and in-hospital trauma deaths). We read this as evidence that rejected applicants' outcomes really do exist in other agencies' records. The file also stresses that linkage errors concentrate in vulnerable groups, and that is the failure mode we model.
The closest methods recover missing outcomes from inside a single dataset. From Biased Selective Labels to Pseudo-Labels (DCEM) imputes soft labels for untested patients with expectation-maximization and a causal regularizer. Characterizing Fairness Over the Set of Good Models Under Selective Labels (FaiRS) extrapolates labels for rejected cases across the set of near-equally accurate models. SELLF imputes labels inside a reinforcement-learning loop. All three infer the missing outcome from the selected units alone and depend on selection on observables. We bring in an external observation instead. Two other methods handle confounded selection with structural assumptions. Multi-decision-maker instruments (Learning with Selectively Labeled Data from Multiple Decision-makers) need quasi-random assignment to officers. Shadow variables (Efficient Causal Decision Making with One-sided Feedback) need completeness conditions that are hard to test. Our bridge assumption is a different and partly testable route, described in the decisive checks below, and we use officer leniency where it exists as a diagnostic, not as the identifying source.
The debiasing step reuses existing methods. Design-based supervised learning (Using Imperfect Surrogates for Downstream Inference, DSL) supplies the residual-correction pseudo-outcome. Multiwave predict-then-debias (M-estimation under Two-Phase Multiwave Sampling) supplies adaptive allocation of the audit budget across waves. The doubly robust estimator for automated phenotypes (Towards the Efficient Inference by Incorporating Automated Computational Phenotypes under Covariate Shift) supplies the no-harm guarantee we aim to inherit. That paper also constrains our design: it assumes the label-given-features relationship is invariant across strata, and we expect that to fail between approved and rejected firms. This is why we condition on $W$ and fall back to bounds. The δ-regret intervals of Predictive Performance Comparison of Decision Policies Under Confounding supply the form of our zero-audit bounds. We follow its observation that uncertainty cancels wherever the old and new policies agree.
Research Program
The work has three stages. The first stage builds the estimator and states its guarantees. We will show consistency under the bridge assumption plus correct modeling of either the calibration or the linkage propensity. We will show that design-based validity holds whenever the audit probabilities are known. We will derive bounds when the bridge is relaxed by a sensitivity parameter.
The second stage builds semi-synthetic testbeds where ground truth is known. We start from the real applicant pools in the Fintech loan dataset (42,777 applications) used by Chu et al. and the CommBank personal-loan data (7,414 applications) used by FaiRS. On top of these we simulate three things: an external trace whose relationship to repayment drifts with firm size, linkage failure whose rate rises for small and informal applicants, and approval rules confounded by an unrecorded "officer impression" variable. We build a sustainability analogue on the Chinese A-share panel (CSMAR/CNIPA). There we simulate a green-credit gate on listed firms. Patent counts serve as the deliberately biased proxy, and a simulated physical-emissions outcome serves as the truth.
The third stage is a field study, conditional on a data-sharing agreement. It would cover a regional bank's green-loan applications, approved and rejected, deterministically linked through corporate tax registry identifiers to tax filings, business-registry closures, and grid consumption. A funded audit of a sampled set of rejected firms would provide gold-standard outcomes. We flag this stage as dependent on access. The first two stages stand on their own.
Baselines
The naive reference is to train and evaluate the allocator on approved firms only, and alternatively to treat rejected firms as negatives. FaiRS-style evidence and DCEM's own ablations show this is badly biased, and it fixes the size of the problem we must close.
The second baseline is naive linkage: use the linked trace $W$ as the label for every firm that links, and drop firms that do not. This is what a practitioner would do first, so it is the most important baseline to beat.
The strongest within-dataset imputation competitor is DCEM. On MIMIC-III Sepsis-3 it reports a median AUC of 0.620 against an oracle median of 0.633, and a median ROC gap of 0.030 on synthetic bias (From Biased Selective Labels to Pseudo-Labels). We pair it with FaiRS's interpolation-and-extrapolation imputation, for which no reported result was found on Lacuna for CommBank AUC or disparity.
For confounded selection, we run the shadow-variable efficient estimator of Chu et al. No reported numeric RMSE was found on Lacuna for the Fintech dataset; the paper reports only that its estimator had the lowest RMSE and standard deviation.
The strongest competitor overall is plain DSL with the same audit budget but without the linked trace or the linkage model. DSL reports restored 95% coverage and 14% to 31% lower RMSE than gold-standard-only estimation. For long-run allocation we also compare against SELLF, which reports a true disparity of 0.03 on FICO lending against an oracle of 0.05.
All methods receive the same applicant pool, the same audit budget and audit sample, the same model classes for nuisance functions, and the same hyperparameter search budget. Every method is scored on the full applicant population.
Two ablations isolate the key ingredients. The first removes the linkage-failure model, treating linked firms as representative. The second replaces SME-targeted multiwave audits with uniform random audits.
Beating the baselines means three things. Our 95% intervals for SME-stratum outcome rates must keep nominal coverage where naive linkage and the imputation methods do not. Our intervals must be at least 25% narrower than plain DSL at equal audit budget. A retrained allocator must close at least half of the gap in true policy value between the approvals-only model and the oracle, with SME approval disparity at or below SELLF's reported level.
Why not just…?
Why not just use the linked record as the label for everyone? If links were complete and the trace equaled the outcome, this would be optimal. Neither condition holds. DSL shows that a surrogate with 90% nominal accuracy can still drive 95% interval coverage down to 40% when its errors correlate with covariates. Firm size is exactly such a covariate for grid use and tax filings. Dropping unlinked firms also reintroduces selection, concentrated in SMEs. The naive-linkage baseline and the no-linkage-model ablation measure this cost directly. If naive linkage matches us in the semi-synthetic runs at realistic link-failure gradients, our contribution narrows to the zero-audit bounds, and we will say so.
Why not just impute rejected firms' outcomes inside the bank data, as DCEM or FaiRS do? These methods assume the bank's recorded covariates explain the approval decision. FaiRS states that extrapolating labels for rejected cases fails when officers use unrecorded judgment, and Chen et al. report that reweighting and extrapolation degrade sharply as confounding grows. Our testbeds vary the strength of the unrecorded "officer impression" variable. The prediction is that imputation methods degrade with it while our estimator does not, because $W$ is observed after the decision and reflects the firm's actual trajectory.
Why not just audit a random sample of rejected firms and run DSL or predict-then-debias? This is the real threat. With known audit probabilities, DSL is valid without any bridge assumption. Our answer is not that DSL is wrong. It is that audits of rejected SMEs are expensive, and DSL's efficiency depends on how good its surrogate is. The overlap-calibrated trace is meant to be a much better surrogate than anything inside the bank's records. Multiwave targeting adds to that; MPD reports gains of up to 1.8× effective sample size. If our interval widths at equal audit budget are not clearly smaller than plain DSL's, the linkage machinery does not pay for itself. In that case the proposal reduces to recommending DSL with linked covariates.
Decisive Checks
The first check tests the bridge assumption using only approved firms. Approved firms near the approval threshold resemble rejected ones. Where officer assignment varies, the most lenient officers' marginal approvals resemble them even more. If the calibration $\hat m(X,W)$ fitted on firms approved with a wide margin fails to predict outcomes for these marginal approvals, the bridge is suspect. In that case we report the bounds, not the point estimate.
The second check is coverage on the semi-synthetic testbeds as the size gradient in link failure varies from none to severe. The estimator should hold nominal coverage while naive linkage and DCEM drift.
The third check is the sustainability panel. Recovered SME green-outcome rates should track the simulated physical truth, not the patent proxy. This is the case where Enhancing Sustainability Through Regional Integration and similar patent-based studies would mis-rank firms.
If the field data become available, the final check compares the point estimates for rejected firms against the audited gold-standard firms that were held out from fitting.
References
- Enhancing Sustainability Through Regional Integration: A Quasi-Natural Experiment on Green Innovation of Listed Firms in the Yangtze River Delta
- Can Agriculture-Related Enterprises’ Green Technological Innovation Ride the “Digital Inclusive Finance” Wave?
- Algorithmic Censoring in Dynamic Learning Systems
- Long-term Fairness with Selective Labels
- Adaptation and Challenges
- Differences in the epidemiology of out-of-hospital and in-hospital trauma deaths
- From Biased Selective Labels to Pseudo-Labels: An Expectation-Maximization Framework for Learning from Biased Decisions
- Characterizing Fairness Over the Set of Good Models Under Selective Labels
- Learning with Selectively Labeled Data from Multiple Decision-makers
- Efficient Causal Decision Making with One-sided Feedback
- Using Imperfect Surrogates for Downstream Inference: Design-based Supervised Learning for Social Science Applications of Large Language Models
- M-estimation under Two-Phase Multiwave Sampling with Applications to Prediction-Powered Inference
- Towards the Efficient Inference by Incorporating Automated Computational Phenotypes under Covariate Shift
- Predictive Performance Comparison of Decision Policies Under Confounding