How Do We Know the Loan Changed the Outcome?
The SBA disaster recovery loan has a plausible bridge mechanism, but plausibility is not evidence that the loan caused a firm to survive. Businesses that receive credit may already be stronger, better connected, or more likely to recover; loan officers may also direct funds toward firms that appear especially damaged. This chapter explains how the Census study builds a counterfactual using owner FICO thresholds, what its long-run estimates establish, and where those estimates stop. The goal is to read a large effect as a disciplined causal result rather than as a reward assigned to “good borrowers.”
The counterfactual question is straightforward even when the method is not: what would have happened to a similar applicant facing the same disaster if the loan had not been approved? The answer cannot be observed for the same firm at the same time. It must be approximated with firms whose pre-disaster situations are close enough that a rule-driven difference in approval is the main meaningful difference between them. That is what allows the study to connect a loan to later outcomes rather than merely connecting financial health to the fact of borrowing.
Approval Is Not a Neutral Comparison
Suppose we compare every firm that received a disaster loan with every firm that did not. The result would mix several forces. A lender may approve firms with better credit and stronger pre-disaster cash flow because they are more likely to repay. That selection would make the loan look more effective even if the money itself changed nothing. But the reverse selection is also possible: a loan officer may use discretion to direct funds toward firms with severe damage or urgent need. That could make recipients look weaker than nonrecipients, understating the benefit of the loan.
The problem is not solved by adding more observable characteristics. Some differences are difficult to measure: the quality of a repair plan, the owner's persistence, an unrecorded relationship with a supplier, or the exact condition of a local market. A credible comparison needs a source of variation in approval that is close to arbitrary with respect to those underlying recovery prospects.
The study uses the owner's FICO score because the SBA's underwriting process included score thresholds. Around a threshold, two applicants can have very similar scores and other characteristics, but the probability of approval changes sharply when one score is just above the line and the other is just below it. The score does not become economically meaningful in a sudden way at that exact point. The discontinuity comes from the program's rule for approving loans.
The researchers identify 22 threshold-by-year natural experiments. The thresholds vary across time and geography, covering 13 FICO thresholds over 12 years and 916 natural disasters. In the combined sample, businesses just above the relevant threshold were about 12 percentage points more likely to be approved. Applicants are compared within a 29-point band around each threshold, which keeps the comparison local enough that firms on either side are plausibly similar while providing enough observations for analysis.
Using many thresholds matters. A result based on one cutoff could describe a narrow group of borrowers or an unusual underwriting rule in one year. The study instead combines threshold changes that ranged from FICO scores of 540 to 780 over the sample period. That broadens the set of applicants represented in the estimate, while the comparison remains local within each threshold. The trade-off is important: pooling does not turn the design into a random sample of all firms. It makes the causal evidence broader than a single cutoff, but still conditional on applicants near the program's identified boundaries.
This is easier to understand as a lottery with a biased ticket boundary than as a general credit-score ranking. The applicants are not randomly selected from all businesses in the country. They have applied for a disaster loan and are close to a threshold used in their particular period. But among those nearby applicants, crossing the rule's boundary changes approval probability without necessarily changing the underlying damage or entrepreneurial ability. The threshold supplies the variation; the research design estimates what the approval variation did to later outcomes.
The study combines that approval variation with observations of firms before and after the disaster. It follows firms for five years before the event and up to seven years afterward, using the pre-disaster period to check whether the groups were already moving along different paths. In statistical terms, approval is instrumented by being above the threshold, and the outcome is compared across the post-disaster period relative to the pre-disaster period. The important intuition is simpler: the study asks whether firms that were nearly alike before the shock diverged after a rule-driven difference in access to the recovery loan.
The first stage of this design is the approval jump. The second stage asks what the approval-induced difference did to outcomes. Keeping those stages separate prevents a common mistake: treating a firm's FICO score as the treatment and the later result as a direct consequence of credit quality. The study is not saying that firms with high scores naturally fare better. It is using a score rule to create a change in loan access, then tracing the consequences of that change.
The estimate also concerns approval rather than a universal promise that every approved firm will borrow or experience the same effect. Some approved applicants did not take up the loan, so the paper interprets the design as an effect of approval induced by the threshold, with take-up treated as orthogonal near the cutoff. That is a subtle but important boundary: the result is about the businesses whose access was changed by this institutional rule, not about a hypothetical program that forces every firm to accept debt.
Checks, Outcomes, and the Meaning of Persistence
A threshold design is only persuasive if firms cannot manipulate their position around the cutoff and if other relevant characteristics do not jump at the same point. The researchers find no evidence of bunching or manipulation in the score distribution. Firm characteristics and pre-disaster financial outcomes are continuous around the threshold, including private debt balances before the disaster. They also find that approval rises at the thresholds across the individual natural experiments, rather than appearing only after data are pooled.
Each check addresses a different failure mode. If applicants could adjust their reported score or timing to cross the line, firms above it might be systematically different. If baseline characteristics jumped at the cutoff, the later outcome difference could be caused by those characteristics instead of the loan. If the approval effect appeared only after aggregation, a few unusual disasters could be driving the pooled result. The reported continuity and repeated approval jumps do not prove perfect comparability, but they make these alternative explanations less credible.
The event-study structure supplies another check. If firms on the two sides of the threshold were already on different recovery trajectories, their outcomes should diverge before the disaster. The study finds no evidence of pre-trends for the main credit outcomes. That does not prove that every unmeasured characteristic is identical, but it makes a story of large pre-existing divergence less plausible. In evidence terms, the design earns a stronger causal interpretation by surviving several attempts to find a non-loan explanation.
The headline result is a substantial reduction in exit. Receiving a recovery loan reduces the probability of firm exit by 13 percentage points, compared with a post-disaster mean exit rate of about 21% for declined firms. The dynamic estimates show that the gap grows over time, reaching roughly 20 percentage points by seven years after the disaster. These are not two competing versions of the same number. The 13-point estimate is the study's baseline treatment effect over the relevant post-disaster period; the approximately 20-point figure describes the cumulative separation at a later event-time horizon. The difference reflects the timing of the effect, not an unresolved choice between sources or estimates.
That timing is central to the bridge question. If the loan only supplied cash to firms that would eventually fail, it might reduce exit in the first year and then produce a later wave of closures once the cash was exhausted. Instead, the estimated effect appears within a year and persists, with the gap widening over time. Persistence is not proof that every surviving business became productive, but it weighs against the claim that the program merely concealed inevitable failure.
Bankruptcy offers a sharper measure of distress than exit alone. A firm can close for many reasons, including a voluntary decision to stop operating, while bankruptcy imposes costs on lenders and other parties. The loan reduces the chance of bankruptcy by 3.8 percentage points, an 86% reduction relative to the post-disaster bankruptcy rate of declined firms. The raw paths in the study show bankruptcy rising above its pre-disaster level for both groups, but rising less for approved firms. Emergency credit therefore did not make the shock disappear; it changed the probability that the shock would end in a particularly costly form of failure.
The credit-bureau outcomes point in the same direction. Recovery loans reduce the share of debt that is delinquent by 34 percentage points and reduce the average number of days late across financial and operating contracts by 35 days. The latter measure includes obligations such as leases and utilities, not only conventional loans. The estimates also survive a check that adds charged-off SBA loans directly to the delinquency measure. That matters because an apparent improvement could otherwise be an accounting artifact caused by SBA balances not appearing in ordinary credit-bureau records until charge-off.
Exit, bankruptcy, and delinquency are related but not interchangeable. Exit tells us whether the firm remains in the observed business population. Bankruptcy identifies a costly legal and financial failure. Delinquency shows whether obligations are being serviced on time. A loan could reduce one without reducing the others: for example, it might keep a business open while payments fall behind. The fact that all three distress measures move in a favorable direction is more informative than any one number, especially because the study also observes longer-run operating outcomes.
Other outcomes extend the causal picture beyond distress. Among survivor firms, employment rises by about 18%, roughly half a worker at the sample mean. For firms that were employers before the disaster, the estimated increase is about 45%, or around 2.25 workers, and revenue rises by about 100% of the mean. These estimates belong to different samples and measures: employment is observed among firms operating in the relevant year, and revenue is missing for many firms, especially nonemployers. They are evidence of real firm-level recovery in the study setting, not a guarantee of net employment growth across an entire region.
The survivor condition deserves attention. Employment is not observed in the same way for a firm that has exited, so the employment estimate describes operating firms rather than the entire original applicant pool. That does not erase the separate causal exit result, but it means the two estimates answer different questions. The exit result asks whether the business remains; the employment result asks how many workers are attached to firms that remain observable. Combining them casually would overstate what either measure alone says.
The study also finds that recovery loans increase non-SBA private debt by nearly $18,000 and paid-on-time private balances by about $16,000. That result belongs to the next part of the argument because it helps explain how a government loan can coexist with healthier debt service. For present purposes, it is another reason not to judge the bridge solely by whether total leverage falls. A firm can carry more debt while becoming less delinquent if the borrowed funds restore the income needed to meet its obligations.
The evidence has a defined scope. The causal effect is a local average treatment effect for applicants near the identified FICO thresholds whose approval was changed by the rule. It is not a randomized estimate for every small business, every credit score, every loan size, or every type of crisis. The study's matched Census and Experian data also have coverage and measurement limits, and revenue is incomplete for a meaningful part of the sample. A strong design does not turn missing observations into evidence about firms that were never observed.
The public-cost calculations have a separate boundary. The authors estimate that each dollar loaned to businesses costs the government about $0.41, combining administrative expenses, the loan subsidy, and an assumed tax deadweight cost. They translate the employment estimate into roughly $53,000 in government cost per job and the employer-firm revenue estimate into about $87,000 per $1 million of new annual revenue. These are back-of-the-envelope calculations, not a full welfare analysis. Administrative costs are allocated using an assumption, the tax cost is contestable, and revenue is not the same as social surplus.
The causal conclusion is therefore strong but conditional. Near the SBA's approval thresholds, approval changed the long-run path of applicant firms: fewer exited or entered bankruptcy, debt was less delinquent, and surviving firms showed more employment, revenue, and private credit. The results support the proposition that targeted emergency liquidity can be a durable bridge. They do not establish that every emergency loan will have that effect, nor do they yet explain exactly why private lenders became more willing to extend credit. The next chapter follows the recipient firms through that financial and operating lifecycle.