How the Evidence Separates Price from Access
To understand whether state rate caps changed access to credit, the key evidence is not only the legal text but a set of quarterly household credit records. This chapter focuses on how the New York Fed study turns those records into comparisons across risk groups and time, so readers can distinguish an access proxy from a direct observation of lending and a carefully designed estimate from a simple before-and-after change.
What the credit records can—and cannot—show
The study uses the Federal Reserve Bank of New York Consumer Credit Panel, built from Equifax data. It is a 5 percent random and anonymized sample of American households tracked by the credit bureau. The observation period runs from the first quarter of 2015 through the fourth quarter of 2022. That window gives the researchers several quarters before the first rate-cap event and several quarters after the final event, allowing them to look for both pre-existing trends and post-policy changes.
The data are organized around three outcomes. Debt is the household’s outstanding balance, excluding mortgage and student-loan debt. It captures the intensive margin: how much credit a household has outstanding. Accounts is the number of open credit accounts, with the same exclusions. It captures the extensive margin: how many credit relationships remain open. Delinquent indicates whether the household has any account at least 90 days past due in a given quarter. That measure offers one window into financial stress and repayment performance.
These outcomes answer different questions. A lower balance could mean that a household borrowed less, paid down debt, lost an account, or moved to a source not captured in the relevant category. A lower account count more directly suggests a reduction in open credit relationships, but it still does not reveal whether an application was rejected or whether a household chose not to apply. A delinquency indicator can show whether repayment trouble changed, but it does not measure the interest rate paid, the total cost of borrowing, missed needs, informal debt, or the household’s broader welfare.
Using the two credit measures together makes the interpretation more disciplined. If balances fall while account counts remain stable, the change could reflect smaller balances or repayment on existing accounts. If both balances and accounts fall, the evidence is more consistent with a reduction in the number of active credit relationships as well as the amount borrowed. If balances rise without a comparable increase in accounts, existing borrowers may be carrying more debt rather than more households gaining access. None of these patterns, by itself, identifies the lender’s decision or the borrower’s reason for changing behavior. They are complementary signals, not interchangeable definitions of access.
Delinquency is deliberately kept separate from those signals. A household can have fewer accounts and still remain delinquent on one of them. It can borrow more without becoming delinquent during the observation window. It can also avoid a new delinquency by cutting consumption or finding an unobserved source of funds. That is why a policy evaluation that reports only balances, only account counts, or only repayment trouble can miss an important part of the outcome.
The study therefore treats credit balances and account counts as useful measures of credit provision, not as a complete census of credit access. The data do not identify the lender behind every account, the exact product, the rate offered, an application that was denied, or funds borrowed from family and other informal sources. They also do not identify whether a household would have borrowed in the absence of the cap. Those are not minor technical omissions: they define what conclusions the estimates can support.
The researchers divide households by Equifax Risk Score 3.0, which ranges from 300 to 850 and rises with creditworthiness. For households in the treated states, the risk-score deciles are based on the four quarters before the state’s limit took effect. For households in control states, the distribution is calculated over the sample period. The bottom decile is the study’s high-risk group. To investigate possible reallocation, the researchers then examine the second through fifth deciles against borrowers in higher deciles.
This grouping is a way to ask whether the policy affected households differently according to risk. It is not a claim that everyone in a decile is alike. A score summarizes credit risk; it does not record every feature of a borrower’s finances or every reason a lender makes a decision. The deciles are useful because they make a distributional pattern visible: if the bottom group moves in one direction and groups just above it move in another, an all-household average may conceal the distinction.
The timing of the grouping protects the comparison from a simple form of circularity. In treated states, the thresholds are set using the four quarters before the law, so a borrower’s post-law outcome does not determine which risk group they are being used to evaluate. The control-state distribution is defined across the sample period, which gives the researchers a stable way to classify those households in the comparison setting. These choices do not eliminate every source of selection, but they make the question clearer: how did borrowers who were already relatively risky before the intervention fare afterward?
The reference group also carries meaning. When the bottom decile is compared with higher deciles, the estimate is not asking whether high-risk borrowers changed in isolation. It asks whether they changed more or less than borrowers who faced the same broad period but were less exposed to a cap that binds at the margin. When deciles 2 through 5 are studied against higher-score borrowers, the comparison is designed to look for a different pattern: whether credit expanded for borrowers who were safer than the most exposed group but still close enough to the affected market to plausibly receive redirected lending.
The exclusions also matter. Mortgage and student debt are unlikely to respond to the studied consumer-loan caps because those products generally carry much lower interest rates. Removing them makes the measured outcomes more relevant to the market under investigation. It also means the findings should not be read as a statement about every form of household borrowing. The study is examining a defined slice of credit, observed through household-level records.
The study combines household records, state treatment timing, risk groups, and multiple outcomes; no single measure captures the whole access question.
How the comparisons make the policy visible
A raw before-and-after comparison would be weak evidence. Credit conditions can change because of the economy, local events, household aging, or other policies. A state that adopts a cap may also differ from a state that does not adopt one. If borrowing falls after a law takes effect, the decline cannot automatically be attributed to the law.
The study first uses a difference-in-differences comparison. It compares households in the three states that enacted limits with households in seven states that did not enact consumer usury limits during the study period. The relevant estimate is the change in the treated states after their laws take effect, relative to the change in the comparison states. This design removes some common movement over time and some persistent differences between places. It is more informative than asking only whether borrowing was lower after the law than before it.
The design still needs an assumption: absent the law, treated and control states would have followed sufficiently similar trends. The report examines event-study estimates before and after the intervention. Pre-policy estimates that are close to zero are consistent with the parallel-trends assumption, because they suggest that the groups were not already diverging in the outcome being studied. The assumption cannot be proven by a graph, but visible pre-trends would make the comparison less credible.
The researchers then add a risk dimension through a triple-difference design. Instead of looking only at all households in a treated state, they compare the bottom risk decile with other borrowers, and ask whether the relative difference changes after the cap. Household fixed effects account for stable differences across households. Zip-code-by-quarter fixed effects absorb local conditions that change over time, such as a local economic shock or a shift in the surrounding credit market. Borrower age is also controlled for because credit demand changes over the life cycle.
In plain terms, the estimate asks a more demanding question: did high-risk households in capped states change differently after the law than lower-risk households in those same changing local environments, and differently from the corresponding comparison in states without a cap? This does not turn the data into an experiment. It does, however, narrow the set of alternative explanations that a simple before-and-after comparison would leave open.
The never-treated control states are important in a staggered policy setting. South Dakota, Illinois, and North Dakota did not enact their laws at the same time, so the study must align outcomes around different dates. A group that never receives the treatment can provide a continuing comparison rather than becoming treated later and serving as a potentially confusing control for an earlier event. The authors note that this helps address concerns about interpreting staggered difference-in-differences estimates, although it does not remove every concern about policy timing or changing effects.
The first result illustrates why the level of aggregation matters. At the state level, the estimated change after the limits is small: total debt balances fall by about 0.9 percent and the number of accounts by about 0.6 percent. The study finds no change in delinquencies for the average borrower. Those estimates are compatible with a market that appears broadly stable. They are not evidence that every risk group remained stable.
There are two reasons an average can be quiet. First, many households may not have used the high-cost products directly affected by the caps. Their credit behavior can dilute the effect on the households most exposed to the rule. Second, a decline for one group can be offset by an increase for another. If the riskiest borrowers lose accounts while moderately safer borrowers gain accounts, the state-wide account total can move only slightly even though the distribution of access changes substantially.
A relative estimate is consequently different from a simple total. The study’s state-level coefficient does not say that every household lost roughly the same fraction of credit, nor does it report how much of the state’s lending capacity moved from one risk group to another. It summarizes the average difference between a treated setting and a comparison setting after accounting for the model’s controls. The subgroup estimate then asks whether a particular risk group moved differently from its comparison group. The two estimates answer different questions and should not be forced into one headline.
The fixed effects help with some confounding, but they do not make the groups identical. Household effects account for stable characteristics of the same households; zip-code-by-quarter effects account for local conditions at a particular time. They cannot automatically account for a policy campaign that was triggered by an unmeasured credit trend, a lender response that differs across states, or a change in borrowing that never appears in the credit-bureau data. The report’s evidence is strongest when the reader keeps the comparison and its assumptions visible.
The comparison therefore has a hierarchy. The state-level estimate tells us about the average change in measured household credit. The risk-group estimate tells us whether that average is hiding unequal effects. The event study tells us when those changes appear and whether treated and control groups looked plausibly similar beforehand. The outcomes themselves tell us different things about balances, open relationships, and delinquency. Reading one layer without the others invites overstatement.
The study’s robustness exercises reinforce this layered interpretation. The high-risk contraction remains similar when the authors exclude the COVID years, use only Utah and Wisconsin as controls, and compare changes within treated states. But the state-specific results are not identical: high-risk debt declines in Illinois and North Dakota but not significantly in South Dakota, and the account decline is significant in North Dakota but not in Illinois or South Dakota. The pooled result is informative about the common pattern in the sample; it is not a guarantee that every state experienced the same magnitude or every margin of change.
The same caution applies to reallocation. The pooled evidence is consistent with credit moving toward moderately safer groups, while separate-state reallocation estimates are not consistently significant, possibly because each state analysis has less statistical power. A robust pooled pattern and uncertain state-by-state estimates can coexist. What would change the conclusion? Evidence on lender-level originations, rejected applications, offered rates and fees, product substitutions, and the same borrowers’ access across institutions would help distinguish the mechanisms more directly.
For now, the design supports a disciplined reading. It can compare realized credit outcomes across risk groups and policy timing with controls for important household and local factors. It cannot observe every offer, denial, lender decision, or welfare consequence. That is enough to test whether rate caps have uniform effects. It is not enough to treat a state-wide average, or a single credit-bureau proxy, as the whole policy story. With that measurement framework in place, the sharpest result is the one hidden by the average: what happens to the riskiest borrowers themselves.