How the Study Separates a Merger Effect from a Misleading Average
For completed U.S. bank mergers, the key empirical question is not whether the combined institution’s reported mortgage average changed after the legal completion date. It is whether the merger changed the lender’s pricing, approval, or subsequent loan performance relative to what comparable lenders were doing in the same local market and period. This chapter follows the evidence chain behind that comparison and explains why a raw before-and-after average can move even when the underlying pricing rule does not.
That distinction is essential because a merger changes the identity under which loans are reported. Before completion, the acquirer and target have separate portfolios, borrower mixes, and business models. After completion, those portfolios may be recorded under one institution. A change in the combined average can therefore be a change in what is being averaged rather than a change in how either institution treats a comparable borrower.
From application record to loan history
The study begins with Home Mortgage Disclosure Act data, or HMDA. HMDA reports mortgage applications and originations from regulated financial institutions. Across the underlying records, the authors observe more than 350 million mortgage entries with information such as application outcomes, application and closing dates, loan amounts, and originator identities. That breadth matters because the study is not built from a small set of handpicked bank cases. It starts with a near-universe of reported mortgage activity, then links those records to information that follows a loan after origination.
HMDA is not literally every mortgage in the United States. Banks and credit unions can be exempt based on asset size and loan-volume criteria, and the reporting rules have changed over time. The study also drops observations missing key information about interest rates, applicant income, loan-to-value ratios, credit scores, amounts, maturities, rate type, mortgage type, occupancy, or repayment status. The resulting estimates are therefore based on a large, carefully filtered reporting universe, not on an assumption that the raw data are complete without qualification.
The second major input is the ICE McDash mortgage-servicing dataset. It supplies loan-level contract terms—including interest rates, loan-to-value ratios, and mortgage duration—and monthly performance information from origination through resolution. For mortgages originated between 1994 and 2023, the records can show whether a loan is refinanced, prepaid, delinquent, foreclosed, sold, securitized, or retained on the originator’s balance sheet. This transforms the question from “what rate did the lender quote?” into a broader sequence: what kind of loan was made, on what terms, and how did it perform afterward?
After the HMDA and McDash records are linked and incomplete cases are removed, the linked data contain approximately 62.6 million unique loans. The final quality-filtered sample contains approximately 44.3 million unique mortgages from 1994 through 2023. The difference between those two figures is informative. A large linked dataset does not eliminate the need to define a usable outcome, and the records retained for a rate or performance analysis are not necessarily all the records initially observed.
The third input supplies the institutional event. The Federal Reserve’s National Information Center database identifies acquiring and target institutions, transaction announcement and completion dates, pre-merger asset sizes, transaction types, and regulatory approval status. The authors identify 4,829 distinct merger events occurring between 1996 and 2021. To keep the institutional identity consistent over time, mortgage origination is aggregated at the bank-parent level. A parent-company crosswalk prevents a bank’s charters or subsidiaries from being treated as unrelated lenders when ownership has not actually changed.
These ingredients are assembled into different analytical views. The main event-study panel is organized at the merger–bank–county–quarter level. It follows acquiring banks, target banks, and control banks through a 17-quarter window: eight quarters before and eight quarters after completion. A separate county-quarter panel measures the local competitive environment, including bank and nonbank originators. The two panels answer different questions. The first asks whether a merging institution’s borrower-facing decisions changed relative to controls. The second asks whether the surrounding market itself became more or less competitive.
The treatment identity also needs care. During the event window, pre-merger observations for the target are assigned to the acquirer’s identifier. The treated bank–county cell is thus intended to represent the pro-forma combined entity throughout the window rather than abruptly switching identities at quarter zero. This construction gives the fixed effects a meaningful job: they absorb the persistent level of the bank–county–merger relationship, so the estimated post-merger coefficients focus on deviations from the combined baseline instead of mechanically comparing two separate portfolios with different starting points.
The design’s strength comes from the links between these inputs. HMDA alone would show application and origination behavior but not the full loan history. McDash alone would show contracts and performance but not the complete application decision or the merger identity in the same way. Merger records alone would establish that an institutional event occurred but not whether a borrower’s experience changed. The linked data make it possible to examine price, access, and performance around the same event.
The comparison is built to reject false before-and-after stories
A simple comparison would calculate a lender’s average mortgage rate before completion and compare it with the average afterward. That approach is easy to understand and often wrong for the question at hand. It mixes three things: changes in the borrowers or products being served, changes shared by the local market, and changes in the lender’s own behavior. The paper’s design tries to isolate the third.
For mortgage rates, the authors first construct a residualized rate. In plain language, they remove the portion of the observed rate associated with characteristics that reasonably affect pricing: applicant income, FICO score, loan-to-value ratio, mortgage amount, duration and term, whether the rate is fixed, the loan’s purpose and type, and occupancy status. They also absorb county-by-quarter conditions, such as local housing or credit-market movements that affect all lenders in that place and period. The residual is not a borrower’s full cost of homeownership. It is a way to compare the part of the contract rate left over after observable loan risk and local timing have been accounted for.
Approval rates and delinquency rates are handled differently. A denied application has no originated contract rate to residualize, and a pre-origination application cannot yet have a realized delinquency history. Those outcomes therefore enter the stacked difference-in-differences directly, with event-specific and bank–county–merger controls. The distinction prevents the analysis from pretending that one adjustment procedure fits every outcome.
The control group is local and contemporaneous. For each merger event, the treated lender is compared with other banks originating mortgages in the same county and quarter. Those lenders face many of the same local housing conditions, interest-rate environment, and demand shocks. If the treated institution and its controls were moving together before completion, then a later divergence is more plausibly associated with the merger than with a broad change affecting the whole county.
The stacked event-study expresses that comparison across time. Each quarter is measured relative to the completion date, with coefficients for the eight pre-merger and eight post-merger quarters. Bank–county–merger fixed effects absorb persistent differences between treated and control relationships. Calendar-quarter–merger fixed effects absorb common movements within an event, while event-time fixed effects account for systematic patterns associated with being a certain number of quarters from completion. The result is not simply “post minus pre.” It is the change for the treated entity relative to the change for comparable local lenders, within the event structure.
That design also makes a prediction testable. If an acquirer used the merger to gain market power in mortgage lending, the treated institution’s risk-adjusted post-merger rates should rise relative to controls. Approval and delinquency predictions are less mechanically directional: tighter credit standards could reduce approvals, while changed underwriting could either raise or lower later delinquency. The study therefore does not force every outcome into the same theoretical sign. It asks whether the data show a systematic divergence and whether that divergence is statistically distinguishable from zero.
The most important example is a large bank acquiring a community bank. Before the merger, the large acquirer’s residualized rate is slightly below the rate of local controls, while the community target’s rate is about 20–30 basis points higher. Once both portfolios are reported as one institution, the combined average can rise even if the large bank has not raised its own rate and the target has not changed its pricing.
Consider the paper’s illustration. Suppose the large acquirer originates 1,000 mortgages per quarter at a residualized rate of zero basis points. The community target originates 100 mortgages at plus 25 basis points. If both pricing patterns remain unchanged, the combined average is:
[ \frac{1{,}000 \times 0 + 100 \times 25}{1{,}100} \approx 2.3\text{ basis points}. ]
The reported average rises because a higher-rate portfolio has been added. That is not the same as the acquirer charging its original customers 2.3 basis points more, much less than the target charging every borrower 25 basis points more. The direction of the average movement is real; the interpretation of its cause is the issue.
There are at least three possible stories behind that movement. The first is mechanical averaging: the two existing portfolios are combined. The second is strategic repricing: the acquirer uses reduced rivalry to raise its own rates. The third is integration or customer migration: the acquirer applies a new policy to target borrowers, perhaps lowering some target rates while changing the composition of the loans observed under the combined name. A raw average cannot distinguish these stories.
The within-cell comparison addresses the first problem by asking whether the same bank–county relationship moved relative to its controls. The rate-distribution analysis provides another check: if the acquiring bank’s underlying distribution does not shift around the event, the average movement is less consistent with a broad strategic repricing. In the formal stacked difference-in-differences results, the post-merger rate coefficients are not statistically significant for community–community, large–community, or large–large mergers. The evidence is therefore consistent with composition and integration dynamics rather than a systematic exercise of mortgage market power.
This is also why the event window and sample filters are part of the reasoning, not administrative clutter. The study requires targets to have positive pre-merger market share in the county, excludes counties with multiple merger events in the window, removes merger-county combinations where the acquirer had no pre-merger presence, excludes control banks that experience a merger in that county during the window, and omits mergers completed during the 2007–2009 financial crisis. These choices reduce contamination and avoid confusing a merger with entry into a new market or an overlapping shock.
The remaining identification assumption is parallel trends. Before the merger, treated and control outcomes should evolve similarly in the absence of the transaction. The reported pre-merger coefficients are generally flat, which supports that assumption in the study’s specifications. But parallel trends cannot be proven for every unobserved outcome, and a clean pre-trend does not remove every concern about selection. Mergers differ in size, geographic overlap, business model, and motive. The estimates should therefore be read as average treatment effects over the selected events, not as one uniform effect that applies to every bank or borrower.
The design changes the standard a claim must meet. A rate chart showing that a combined lender’s average increased is a useful observation, but it is not yet evidence that the merger caused a pricing increase. To support that stronger claim, the movement would need to survive adjustment for borrower and loan characteristics, comparison with contemporaneous local lenders, the pro-forma identity construction, and the study’s event-time tests. Even then, the conclusion would concern systematic effects in the selected sample, not every individual contract.
The same discipline carries forward to approval and delinquency. A post-merger level difference may reflect who applied, what products were originated, or how a portfolio was assembled. The relevant test is whether the treated institution diverged from comparable local lenders after completion. Once that question is stated correctly, a stable average is no longer an unexplained absence of movement. It is the outcome of a comparison designed to distinguish a changed portfolio from a changed decision rule.