A practitioner’s guide to estimating general equilibrium amplification

This appendix first shows how household-level estimates can be translated into an implied effect on aggregate credit growth, facilitating comparisons between micro and macro estimates. We illustrate the calculation using DeFusco et al. (2020). The second part provides an overview of methods for measuring equilibrium amplification and moving closer to an estimate of the aggregate effect. Berg et al. (2021) provide a related guide.

C.1Calculating the implied micro effect

The object of interest is the change in annual aggregate credit growth, in percentage points, implied by estimated household-level responses. The calculation applies the estimated responses to a specified flow of new originations and normalizes forgone lending by the outstanding debt stock: $$\begin{equation*} \Delta(\text{credit growth}) \approx \frac{\Delta(\text{originations})}{\text{debt stock}}\times100. \end{equation*}$$ An important distinction is whether the calculation covers the market segment studied or extrapolates its responses to a broader market. The former measures the studied segment’s contribution to aggregate credit growth. The latter is a hypothetical exercise requiring an assumption about the applicability of the estimated responses outside that segment.

The calculation combines the extensive and intensive margins. Let $e$ denote the share of counterfactual originations eliminated by the policy, $s$ the share shifted to smaller loans, and $\Delta$ the average proportional loan reduction among shifted borrowers. Both $e$ and $s$ are measured relative to the same counterfactual market, including borrowers who no longer originate a loan. With annual origination volume $O$ and outstanding debt stock $B$, the implied effect is $$\begin{equation} \label{eq:microcalc} \Delta g \;\approx\; -\,\underbrace{\big[e+s\Delta\big]}_{\text{Extensive + intensive margin}} \,\frac{O}{B}\times100. \end{equation}$$(C.1) Because $s$ is measured relative to all counterfactual originations rather than only surviving borrowers, no additional survival adjustment is needed. If the estimated responses instead refer only to borrowers above the regulatory threshold, they must first be weighted by that group’s share of the relevant market.

Equation C.1 is exact only under the appropriate volume weighting. Bunching estimates typically identify shares of loans rather than shares of lending volume. Applying these shares to dollar originations therefore assumes that the counterfactual loan sizes of eliminated and shifted borrowers are adequately represented by the market average. Otherwise, the calculation requires separate average loan sizes for these groups.

An illustration using DeFusco et al. (2020). The authors study the US Ability-to-Repay/Qualified Mortgage rule introduced in 2014. The rule increased the regulatory cost of originating jumbo mortgages with debt-service-to-income ratios above 43 percent, while conforming mortgages were exempt. Their bunching estimates imply that 15 percent of counterfactual high-DTI jumbo loans were eliminated and another 20 percent shifted below the threshold. Expressed relative to the entire counterfactual jumbo purchase market, these shares are approximately 2 percent and 2.7 percent.

Following the authors’ extrapolation, we apply these jumbo-market responses to the full US purchase-mortgage market of $600 billion. For shifted borrowers, we use the paper’s illustrative 4.4 percent loan reduction. This is a calculation for a representative borrower above the threshold, not an estimate of the average reduction among borrowers who adjusted. The implied reduction in originations is $$\begin{equation*} \big[0.02+0.027\times0.044\big]\times\$600\text{bn} = \$12.71\text{bn}. \end{equation*}$$ Dividing by the $8.17 trillion mortgage stock reported by the Federal Reserve Bank of New York for end-2014 gives $$\begin{equation*} \Delta g \approx -\frac{12.71}{8{,}170}\times100 = -0.156\text{ percentage points}, \end{equation*}$$ or approximately $-0.16$ percentage points. The extensive margin accounts for approximately 94 percent of the total.

Four considerations matter when interpreting this exercise. First, the population to which the responses are applied must be explicit. Applying jumbo-market responses to all purchase originations assumes that the same proportional responses would occur outside the jumbo segment. Restricting the calculation to jumbo purchase lending would instead give the studied segment’s contribution to aggregate credit growth, which is much smaller.

Second, count shares and volume shares need not coincide. High leverage or high debt service relative to income does not, by itself, establish that affected loans are larger than average. Researchers should therefore report the relevant average loan sizes or explain the assumptions used to translate loan counts into lending volumes. The size of the intensive adjustment also needs to be distinguished from the share of borrowers adjusting: bunching identifies the latter more directly than the former.

Third, the debt-stock denominator must match the outcome used in the comparison. Household mortgage debt, total household credit, and total bank credit are different aggregates. A mortgage-stock denominator delivers an implied effect on mortgage credit growth. Comparison with macro estimates for a broader credit aggregate requires recalculating the effect using the corresponding stock.

Fourth, the horizon must be specified. Equation C.1 measures forgone lending over one year relative to a stated debt stock. Longer-run effects depend on subsequent originations, repayments, and whether excluded borrowers postpone their purchases or remain out of the market. For an exact contribution to annual credit growth, the denominator should be the beginning-of-year stock; the illustration above uses the end-2014 stock as an approximation.

The resulting number is a partial-equilibrium accounting exercise rather than an estimate of the full aggregate policy effect. It does not recover market-wide changes in house prices, lending conditions, or other equilibrium responses that the micro design does not identify. This limitation is related to the missing-intercept problem discussed by Wolf (2023). In the DeFusco illustration, extrapolation beyond the regulated segment introduces an additional assumption about external validity.

Nevertheless, reporting these calculations can make micro estimates easier to compare across studies and with macro benchmarks. Researchers should state the market covered, distinguish the studied segment’s contribution from any broader extrapolation, decompose the result into extensive and intensive margins, and report sensitivity to assumptions about loan sizes and the amount by which shifted loans shrink.

C.2Estimating general equilibrium amplification

To provide a full estimate of the total effect of a policy, researchers need to estimate the total effect, including any general equilibrium amplification usually removed by fixed effects. This section provides an overview of recent methods that try to estimate the total effect of a policy in different ways.

Before we discuss how recent studies have attempted to estimate general equilibrium amplification or spillovers, we need a precise definition of what we are after. The general equilibrium multiplier is the ratio of the total effect to the direct effect, for a stated outcome, at a stated level of aggregation, over a stated horizon. The evidence in Section 5.2.2 shows that this multiplier differs by outcome, that it differs by the state of the market, and that it is endogenous to the policy itself. For example, Acharya et al. (2022) estimate that equilibrium effects accounted for 94 percent of the cross-sectional credit response to borrowers’ distance from the Irish limits during the pre-introduction boom, but only 23 percent of the response to the limits themselves. This gives ratios of total to direct effects of roughly 17 and 1.3. The first number describes the credit and house-price feedback of the boom and the second the policy response, which is imprecisely estimated, and the authors caution that the decline cannot be attributed to the limits alone. In addition, the regional multiplier is different from the national multiplier, as discussed in Section 5.2.3, and will also differ depending on the monetary policy response (Chodorow-Reich 2019). A claim about “the” multiplier should therefore always say the multiplier of what, where, and when.

Direct estimation of the multiplier. The most immediately feasible approach requires no data beyond what existing micro studies already use. Suppose the outcome of household $i$ in market $m$ depends on its own exposure to the constraint and on an equilibrium object that is a function of average exposure in the market. When spillovers are homogeneous and linear, and own and market-average exposure are unrelated to household-specific trends and to other local shocks, a single regression of the outcome on own exposure and on the leave-out mean of exposure among other units in the same market, with time fixed effects, recovers both objects at once (Huber 2023): $$\begin{equation} \label{eq:huber} y_{imt} = \alpha_i + \delta_t + \beta\,(E_i \times \text{Post}_t) + \gamma\,(\bar{E}_{-i,m} \times \text{Post}_t) + \varepsilon_{imt}, \end{equation}$$(C.2) where $E_i$ is the household’s pre-policy exposure and $\bar{E}_{-i,m}$ is the mean exposure of other households in market $m$. The direct effect is $\beta$, the spillover is $\gamma$, and the ratio of total to direct effects is $(\beta+\gamma)/\beta$. Because $\delta_t$ absorbs effects common to all markets, this ratio is a regional rather than an aggregate multiplier. Bäckman and Khorunzhina (2024), studying the introduction of interest-only mortgages in Denmark, estimate within-municipality spillovers from payment-constrained to leverage-constrained households through house prices using a design similar to this.

The equivalent two-regression version estimates the within-market effect under market-time fixed effects and then re-estimates on data collapsed to the market level with time fixed effects only, recovering the multiplier as the ratio (Mian et al. 2026). Acharya et al. (2022) implement this comparison for the Irish limits. The two procedures are closely related, although they coincide only under equal market weighting and homogeneous effects. The one-regression version of Huber (2023) delivers a standard error on the spillover directly, whereas inference on the multiplier itself requires the joint uncertainty of the total and direct estimates.

In practice the design requires three construction choices. The market definition should correspond to where the equilibrium object lives, which for housing spillovers means a local housing market such as a county, municipality, or commuting zone. The exposure measure should be defined before the policy, from the pre-reform distance to the limit or a prediction of violation based on pre-reform characteristics. Finally, the specification should be estimated on the same outcome, instrument, and horizon as the partial-equilibrium estimate to allow for the comparison.

Diagnostics. Huber (2023) shows that the leave-out-mean regression is biased when there are omitted spillover types, nonlinear direct effects, or measurement error. The decomposition is valid when spillovers are homogeneous and thus affect treated and untreated units alike. In that case, market-time fixed effects absorb the spillovers for the individual unit, and removing the market-time fixed effect estimates the effect with the spillovers included. However, this is a hard assumption to fulfill, especially for mortgage constraints. Berg et al. (2021) show that homogeneity fails when the treatment acts as a binding constraint. Imagine, for example, a policy that loosens the LTV constraint, which creates spillovers to the untreated units through increases in house prices. Treated households at the LTV constraint will not be able to respond to rising house prices in the same way as the untreated households, as they are bound by the collateral constraint. More generally, a household at its borrowing limit cannot respond fully to a market-level spillover, which the unconstrained neighbors can. In this case, Berg et al. (2021) show that fixed effects can amplify rather than remove the bias, although this is not always the case. Berg et al. (2021) recommend estimating the outcome as a function of the share of exposed households in the market separately for exposed and unexposed households, without market fixed effects, and plotting the two fitted lines together with the market average.

Huber (2023) adds a complementary test: the estimated spillover should be smaller for units less exposed to a hypothesized channel. A spillover that is equally large for less exposed units is likely to be mechanical. Under an LTI limit, for example, the collateral channel is absent, so the house-price spillover on credit should be weaker for LTI-constrained than for LTV-constrained households. Huber shows that omitted spillover types, nonlinear direct effects, and measurement error in exposure can all produce such mechanical bias, and that additional leave-out means for other channels, flexible functional forms, and an instrument for own exposure that is uncorrelated with the exposure of others can address it. The direction of the resulting bias in the multiplier depends on which group the spillover affects most. If lower prices reduce borrowing more among comparison households than among exposed households already at the limit, the within-market gap understates the direct effect and the multiplier is overstated. If the spillover falls mainly on exposed households, as with the collateral feedback under an LTV limit, or if lower prices draw new buyers into the comparison group, or if lenders reallocate credit toward the comparison group, as the Irish evidence documents, the gap overstates the direct effect and the multiplier is understated.

Interpreting the output. The interpretation of the results depends on several factors that researchers ought to be aware of. First, when several spillover channels operate at once, a likely case when it comes to mortgage constraints, a single leave-out mean does not isolate each type of spillover, and cross-market channels contaminate the comparison across markets as well as within them. For example, mortgage constraints can plausibly generate spillovers through local housing demand, lender balance sheets (Loutskina and Strahan 2015), and the rental market (Castellanos et al. 2024).

Second, idiosyncratic, within-market measurement error in exposure attenuates the within-market coefficient more than the market-level one, because aggregation averages it out, and therefore inflates the ratio of the total to direct effects. Error in the market-level component of exposure biases the ratio in the opposite direction (Mian et al. 2026). Predicted-treatment designs guarantee some mis-measurement, since households respond with family transfers, cheaper properties, or different contract terms (Tzur-Ilan 2023).

Third, the output is a regional multiplier, not the missing intercept. National equilibrium responses, including the policy rate, system-wide credit reallocation, and the regulator’s reaction, sit in the time fixed effects. Mian et al. (2026) show that regional amplification and aggregate dampening can coexist. A researcher interested in the national multiplier needs to turn to alternative approaches, with their own caveats and difficulties. We turn to these next.

Alternative approaches. Two alternatives do not rely on the within-market comparison and therefore avoid the contamination just described, although each carries assumptions of its own. The aggregate component can be recovered from regional data directly, either by combining a regional VAR with factor analysis (Sarto 2025a) or by estimating local and aggregate effects jointly in a Bayesian framework that treats micro estimates as priors (Matthes et al. 2025). Where mortgage lending is concentrated among a few lenders, as it is in most countries that have adopted these policies, the idiosyncratic shocks of large lenders can be aggregated into an instrument for aggregate outcomes (Gabaix and Koijen 2024; Baumeister and Hamilton 2023). This is one of the few designs available when the policy variation is purely national and there is no cross-section to exploit, although it identifies propagation from a lender shock rather than from the policy itself.

Another approach is to try to estimate a single structural parameter that governs the spillover. For housing, Greenwald and Guren (2025) identify the degree of market segmentation as an important parameter that governs how credit affects house prices and thus generates spillovers. The degree of market segmentation is identified by the ratio of the price-rent response to the homeownership response to an identified credit shock (Greenwald and Guren 2025). It has been estimated for the United States alone, and estimating it in the countries that supply the micro evidence would discipline the micro-to-macro extrapolation more than any additional household-level estimate.

The source of the amplification. For a researcher interested in identifying the source or mechanism behind the spillover, the mediation approach of Sarto (2025b) addresses that directly. The approach exploits the fact that the housing channel propagates within geographically segmented markets while the intermediary channel propagates over lender networks that span them. Estimating the source requires loan-level data with lender identifiers, which exist in several of the countries that supply the micro evidence, but it has not yet been applied to a policy shock.