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Dynamic Local Average Treatment Effects in Time Series
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{{ {\bf{JEL Classification}}: B41, C12, C32.\\ {\bf{Keywords}}: Compliers, Conditional inference, Exclusion, LATE.}} \\
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Economists work hard to extract plausibly exogenous variation in order to identify causal effects. Many identification strategies used in applied work either rely directly on instrumental variables (IVs) or can be reframed in terms of IV identification. This holds also in dynamic settings where, for example, external IVs may be constructed using a narrative approach or heteroskedasticity is exploited to yield additional identifying equations. Since imbens/angrist:1994, it has been well-known that IV-based approaches identify the local average treatment effect (LATE)\textemdash the average treatment effect for the sub-population of compliers, i.e., those whose treatment status is influenced by the policy intervention (the instrument).
In the LATE framework, the sub-population of compliers is unobserved. This means that although a LATE can be identified, the specific sample observations this effect represents is unknown. This limitation is often described informally as the inability to observe an observation's treatment status under both the intervention and non-intervention scenarios. From a practical interpretability perspective, this presents a challenge that has been widely discussed in the literature {[}see, e.g., angrist/imbens/rubin:1996, heckman:1996, imbens:2010 and robins/greenland:1996{]}. Some progress has been made by imbens/rubin:1997 and abadie:2003 who show that the proportion of compliers and some of their statistical characteristics can be identified, provided these characteristics can be expressed as functions of moments of the joint distribution of observed data. Using these results, bhuller/dahl/loken/mogstad:2020 conduct a detailed analysis of compliers in the context of interpreting IV estimates of the effect of incarceration on recidivism and subsequent labor market outcomes. Their work, along with many other studies, highlights the importance of identifying the (characteristics of) compliers when drawing policy implications.
This paper considers IV identification in dynamic settings and shows how compliers can be identified individually in this context. We first show that the notion of compliers can be equivalently rewritten in terms of an inequality involving the difference in means of the potential treatment under different instrument values. Under assumptions of continuity over time in the mean of the potential treatment assignment process\textemdash conditional on a fixed hypothetical value of the instrument\textemdash it is possible to recover counterfactual values by averaging observations in a neighborhood around a given time point.
For example, consider heteroskedasticity-based identification of the causal effects of monetary policy {[}cf. rigobon:2003 and nakamura/steinsson:2018{]} where the instrument indicates whether there was an FOMC announcement on each date in the sample and the treatment variable is equal to the variance of a short-term interest rate. Here compliers are defined as observations for which the volatility of the policy variable (change in short-term interest rate) increases if and only if there is an FOMC announcement. Suppose that there is an FOMC announcement on a given date of interest so that we do not observe the potential treatment assignment under the counterfactual instrument value indicating the absence of an announcement. Although the mean treatment assignment under non-announcement is unobserved at this date, it can be recovered if mean treatment assignments are a smooth function of time by computing an average of nearby days without an announcement. Under an additional assumption of deterministic complier status, the complier status of the date in question can be estimated and tested by comparing local means of the treatment variable, one corresponding to nearby dates for which an announcement occurred and the other corresponding to nearby dates for which it did not.\footnote{Even though we focus on a time series setting, our identification results immediately apply to cross-sectional settings with spatial data provided that the temporal distance between observations is interpreted as geographical distance, and analogous continuity assumptions are imposed over space.} Applying our identification results and tests to the heteroskedasticity-based identification of monetary policy effects, we find that about 75% of observations are compliers while the non-compliers are primarily concentrated in the early zero lower bound period, when the central bank could no longer lower interest rates and forward guidance was not aggressive.
Identification of compliers is not only valuable in its own right. It also enables us to test the exclusion restriction, a key condition for valid IV estimation that is typically untestable in practice. By identifying compliers, and thus also non-compliers, we show that the exclusion restriction can be tested using a $t$-test that compares the average outcomes of non-compliers across different instrument values.
A key condition for identification of the LATE in the IV framework is instrument relevance, entailing nontrivial correlation between the endogenous variable and the instrument. We begin by analyzing the problem of weak instruments, entailing low correlation between the endogenous variable and instrument, in empirical work through a survey of articles using IVs published from 2019 to 2022 in five leading journals: American Economic Review, Econometrica, Journal of Political Economy, Quarterly Journal of Economics, and Review of Economic Studies. Our sample includes 1,560 specifications from 18 papers, with 199 involving time series and 1361 involving panel data.\footnote{See the supplement for the full list of papers and inclusion criteria.} The left panels of Figure (ref) show histograms of full sample first-stage $F$-statistics for the specifications in our survey, truncated above 100 for visibility. Many $F$-statistics concentrate around the $\chi_{1}^{2}$ critical values and fall below the conventional thresholds of 10 and 23.1 suggested by staiger/stock:1997 and montielolea/pflueger:2013, raising serious concerns about weak instruments.\footnote{Indeed, staiger/stock:1997 derive the threshold of 10 under the homoskedasticity-only assumption\textemdash the relevant thresholds for time series data are larger {[}see montielolea/pflueger:2013{]}.} These findings align with those of andrews/stock/sun:2019, who analyze cross-sectional studies. For example, we find that 75% of time series and 72% of panel data specifications have first stage $F$-statistics below 24. The median $F$-statistic is 12.63 for time series and 9.29 for panel data.\footnote{For panel data specifications we consider each cross-sectional unit individually to enable comparison to our proposed time series test shown on the right panels.}
When identification fails or is weak, IV estimators can be severely biased for LATEs and conventional inference methods are rendered invalid. These problems have prompted extensive research on detecting weak instruments and constructing identification-robust confidence sets.\footnote{See, e.g., \textcolor{MyBlue}{Andrews et al.} andrews/moreira/stock:2006, kleibergen:2002, moreira:2003 and staiger/stock:1997.} However, there has been little work on estimation and inference in a general LATE setting when identification may be stronger over subsamples. The second main contribution of this paper is to develop a framework for identification, estimation, and inference on LATEs that accommodates time-varying instrument relevance. Within this framework, we propose a first-stage $F$-test to detect whether identification fails over all nontrivial subsamples. To solve the computationally intensive problem of searching for maximal identification strength among all possible sample partitions, we employ dynamic programming. This optimization is more complex than that in the structural break literature since evaluating identification strength requires more than comparing parameter changes across regimes.
In an attempt to understand the sources of weak IVs we plot the histograms of the $F^{*}$ statistic proposed in this paper (cf. Section (ref)) in the right panels of Figure (ref). The statistic $F_{}^{*}$ searches for the subsample with maximal identification strength among all possible subsamples of size at least $\pi_{L}T$.\footnote{We set $\pi_{L}=0.6$ in Figure (ref). We discuss the choice of $\pi_{L}$ below.} The idea is that while the IVs may appear weak in the full sample, they may be strong in a possibly large subsample. Figure (ref) shows that this is indeed often the case. The red vertical lines in Figure (ref) mark the $95^{th}$ percentile of the asymptotic distributions of the $F$ and $F^{*}$ statistics under the null of identification failure. Although its quantiles are larger, the $F^{*}$ statistics have substantially more mass in the upper quantiles of their null distribution. This has at least three implications. First, it confirms substantial time variation in the instruments' strength. Second, strong identification appears to be frequently present in a sizeable subsample even when the instruments appear weak in the full sample. The median $F_{}^{*}$ is 27.22 for time series and 33.81 for panel data specifications. These are substantially higher than their full sample counterparts and this difference cannot be simply attributed to the different null asymptotic distributions of the two test statistics given that the difference in the asymptotic critical values is relatively small while the empirical distributions of the two test statistics is markedly different. About one half of the specifications that appear to suffer from weak IVs in the full sample seem better characterized by strong IVs in the subsample with maximal identification strength. Third, the subsamples where instruments appear strong tend to be large. From an empirical perspective, this is encouraging: although weak instruments in the full sample are common, researchers can often succeed in identifying large subsamples where instruments appear strong.
Motivated by this survey evidence, we construct consistent estimators of LATEs when subsamples are strongly-identified. It is commonly believed that if IVs are strong only in some portion of the sample, the full sample IV estimator remains consistent for a LATE. We show that this belief is unwarranted unless the LATE of interest is time-invariant (i.e., homogeneous). If this condition fails, one can at best identify a LATE corresponding to the strongly-identified subsample. Even when the LATE is homogeneous, the full sample IV estimator may still be severely biased if instruments are irrelevant over parts of the sample.
Our approach differs from that of magnusson/mavroeidis:2014 and antonie/boldea:2018, who use time variation in IV strength to add moment conditions in a GMM context, enabling more efficient inference and estimation. In contrast, we exploit this time variation to identify the subsample where IVs are strongest and base our estimation on this subsample. This insight allows for consistent estimation even when subsamples suffer from identification failure.\footnote{Another major difference from magnusson/mavroeidis:2014 is that we address the computational challenge for the case of multiple breaks in the first-stage coefficient. magnusson/mavroeidis:2014 did not attempt to address this issue and refer to it as “computationally demanding”.} If the parameter of interest is heterogeneous, our estimator remains valid but is interpretable only within the strongly-identified sub-population.
We apply our methodology to the heteroskedasticity-based identification strategy used to estimate the causal effects of monetary policy from high-frequency data {[}e.g., nakamura/steinsson:2018{]}. The key identification condition for this strategy is that the volatility of the daily changes in short-term interest rates is higher on FOMC announcement days than on non-FOMC days. lewis:2020 provides evidence of weak full sample identification and shows that IV and GMM estimates even differ in sign. We find that identification is substantially stronger over a subsample comprising 80\textendash 90% of the data, with the excluded subsample centered around the financial crisis, during which volatility was high even on non-FOMC days. Estimation using the most strongly-identified subsample yields IV and GMM estimates that have the same sign and similar magnitudes. We recommend reporting the most strongly-identified subsample estimates in addition to the full sample estimates when strong full sample identification may be in question.
Although our new methods are able to find the most strongly-identified subsample, this subsample may still fail to be strongly-identified. For our final theoretical contribution, we develop identification-robust inference procedures using the most strongly-identified subsample. We propose versions of the Anderson-Rubin, Lagrange Multiplier, and conditional likelihood ratio tests, which depend only on this subsample. These tests are more efficient than their full sample counterparts, which include noise from regimes suffering from identification failure. When instruments are strong throughout the sample, our tests coincide with the conventional ones. When instruments are irrelevant over parts of the sample, our tests achieve higher efficiency by focusing on stronger segments. In the worst case, when IVs are weak everywhere, our methods are no less efficient than existing ones. While there is a trade-off between using fewer observations and more strongly identified subsamples, simulations show that our tests have higher power, indicating that the efficiency loss from a smaller sample size is outweighed by the gain in identification strength.
The paper is organized as follows. Section (ref) introduces the potential outcome framework and dynamic causal effects, and presents identification results. Section (ref) discusses issues pertaining to heteroskedasticity-based identification of monetary policy. Section (ref) presents an $F$-test for full sample identification failure. Estimation and inference robust to weak identification are discussed in Sections (ref)-(ref). An empirical application is considered in Section (ref). Section (ref) concludes. The supplements casini/mccloskey/pala/rolla_Dynamic_Late_Supp_Not_Online (casini/mccloskey/pala/rolla_Dynamic_Late_Supp_Not_Online, casini/mccloskey/pala/rolla_Dynamic_Late_Supp) include the Monte Carlo simulations, proofs and additional results.
A growing literature in macroeconomics uses IVs to identify dynamic causal effects when the policy variable of interest is endogenous.\footnote{See, e.g., gertler/karadi:2015, jorda/schularick/taylor:2015, mertens/olea:2018, mertens/ravn:2013, plagborg-Moller/wolf:2022, ramey/zubairy:2018 and stock/watson:2012 (stock/watson:2012, stock/watson:2018).} Many existing identification approaches can be reframed in terms of IVs, either derived from the modeling approach {[}e.g., heteroskedasticity-based identification as in rigobon:2003 and nakamura/steinsson:2018{]} or through external IVs constructed using a narrative approach {[}cf., olea/stock/watson:2021{]}. For example, romer/romer:1989 study the FOMC minutes to pinpoint dates when monetary policy actions were arguably exogenous. This allows the construction of exogenous variables that can be interpreted as IVs for some structural shock of interest.\footnote{See ramey/shapiro:1998 for unanticipated defense spending shocks, kuttner:2001, nakamura/steinsson:2018 and romer/romer:2004 for monetary policy shocks, hamilton:2003, kanzig:2021 and killian:2009 for oil market shocks, kanzig:2021_Carbon for carbon pricing shocks, romer/romer:2010 for tax shocks, and ramey:2011 for government spending shocks.}
We adopt a potential outcomes framework, as introduced by rubin:1974 and extended to time series settings by angrist/kuersteiner:2011 and rambachan/shephard:2021. Let the stochastic process $V_{t}=(Y_{t},\,X_{t},\,D_{t},\,Z_{t})$ be defined on the probability space $\left(\Omega,\,\mathscr{F},\,\mathbb{P}\right)$, where $Y_{t}$ is a vector of outcome variables, $D_{t}$ is a policy variable, $X_{t}$ is a vector of other exogenous and/or lagged endogenous variables, and $Z_{t}$ is a vector of instruments. Let $\vec{X}_{t}=\{\ldots,\,X_{t-1},\,X_{t},\}$ denote the covariate path up to time $t$, with analogous definitions for $\vec{Y}_{t}$, $\vec{D}_{t}$ and $\vec{Z}_{t}$. Let the policy-relevant information set at time $t$ denoted by $\mathscr{F}_{t}=\sigma(\widetilde{V}_{t})$ where $\sigma(\widetilde{V}_{t})$ is the $\sigma$-algebra generated by the history of $V_{t}$, $\widetilde{V}_{t}=(\vec{Y}_{t-1},\,\vec{X}_{t},\,\vec{D}_{t-1},\,\vec{Z}_{t-1})$.
Policy decisions depend on past observable variables and the contemporaneous outcome through a systematic component and on idiosyncratic information available to the policy-maker (i.e., the random component). The systematic component, denoted $D(\widetilde{V}_{t},\,Y_{t},\,Z_{t},\,t)$, is a time-varying non-stochastic function of the observed random variables $\widetilde{V}_{t}$, contemporaneous outcome $Y_{t}$, and the contemporaneous instrument $Z_{t}$. The idiosyncratic information is represented by a scalar stochastic shock $e_{t}$ that is not observed by the researcher. The policy action is determined by $D_{t}=\varphi(D(\widetilde{V}_{t},\,Y_{t},\,Z_{t},\,t),\,e_{t},\,t)$, where $\varphi$ is a general mapping. In a SVAR context, $e_{t}$ is the structural shock to the policy variable $D_{t}.$ For example, if the monetary authority follows a simple Taylor rule for the nominal interest rate, then $\varphi$ is linear and $\widetilde{V}_{t}$ includes inflation, output and the natural rate of interest.
We define two types of potential outcomes. The first, $Y_{t}\left(\left(\epsilon_{1:t}\right),\,\left(z_{1:t}\right)\right)$, denotes the counterfactual values of $Y_{t}$ under hypothetical sequences of the policy shocks $\epsilon_{1:t}$ and instruments $z_{1:t}$, where $a_{1:t}=\left\{ a_{s}\right\} _{s=1}^{t}$.
This definition excludes dependence on future shocks or instruments. The potential outcome process should not be confused with the observed outcome $\left\{ Y_{t}\right\} _{t\geq1}=\left\{ Y_{t}\left(e_{1:t},\,Z_{1:t}\right)\right\} _{t\geq1}$. For $h\geq0$ and any given $\epsilon$ and $z$, write the time-$t+h$ potential outcome along the path $\left(\left(e_{1:t-1},\,\epsilon,\,e_{t+1:t+h}\right),\,\left(Z_{1:t-1},\,z,\,Z_{t+1:t+h}\right)\right)$ as
where $Y_{t,h}\left(e_{t},\,Z_{t}\right)=Y_{t+h}$. Definition (ref) captures the property that $Y_{t,h}\left(\epsilon,\,z\right)$ also depends on policy shocks that occur between time $t+1$ and $t+h$. The notation $Y_{t,h}\left(e,\,z\right)$ focuses on the effect of a single policy shock on current and future outcomes akin to the idea underlying an impulse response. When the potential outcomes do not depend on the instruments, $Y_{t,h}\left(\epsilon,\,z\right)=Y_{t,h}\left(\epsilon\right)$, and for $\epsilon\neq\epsilon'$, $Y_{t,h}\left(\epsilon\right)-Y_{t,h}\left(\epsilon'\right)$ for $h=0,\,1,\,\ldots$ are the dynamic causal effects of a policy shock on the outcome. In a SVAR setting, one is often interested in these dynamic causal effects which are in fact the impulse responses.
The second potential outcome that we discuss, $Y_{t}^{*}\left(\left(d_{1:t}\right),\,\left(z_{1:t}\right)\right)$, is defined as the counterfactual values of $Y_{t}$ under hypothetical sequences of treatments $d_{1:t}$ and instruments $z_{1:t}$. The distinction with $Y_{t}\left(\epsilon_{1:t},\,z_{1:t}\right)$ is that this formulation focuses on causal effects of the policy variable $D$, not the policy shock $e$. For $t\geq1$, we assume that $d_{t}\in\mathbf{D}$, $z_{t}\in\mathbf{Z}$ for some sets $\mathbf{D}$ and $\mathbf{Z}$. In many applications outside SVARs, the causal effects of the policy are of interest. Think about the slope of demand functions, price elasticities, response coefficients or reaction functions of, for example, asset prices to monetary policy, and so on. Typically these causal effects are analyzed using event-studies, quasi-experiments, IV regressions, etc. The recent literature on causal effects in time series {[}e.g., rambachan/shephard:2021{]} focuses on the identification of causal effects of the structural shocks. In this paper, we consider identification of causal effects of the policy variable. We illustrate the difference between these two causal effects and an application to SVAR using the following two examples.
In the following, we discuss identification of causal effects of the policy via IV estimands.
We explicitly allow for endogeneity and rely on IVs. We assume that the instrument only has a contemporaneous effect on $D_{t}$ so that we may write $D_{t}=D_{t}(Z_{t})$ where $D_{t}(z)=\varphi(D(\widetilde{V}_{t},\,Y_{t},\,z,\,t),\,e_{t},\,t)$ is the potential treatment assignment at time $t$ when $Z_{t}$ is set equal to $z\in\mathbf{Z}$. The instrument $Z_{t}$ is assumed to be (conditionally) independent of the potential outcomes $Y_{t,j}^{*}\left(d,\,z\right)$ and treatments $D_{t}(z)$ but correlated with the observed treatment $D_{t}$.
Assumption (ref) states that, given $\widetilde{V}_{t}$, the instrument is as good as randomly assigned.
The second assumption is that potential outcomes $Y_{t,h}^{*}\left(d,\,z\right)$ are a function of $d$ but not of $z$. In studies of causal effects of monetary policy such as nakamura/steinsson:2018, $Z_{t}=1$ if there is an FOMC announcement on day $t$ and $Z_{t}=0$ otherwise. Then, potential realizations of expected output growth respond to changes in the monetary policy variable regardless of whether the change is associated with an FOMC announcement or not.
In a dynamic simultaneous equations model (e.g., a SVAR) the exclusion restriction requires the instrument not to appear in the causal equation of interest. In Example (ref), Assumption (ref) corresponds to condition (ii), i.e., $\mathbb{E}(Z_{t}\eta_{t})=0$ where $\eta_{t}$ is composed of the structural shocks other than $e_{t}$. Under Assumption (ref) we write $Y_{t,h}^{*}\left(d,\,z\right)=Y_{t,h}^{*}\left(d\right)$.
Identification based on IVs requires instrument relevance or “existence of a first-stage”. The latter means that $\mathbb{E}(D_{t}\left(z\right)|\,\widetilde{V}_{t})$ is a non-trivial function of $z$. In cross-sectional settings, the existence of a first-stage is typically assumed to hold for all units to guarantee strong identification. Strong identification of this form often fails to hold in applications involving time series data due to temporary misspecification, bad luck, rare events or parameter instability. The analysis based on articles in five leading journals that we report earlier suggests that there are time periods for which the first-stage exists (strong identification) and others for which it does not (identification failure). Standard first-stage $F$-tests are then likely to indicate weak identification since they are based on averaging these two sub-populations.
We provide a theoretical framework to address this identification problem by assuming that there are two sub-populations. One comprises a fraction $\pi_{0}\in\left[0,\,1\right]$ of the overall population for which the first-stage exists. For the second sub-population, which comprises a fraction $1-\pi_{0}$ of the population, the first-stage does not exist. This leads to a new notion of LATE, which we name $\pi$-LATE, the LATE for the (unknown) $\pi_{0}$ fraction of the population for which the first-stage exists. If $\pi_{0}=1,$ then one recovers LATE.
Denote by $|\mathbf{S}_{0,T}|$ the cardinality of $\mathbf{S}_{0,T}$ (i.e., the number of indices in $\mathbf{S}_{0,T})$.
Assumption (ref) implies that there are two sub-populations: one for which the first-stage exists and one for which it does not. An average treatment effect can only be identified via IVs for the fraction $\pi_{0}$ of the population for which a first-stage exists.
The next assumption is monotonicity which, under heteroskedasticity-based identification of monetary policy (see Section (ref)), means that while for some days the FOMC announcement does not coincide with higher volatility in the policy variable, all of those days in which the announcement affects the volatility of the policy variable, volatility is shifted up.
If $\pi_{0}=1$ (so $|\mathbf{S}_{0,T}|=T$), the condition reduces to that in imbens/angrist:1994.
Following kolesar/plagborgmoller:2025, we impose the following assumption.
Assumption (ref) allows $D_{t}$ to be either discrete, continuous or mixed. When $D_{t}$ is discrete or mixed, it is implicitly assumed that to deal with the gaps in the support of $D_{t}$ one extends $Y_{t,h}^{*}\left(\cdot\right)$ to $\mathbf{D}$ such that the extension is locally absolutely continuous. The support of $D_{t}$ is allowed to be unbounded. These conditions are weaker than counterparts imposed in the recent literature {[}cf. casini/mccloskey:2024 and rambachan/shephard:2021{]}, in particular local absolute continuity replaces differentiability of $Y_{t,h}^{*}\left(\cdot\right)$ plus bounded support of $D_{t}$. It allows the application of the fundamental theorem of calculus to $Y_{t,h}^{*}\left(\cdot\right)$ without requiring the support of $D_{t}$ to be bounded.
We first discuss the case of a discrete instrument. When the first-stage does not exist for all $t$, it is useful to define an IV estimand corresponding to the sub-population for which it does. Let the generalized Wald estimand be defined for all $z',\,z\in\mathbf{Z}$ by
where $\widetilde{v}\in\mathbf{V}$. This is the ratio of a reduced-form generalized impulse response to a first-stage generalized impulse response for $t\in\mathbf{S}_{0,T}$. We show that for $t\in\mathbf{S}_{0,T}$, the estimand $\beta_{\pi,t,h}\left(\widetilde{v}\right)$ identifies a weighted average of causal effects for the compliers. Recall that $t\in\mathbf{S}_{0,T}$ and $\pi_{0}$ are related by $|\mathbf{S}_{0,T}|=\left\lfloor \pi_{0}T\right\rfloor $. When $\pi_{0}=1$ and there is no conditioning on $\widetilde{V}_{t}=\widetilde{v}$, $\beta_{1,t,h}$ reduces to the Wald estimand considered by rambachan/shephard:2021. For $t\notin\mathbf{S}_{0,T}$, $\beta_{\pi,t,h}$ does not identify a causal effect because the denominator of (ref) is equal to zero.
We show that for $t\in\mathbf{S}_{0,T}$, the generalized Wald estimand is equal to a weighted average of marginal effects where the latter are the derivatives $\partial Y_{t,\,h}^{*}\left(d\right)/\partial d$.
Proposition (ref) shows that $\beta_{\pi,t,h}\left(\widetilde{v}\right)$ identifies a weighted average of causal effects for compliers, characterized by $D_{t}(z')>D_{t}(z)$, for observations with a first-stage, with weights $w_{t}\left(d|\,\widetilde{v}\right)$ determined by the (conditional) likelihood that $D_{t}\left(z\right)\leq d\leq D_{t}\left(z'\right)$. We refer to the average treatment effect on the right-hand side of (ref) as the time-$t$ $\pi$-LATE since it is the LATE for the observations in this sub-population, which is a fraction $\pi_{0}$ of the whole population. In practice, the IV estimand $\beta_{\pi,t,h}\left(\widetilde{v}\right)$ is characterized by two types of averaging. First, there is averaging over time. For any treatment $d$, the average involves only those observations whose treatment variable can be induced to change by a change in the instrument and is computed only over those observations that satisfy the first-stage (i.e., $t\in\mathbf{S}_{0,T}$). The second averaging is over different treatment values $d$ at the same date $t$. This is reflected in the weight $w_{t}\left(\cdot\right)$ which is proportional to the number of observations in $\mathbf{S}_{0,T}$ for which $D_{t}\left(z\right)\leq d\leq D_{t}\left(z'\right)$. Indeed, under regularity conditions permitting one to change the order of differentiation and integration, viz., \[ \mathbb{E}\left[\left.\frac{\partial Y_{t,\,h}^{*}\left(d\right)}{\partial d}\right|\,D_{t}\left(z\right)\leq d\leq D_{t}\left(z'\right),\,\widetilde{V}_{t}=\widetilde{v}\right]=\frac{\partial}{\partial d}\mathbb{E}\left[\left.Y_{t,\,h}^{*}\left(d\right)\right|\,D_{t}\left(z\right)\leq d\leq D_{t}\left(z'\right),\,\widetilde{V}_{t}=\widetilde{v}\right], \] $\beta_{\pi,t,h}\left(\widetilde{v}\right)$ can be interpreted as a local average marginal effect.
Stationarity of the conditional joint distribution of the average potential outcome and treatment assignment functions for observations with a first-stage lends further interpretability to the generalized Wald estimand. Specifically, if $\{Y_{t,h}^{*}\left(d\right),D_{t}(z)\}|\widetilde{V}_{t}$ is identically distributed across $t$ for all $t\in\mathbf{S}_{0,T}$, $d\in\mathbf{D}$ and $z\in\mathbf{Z}$, Proposition (ref), immediately implies that $\beta_{\pi,t,h}$ is equal for all $t\in\mathbf{S}_{0,T}$. Given this, we can write $\beta_{\pi,t,h}=\beta_{\pi,h}$, making explicit that the generalized Wald estimand (ref) equals a weighted average of causal effects for members of the sub-population with a first-stage, which represents a $\pi_{0}$-sized fraction of the total population. Under this assumption, we refer to the average causal effect inside of the integral as $\pi$-LATE since it is a LATE for a member of the $\mathbf{S}_{0,T}$ sub-population whose treatment variable can be induced to change by a change in the instrument.
The sample counterpart to the generalized Wald estimand (ref) involves replacing the conditional expectations with sample estimates based upon observations $t\in\mathbf{S}_{0,T}$, yielding an estimator of a causal effect. When Assumption (ref) holds with $\pi_{0}\in\left(0,\,1\right)$, the full sample estimand, i.e., the ratio of the time averages of the numerator and denominator of (ref), is a poor representative of the full sample average treatment effects because it includes observations for which the instrument is not relevant in the averaging. We caution that the usual practice of estimating the conditional expectations in (ref) with full sample estimates will not estimate the full sample LATE, but $\pi$-LATE.
angrist/graddy/imbens:2000 and rambachan/shephard:2021 consider related results in cross-sectional and time series settings. The difference here is that we do not require $D_{t}$ to be continuous or that the first-stage holds for all $t.$ kolesar/plagborgmoller:2025 established a similar result for the slope coefficient in the population version of the “reduced-form” regression of the outcome $Y_{t+h}$ onto $Z_{t}$ where they imposed no restriction on the first-stage and allowed for a continuous instrument.
A connection to program evaluation with binary policy actions arises when we map a dynamic problem with continuous variables into one with binary policy actions and instruments. For example, consider the analysis of causal effects of monetary policy using heteroskedasticity-based identification {[}cf. nakamura/steinsson:2018 and rigobon/sack:2003{]}. Define a binary instrument $Z_{t}$ with $Z_{t}=1$ if there is a scheduled announcement on day $t$ and $Z_{t}=0$ otherwise. The policy $\Delta i_{t}$ typically reflects changes in short-term interest rates. Identification relies on higher volatility in $\Delta i_{t}$ during announcement days (policy sample) compared to non-announcement days (control sample). Think about mapping $|\Delta i_{t}|$ into a binary treatment such that $D_{t}=1$ if $|\Delta i_{t}|\geq\delta$ for some threshold $\delta>0$ and $D_{t}=0$ if $|\Delta i_{t}|<\delta$ {[}cf. rigobon/sack:2003{]}. Here $\pi$-LATE captures the average treatment effect for the sub-population whose interest rate changes exceed $\delta$ only when there is an announcement (i.e., when $Z_{t}=1$). Observations where $|\Delta i_{t}|<\delta$ regardless of announcements are “never-takers,” while those with $|\Delta i_{t}|\geq\delta$ regardless of announcements are “always-takers.” Under monotonicity, these groups form the non-compliers, whose responses are driven by idiosyncratic factors other than announcement-specific effects. In Section (ref) we document regimes where the volatility of $\Delta i_{t}$ is high even in the absence of announcements.
sojitra/syrgkanis:2025 study dynamic treatment regimes with one-sided compliance where treatments in each period may depend on past instruments, treatments, outcomes, and confounding factors, while instruments in each period are generated based on prior instruments, treatments, and states. This setting encompasses applications such as digital recommendation systems and adaptive medical trials. Their focus is on the causal effect of treatment histories on long term outcomes, rather than of one-time shocks or single policy shifts on outcomes at horizon $h$. Under binary instruments and treatments, they establish nonparametric identification of the expected values of multi-period treatment effect contrasts for the corresponding complier subpopulations, which they refer to as dynamic LATE.
A practical challenge for the $\pi$-LATE framework, and LATE frameworks in general, is that the sub-population of compliers is unknown. However, in time series settings with binary instruments, we show below that one can identify the compliers individually, i.e., to determine whether each observation $t$ is a complier. In this section, we consider a binary instrument, e.g., $Z_{t}=1$ if $t$ is an FOMC meeting day and $Z_{t}=0$ otherwise. Under Assumption (ref), assume without loss of generality that $D_{t}(1)\geq D_{t}(0)$ for all $t$. Then, observation $t_{0}\in\mathbf{S}_{0,T}$ is a complier if and only if $D_{t_{0}}\left(1\right)>D_{t_{0}}\left(0\right)$ with probability one\textemdash if the treatment changes in response to the instrument.
We begin with the following assumption which states that each observation is either a complier or a non-complier with certainty.
Assumption (ref) rules out cases where $\mathbb{P}\left(D_{t}\left(1\right)>D_{t}\left(0\right)\right)=p$ for some $p\in\left(0,\,1\right)$. A non-complier cannot be characterized by $\mathbb{P}\left(D_{t}\left(1\right)>D_{t}\left(0\right)\right)>0.$ The latter probability must be zero. Under Assumption (ref), Lemma (ref) in the supplement shows that $\mathbb{P}\left(D_{t_{0}}\left(1\right)>D_{t_{0}}\left(0\right)\right)=1$ is equivalent to $\mathbb{E}\left(D_{t_{0}}\left(1\right)\right)>\mathbb{E}\left(D_{t_{0}}\left(0\right)\right)$. This equivalence implies that compliers can be identified by comparing the expected treatment values under different instrument values.\footnote{Note that this result is different from that in Lemma 2.1 in abadie:2003 who shows that under several assumptions the proportion of compliers can be identified by $\mathbb{E}\left(D_{i}\left(1\right)\right)-\mathbb{E}\left(D_{i}\left(0\right)\right)$ in a cross-sectional setting. He uses this lemma to show that any statistical characteristic that can be defined in terms of moments of the joint distribution of $\left(Y_{i},\,D_{i},\,Z_{i}\right)$ is identified for compliers. He then remarks that it is not possible to identify compliers individually under these assumptions.} Under mild smoothness assumptions that we discuss below, the latter two expected values can be estimated consistently from the sample so that we can determine whether $t_{0}$ is a complier in large samples by looking at the corresponding inequality based on sample quantities.
Let $\mathbf{P}\subset\{1,\ldots,T\}$ denote the “policy sample”, the set of observations for which $Z_{t}=1$ so that $D_{t}=D_{t}(1)$ for all $t\in\mathbf{P}$, and let $\mathbf{C}=\{1,\ldots,T\}\setminus\mathbf{P}$ denote the “control sample”, where $D_{t}=D_{t}(0)$. It is reasonable to assume that, for a given value of the instrument, the potential treatment assignments vary smoothly over time. Suppose we wish to determine whether an observation $t_{0}\in\mathbf{P}$ is a complier. Since $D_{t_{0}}\left(0\right)$ is not observed, under time-smoothness we approximate $\mathbb{E}\left(D_{t_{0}}\left(0\right)\right)$ by averaging nearby observations in the control sample. Letting $N_{0}(t_{0})$ denote the $n_{0}$ largest indices $s\in\mathbf{C}$ such that $s\leq t_{0}-1,$ this implies \[ \overline{D}_{C,t_{0}-1,n_{0}}\equiv n_{0}^{-1}\sum_{s\in N_{0}(t_{0})}D_{s}\overset{\mathbb{P}}{\rightarrow}\mathbb{E}\left(D_{t_{0}-1}\left(0\right)\right) \] as $n_{0}\rightarrow\infty$ with $n_{0}/|\mathbf{C}|\rightarrow0$ under mild conditions. In addition, it follows that $\mathbb{E}\left(D_{t_{0}-1}\left(0\right)\right)$ is close to $\mathbb{E}\left(D_{t_{0}}\left(0\right)\right)$. A similar argument can be applied to $\mathbb{E}\left(D_{t_{0}}\left(1\right)\right)$ using adjacent days in the policy sample: we have $\overline{D}_{P,t_{0},n_{1}}\overset{\mathbb{P}}{\rightarrow}\mathbb{E}\left(D_{t_{0}}(1)\right)$ as $n_{1}\rightarrow\infty$ with $n_{1}/|\mathbf{P}|\rightarrow0$, where $\overline{D}_{P,t_{0},n_{1}}=n_{1}^{-1}\sum_{s\in N_{1}(t_{0})}D_{s}$ and $N_{1}(t_{0})$ denotes the $n_{1}$ largest indices $s\in\mathbf{P}$ such that $s\leq t_{0}$. Thus, observation $t_{0}\in\mathbf{P}$ is a complier if and only if $\overline{D}_{P,t_{0},n_{1}}-\overline{D}_{C,t_{0}-1,n_{0}}\overset{\mathbb{P}}{\rightarrow}c$ as $n_{0},n_{1}\rightarrow\infty$ with $n_{0}/|\mathbf{C}|,n_{1}/|\mathbf{P}|\rightarrow0$ for any $c>0$.
Intuitively, even though $D_{t_{0}}\left(0\right)$ is not observed when $t_{0}\in\mathbf{P}$, observations close to $t_{0}$ characterized by no FOMC announcement provide information about what $\mathbb{E}\left(D_{t_{0}}(0)\right)$ would have been in the absence of an FOMC announcement.\footnote{One could also use the observations to the right of $t_{0}$ to construct $\overline{D}_{C,t_{0}+1,n}$, i.e., $D_{t_{0}+1},\ldots,\,D_{t_{0}+n}$.} There are about six weeks in between any two FOMC meetings, and so $n_{0}\approx30$. Alternatively, following nakamura/steinsson:2018 the control sample could include all Tuesdays and Wednesdays that are not FOMC meeting days. Nevertheless, one can skip the observation that pertains to the previous meeting, say $D_{t_{-1}}\left(0\right)$, whose realization is not observed, and continue averaging using the observations prior to that meeting as well to construct the average $\overline{D}_{C,t_{0}-1,n_{0}}$ possibly applying down-weighting for observations further in time from $t_{0}$, i.e., use $\ldots,D_{t_{-1}-1},\,D_{t_{-1}+1},\,D_{t_{-1}+2}\ldots,\,D_{t_{0}-2},\,D_{t_{0}-1}$. Similarly, observations in $\mathbf{P}$ close to $t_{0}$ provide information about what $\mathbb{E}\left(D_{t_{0}}\left(1\right)\right)$ would have been, though here the successive observations are separated chronologically by the observations in the control sample $\mathbf{C}$.
We now present the formal result for identification of the compliers. The following two assumptions can be justified in large samples when the mean (potential) treatment assignments in both the control and policy samples vary smoothly over time. Under an infill asymptotic embedding where the original observations indexed by $t=1,\ldots,\,T$ are mapped into the unit interval $[0,\,1]$ via $u=t/T$, if $\lim_{T\rightarrow\infty}\mathbb{E}(D_{Tu}(z))$ is continuous in $u$ under a fixed instrument value $z\in\mathbf{Z}$, the following assumptions hold. This type of continuity accommodates general forms of smoothly time-varying means but not abrupt breaks in mean.\footnote{However, breaks in the mean of the assignment process can be estimated under some conditions as we explain below. Then, time-smoothness is required to hold only in regimes defined by successive break dates.}
Assumption (ref)(i) requires a law of large numbers to apply to the rolling-window sample average of $D_{t}$ at the points of continuity of $\mathbb{E}\left(D_{t}\right)$. It is a minimal technical assumption. Assumption (ref)(ii) strengthens part (i) a bit by requiring that for $t\in\mathbf{P}$ the potential treatment assignment under the trajectory $Z_{t}=0$ has a locally constant mean. Assumption (ref)(i) adapts Assumption (ref)(i) to the observations in $\mathbf{P}$. This is a stronger assumption since two successive observations in the policy sample are separated by several observations in the control sample. Assumption (ref)(ii) requires that $\mathbb{E}\left(D_{t}\left(1\right)\right)$ for $t\in\mathbf{C}$ is equal to the mean of the potential treatment assignment at the closest date in the policy sample $s^{*}\left(t\right)$. This is a first moment constancy assumption on the potential treatment assignment under the trajectory $Z_{t}=1$. Assumption (ref) is used to identify the compliers in the policy sample, while Assumption (ref) is used to identify the compliers in the control sample.
Theorem (ref) shows that the compliers can be identified individually. To the best of our knowledge, there is no equivalent result in the cross-sectional setting. The assumptions of the theorem are easily satisfied in time series applications. Using Theorem (ref) is straightforward: one computes the difference between two sample averages and check whether it is greater than zero. Given the sampling uncertainty associated with the two averages, one can conduct inference using a $t$-statistic for the null hypothesis $\mathbb{E}\left(D_{t_{0}}\left(1\right)\right)-\mathbb{E}\left(D_{t_{0}}\left(0\right)\right)=0$ ($t_{0}$ is not a complier) versus the alternative hypothesis that $\mathbb{E}\left(D_{t_{0}}\left(1\right)\right)-\mathbb{E}\left(D_{t_{0}}\left(0\right)\right)>0$ ($t_{0}$ is a complier).
An additional challenge specific to the $\pi$-LATE framework is that the set of observations with a first stage $\mathbf{S}_{0,T}$ is also unknown. However, as the following result states, under Assumption (ref), in the absence of covariates $\widetilde{V}_{t}$, $\mathbf{S}_{0,T}$ is equal to the (identified) set of compliers \textemdash i.e., observations for which the first-stage holds individually.
Knowledge of the compliers sub-population (and hence of the non-compliers sub-population) can be used to test the exclusion restriction (cf. Assumption (ref)) by comparing the mean outcomes of groups of non-compliers across different values of the instrument. For example, one can divide any large subset of non-compliers into two groups according to their assignment status. If one can reject the hypothesis that the average outcomes in these two groups is the same, then the exclusion restriction cannot hold.
Under Assumption (ref) with $D_{t}(1)\geq D_{t}(0)$, the set of non-compliers is $\mathcal{NC}=\{t\in\{1,\ldots,T\}:D_{t}(1)=D_{t}(0)=D_{t}\}$. Let $\mathcal{NC}^{s}$ be any non-empty subset of $\mathcal{NC}$ such that $\mathcal{NC}_{\mathbf{P}}^{s}=\mathcal{NC}^{s}\cap\mathbf{P}\neq\emptyset$ and $\mathcal{NC}_{\mathbf{C}}^{s}=\mathcal{NC}^{s}\cap\mathbf{C}\neq\emptyset$. We can test the exclusion restriction in Assumption (ref) under the following assumption on the subsets $\mathcal{NC}_{\mathbf{P}}^{s}$ and $\mathcal{NC}_{\mathbf{C}}^{s}$.
Condition (i) states that the potential outcome for non-compliers is mean-stationary and the mean is the same across control and policy subsamples. Condition (ii) states that the policy variable and past observables for non-compliers are distributed identically across the control and policy subsamples. Condition (iii) states that a law of large numbers holds for non-compliers observations in both the control and policy subsamples. As long as the policy sample does not tend to contain systematic different values of the policy variable $D_{t}$ among non-compliers than the control sample, these are relatively mild conditions.
Using Proposition (ref) to test Assumption (ref) is simple: since non-compliers can be identified individually using Theorem (ref), one can immediately compute the sample averages specified in Proposition (ref) and conduct inference using a $t$-statistic for the null hypothesis that the population mean of $t\in\mathcal{NC}_{\mathbf{P}}^{s}$ is equal to that of $t\in\mathcal{NC}_{\mathbf{C}}^{s}$. The researcher has the ability to choose the subset of non-compliers $\mathcal{NC}^{s}$ when implementing this test. The simplest choice is to set $\mathcal{NC}^{s}=\mathcal{NC}$, however, the researcher also has the ability to direct the power of the test toward particular types of non-compliers they may suspect of being more likely to violate the exclusion restriction. For example, one may wish to focus on $\mathcal{NC}^{s}=\{t\in\mathcal{NC}:D_{t}\geq d^{*}\}$ or $\mathcal{NC}^{s}=\{t\in\mathcal{NC}:D_{t}<d^{*}\}$ for some $d^{*}$ value, such as $d^{*}=|\mathcal{NC}|^{-1}\sum_{t\in\mathcal{NC}}D_{t}$, in order to test violations of the exclusion restriction for observations roughly corresponding to “always-takers” or “never-takers” in the case of a binary treatment.\footnote{Under an analogous assumption to Assumption (ref) for a function of outcomes $f(Y_{t})$, an analogous result to Proposition (ref) holds. One may use this fact, for example, to test if the variances of groups of non-compliers are equal across different values of the instrument, which is implied by Assumption (ref), or to test the equality of a set of moments across different values of the instrument. Taking this logic even further, one could invoke Gilvenko-Cantelli theorems to show that the difference between the empirical distribution functions of observations in $\mathcal{NC}_{\mathbf{P}}^{s}$ and $\mathcal{NC}_{\mathbf{C}}^{s}$ converge uniformly to zero under Assumption (ref) and use a test for the equality of distributions such as the Kolmogorov-Smirnov test. However, we focus here on testing the equality of means across instrument values because the level of the outcomes, rather than functions of them, are likely to be of primary importance in practice.}
To study the effects of monetary policy on real variables, a large literature has relied on high-frequency identification. This exploits the fact that at the time of an FOMC meeting a large amount of economic news is revealed. Here we discuss rigobon:2003's rigobon:2003 heteroskedasticity identification approach which uses a 1-day window {[}see, e.g., nakamura/steinsson:2018{]}, and can be reformulated as IV-based identification. In Section (ref) we explain when the resulting reduced-form estimands have a causal meaning within the potential outcome framework of Section (ref). In Section (ref) we discuss the weak identification problem of current approaches and show how the $\pi$-LATE framework can be used to strengthen identification.
Consider the following system of equations:
where $\tilde{Y}_{t}$ is the (demeaned) daily change in an outcome variable, (e.g., an asset price or a bond yield) and $\tilde{D}_{t}$ is the (demeaned) daily change in the unexpected component of a short-term interest rate or policy news (e.g., $\Delta i_{t}$ as discussed after Proposition (ref)), $\eta_{t}$ is a shock to $\tilde{Y}_{t}$, $e_{t}$ is the monetary policy shock and $a$ and $\beta_{0}$ are scalar parameters. The errors $\eta_{t}$ and $e_{t}$ have no serial correlation and are mutually uncorrelated. The parameter of interest is $\beta_{0}$ which represents the causal effect of monetary policy on the outcome variable. The model in (ref) could arise from a bivariate VAR. In fact, one could add a vector $X_{t}$ of exogenous variables to the model in (ref). However, to focus on the main intuition, we follow nakamura/steinsson:2018 and we omit $X_{t}$ and lagged terms of $\tilde{Y}_{t}$ and $\tilde{D}_{t}$. See casini/mccloskey:2024 for a detailed discussion of why the lags can be omitted in this setting.
The model in (ref) is a special case of the generalized framework studied in Section (ref). It is useful because it directly motivates a particular IV estimand. However, we study the causal interpretation of this estimand in the general case for which the linear model with stable parameters is not the correct specification.
Heteroskedasticity-based identification requires that the variance of the monetary shock increases in the days of FOMC announcements, while the variance of other shocks is unchanged. Let $T_{P}$ denote the number of days containing an FOMC announcement (policy sample), and let $T_{C}$ denote the number of days that do not contain an FOMC announcement (control sample). Let $\sigma_{e,P}^{2}=T_{P}^{-1}\sum_{t\in\mathbf{P}}\mathbb{E}\left(e_{t}^{2}\right)$ and $\sigma_{e,C}^{2}=T_{C}^{-1}\sum_{t\in\mathbf{C}}\mathbb{E}\left(e_{t}^{2}\right)$ be the average variance of the monetary policy shock in the policy and control samples. Define $\sigma_{\eta,P}^{2}$ and $\sigma_{\eta,C}^{2}$ similarly. Then, the identification condition is
Identification can be shown analytically by first solving for the reduced-form of (ref):
Let $\Sigma_{i}$ denote the covariance matrix of $[\tilde{Y}_{t},\,\tilde{D}_{t}]'$ in the subsample $i=P,\,C$. It follows that
It is typical in the literature to assume within-regime covariance-stationarity, i.e., $\mathbb{E}\left(e_{t}^{2}\right)$ and $\mathbb{E}\left(\eta_{t}^{2}\right)$ are constant within each subsample $\mathbf{P}$ and $\mathbf{C}$ which is, however, restrictive for economic time series. It turns out that this is not necessary for identification. Volatilities can be time-varying as long as the average volatilities $\sigma_{e,i}$ and $\sigma_{\eta,i}$ $\left(i=P,\,C\right)$ satisfy (ref).
When (ref) is correctly specified, i.e., the true model is linear with stable parameters, the parameter $\beta_{0}$ can be identified using (ref) by taking the difference between the covariance matrices in the policy and control samples:
To determine which average treatment effect this approach identifies in the general framework, we re-frame this problem in terms of instrumental variables as follows. Let $Z_{t}=1$ for $t\in\mathbf{P}$ and $Z_{t}=0$ for $t\in\mathbf{C}$. Multiply both sides of (ref) by $\tilde{D}_{t}$ to yield $\tilde{D}_{t}\tilde{Y}_{t}=\beta_{0}\tilde{D}_{t}^{2}+\tilde{D}_{t}\eta_{t}.$ We can use $Z_{t}$ as an instrument for $\tilde{D}_{t}^{2}$. The first-stage is $\tilde{D}_{t}^{2}=\theta Z_{t}+\varepsilon_{t},$ where $\varepsilon_{t}$ is some error term satisfying $\varepsilon_{t}\geq-\theta Z_{t}$. The resulting Wald estimand is
which corresponds to the Wald estimand (ref) for $h=0$, $Y_{t}=\tilde{D}_{t}\tilde{Y}_{t}$, $D_{t}=\tilde{D}_{t}^{2}$ and no conditioning variable $\widetilde{V}_{t}$. Under covariance stationarity within subsamples $\mathbf{P}$ and $\mathbf{C}$, the right-hand side of (ref) is equal to the right-hand side of (ref). The following corollary of Proposition (ref) presents the causal meaning of $\beta_{\pi,t,0}^{*}$ under the general setting of Section (ref).
Corollary (ref) shows that the Wald estimand in (ref) has a causal meaning because it is the ratio of a reduced-form generalized impulse response of $\tilde{D}_{t}\tilde{Y}_{t}$ to a first-stage generalized impulse response of $\tilde{D}_{t}^{2}$. More specifically, $\beta_{\pi,t,0}^{*}$ identifies a weighted average of the derivative of the product between the potential outcome and policy variable for compliers. Hence, contrary to popular belief, the causal interpretation of the heteroskedasticity-based estimator (i.e., Rigobon's estimator) estimator is not the same as that of a standard IV estimator\textemdash though it remains local in nature as it averages over compliers. We continue to refer to it as LATE with the understanding that it is a LATE for $\tilde{D}_{t}\tilde{Y}_{t}$, not $\tilde{Y}_{t}$ itself.
Here the compliers are the observations for which the announcement induces a higher volatility of the policy $\tilde{D}_{t}$. In contrast, the non-compliers are characterized by idiosyncratic or general equilibrium factors that dominate the news specific to the announcement. That is, regimes where $\tilde{D}_{t}^{2}$ remains low regardless of the presence of an announcement correspond to “never-takers,” while regimes where $\tilde{D}_{t}^{2}$ remains high even in the absence of an announcement correspond to “always-takers.” Noting that $D_{t}=\tilde{D}_{t}^{2}$ in this context, we can apply Theorem (ref) to identify the compliers individually. We do so in the empirical application in Section (ref).
It is important to consider how the interpretation of the causal effect identified by ${\beta}_{\pi,t,0}^{*}$ in Corollary (ref) varies with the functional relationship between $\tilde{Y}_{t}$ and $\tilde{D}_{t}$. Let us begin with the linear case with stable parameters as in (ref). From (ref), simple algebra shows that ${\beta}_{\pi,t,0}^{*}$ reduces to $\beta_{0}$ when the denominator of (ref) is nonzero, which means that Rigobon's estimator identifies the causal effect of the policy (i.e., the slope coefficient in (ref)). This result does not generally extend to the case where $\beta_{0}$ is time-varying or the first-stage is zero. At most one could identify a $\pi$-LATE provided that Rigobon's estimator is computed over the sub-population where the first-stage is nonzero. We will return to this in Section (ref).
Let us turn to analyzing the consequences of nonlinearities. When $D_{t}$ and the shock $\eta_{t}$ are additively separable (i.e., $Y_{t}=\varphi_{D}(D_{t})+\varphi_{\eta}\left(\eta_{t}\right)$ for some nonlinear functions $\varphi_{D}\left(\cdot\right)$ and $\varphi_{\eta}\left(\cdot\right)$), kolesar/plagborgmoller:2025 show that the estimand resulting from a regression of $Y_{t}$ on $D_{t}$ using $Z_{t}=(W_{t}-\mathbb{E}\left(W_{t}\right))D_{t}$ as an instrument for which $\mathrm{Cov}\left(D_{t}^{2},\,W_{t}\right)\neq0$ identifies a weighted average of marginal effects of the policy shock $e_{t}$ with weights that are not guaranteed to be positive. As a result, the researcher may infer an incorrect sign for the marginal effects. Thus, this estimand is not weakly causal {[}cf. blandhol/bonney/mogstad/torgovitsky:2025{]}. The authors also note that for the case $Y_{t}=e_{t}\varphi_{\eta}\left(\eta_{t}\right)$ with $\mathbb{E}[\varphi_{\eta}\left(\eta_{t}\right)]=0$ and $e_{t}\bot\eta_{t}$ the estimand is nonzero while the true causal effect of the policy shock is zero since $\mathbb{E}\left[Y_{t}|\,e_{t}\right]=0$.
Corollary (ref) provides even more negative news about the effect of nonlinearities for heteroskedasticity-based identification than that shown by kolesar/plagborgmoller:2025: in a general nonparametric model, Corollary (ref) implies that Rigobon's Wald estimand ${\beta}_{\pi,t,0}^{*}$, which is in general different from the IV estimand examined by kolesar/plagborgmoller:2025, does not necessarily equal a weighted average of marginal effects. The intuition is that the instrument affects $\mathrm{Var}\left(D_{t}\right)$ and not $\mathbb{E}\left(D_{t}\right)$, so variation in the instrument induces exogenous variation in $D_{t}^{2}$, which has a causal effect on $D_{t}Y_{t}$ not just $Y_{t}$. In short, it is generally difficult to interpret ${\beta}_{\pi,t,0}^{*}$ when the true model is nonlinear. Thus, we concur with the recommendation of kolesar/plagborgmoller:2025 that the linearity assumption should be checked carefully when using heteroskedasticity-based identification. This is likely even more important in the context of SVARs and local projections than in the the current event study setting since the former aggregates data over a month or a quarter while the latter uses relatively higher frequency data (e.g., a 30-minute or 1-day change in policy and outcome variables around an announcement), where linearity may be a more credible assumption since a nonlinear function can be locally well approximated by a linear one.\footnote{The differences between our results on identification via heteroskedasticity and those in kolesar/plagborgmoller:2025 are: (i) they consider the causal effect of the policy shock $e_{t}$ while we consider the causal effect of the policy variable $D_{t}$; (ii) they consider an IV estimand while we explicitly consider Rigobon's estimand motivated by $\Delta\Sigma^{\left(1,2\right)}/\Delta\Sigma^{\left(2,2\right)}$ in (ref) and as usually implemented in empirical work based on event studies; (iii) they consider specific nonlinear restrictions and allow the instrument to be continuous whereas we allow for a general nonlinear model and consider a binary instrument as motivated by (ref).}
The key identification condition that the volatility of the policy variable is higher during FOMC announcement days appears reasonable in principle, since each announcement day is likely to be associated with substantial monetary news. However, the volatility of monetary policy variables can be high for other reasons. There are multi-year periods during which the volatility of several macroeconomic variables is elevated. In this case, general equilibrium factors dominate the news specific to the announcement. For example, during the 2007-09 financial crisis and the Covid-19 pandemic, volatility was high across many macroeconomic and financial variables. These facts pose serious challenges for identification, as the first-stage condition may not hold for all $t$. To see this, examine the denominator of $\beta_{0}$ in (ref). If the first-stage does not hold for all $t$, we may have
which would render the estimate of the average treatment effect highly imprecise.
Using an $F$-test for weak identification, lewis:2020 shows that the monetary policy effects based on a 1-day window in nakamura/steinsson:2018 appear to be weakly-identified. We show that this arises from significant time variation in the volatility of the policy variable within both policy and control samples. Figure (ref) plots $\tilde{D}_{t}$ (2-Year Treasury yields) for the control and policy samples. The policy sample includes all regularly scheduled FOMC meeting days from 1/1/2000 to 3/19/2014. The control sample includes all Tuesdays and Wednesdays that are not FOMC meeting days between 1/1/2000 and 12/31/2012.
There appear to be multiple volatility regimes. Using the structural break test from casini/perron:change-point-spectra, which allows for stable or smoothly varying volatility under the null and abrupt breaks under the alternative, we detect three breaks in the control sample. The first break (April 24, 2007) marks the start of the 2007-09 financial crisis. The second (July 28, 2009) captures the crisis period itself, characterized by the highest volatility. Afterward, volatility returns to pre-crisis levels until the third break (February 2, 2011), which aligns with the zero lower bound (ZLB) period and the start of unconventional monetary policy. The final regime shows the lowest volatility, reflecting initial policy effects and stabilization.\footnote{We do not test for breaks in the policy sample due to small size ($T_{P}=74$), treating it as a single regime.}
These findings show significant time variation in $\mathrm{Var}(\tilde{D}_{t})$. In the second regime, control-sample volatility is close to the policy-sample average, contributing to the weak identification in (ref). nakamura/steinsson:2018 find their estimates imprecise and not economically meaningful for some of the interest rates they use as outcome variables. lewis:2020 reports a first-stage $F$-statistic of 8.11\textemdash well below the 23 critical value\textemdash suggesting weak identification.
We propose to focus on $\pi$-LATE. The fraction $\pi_{0}$ of the sample (i.e., all $t\in\mathbf{S}_{0,T}$) that has a first-stage corresponds to the regimes in the control sample where $\mathrm{Var}(\tilde{D}_{t})$ is low (relative to its average level). For example, it is likely that the regime $[\widehat{T}_{1}+1,\,\widehat{T}_{2}]$ does not belong to $\mathbf{S}_{0,T}$ since $\mathrm{Var}(\tilde{D}_{t})$ within this regime appears close to the average volatility in the policy sample. By construction, it is easier to identify $\pi$-LATE than full sample LATE. The usefulness of $\pi$-LATE depends on the magnitude of $\pi_{0}$: a small $\pi_{0}$ implies that identification is achievable only in a small portion of the population, whereas a large $\pi_{0}$ indicates that the identified $\pi$-LATE is representative of a substantial part of the population.\footnote{It is possible that in practice the $\pi_{0}$ fraction of the sample contains a mixture of strong and weak identification. We discuss weak identification in the context of $\pi$-LATE formally in Section (ref).}
The $\pi$-LATE parameter is the same as the LATE parameter (ref) in Section (ref) but instead of supposing that a first-stage exists, only uses observations with a nonzero first-stage. Let $T_{P,S}$ denote the number of days in $\mathbf{S}_{0,T}$ that contain an FOMC announcement, and let $T_{C,S}$ the number of days in $\mathbf{S}_{0,T}$ that do not contain an FOMC announcement. This means $T_{P,S}+T_{C,S}=\pi_{0}T$.\footnote{For notational simplicity we assume that $\pi_{0}T$ is an integer so that we avoid using the notation $\left\lfloor \pi_{0}T\right\rfloor $, where $\left\lfloor \cdot\right\rfloor $ denotes the largest smaller integer function.} Let $\Sigma_{i,S}$ denote the covariance matrix of $[\tilde{Y}_{t},\,\tilde{D}_{t}]'$ in the subsample $i=\mathbf{P},\,\mathbf{C}$ using only observations $t\in\mathbf{S}_{0,T}$. We have
with $\mathbf{P}_{\mathbf{S}}=\mathbf{P}\cap\mathbf{S}_{0,T}$ and $\mathbf{C}_{\mathbf{S}}=\mathbf{C}\cap\mathbf{S}_{0,T}.$ Proceeding as for LATE, the Wald estimand is
to which Corollary (ref) immediately applies without the (now redundant) qualifier “for $t\in\mathbf{S}_{0,T}$.” Under within subsample covariance stationarity, the right-hand side of (ref) is equal to that of (ref), implying $\tilde{\beta}_{\pi,0}=\tilde{\beta}_{\pi,t,0}^{*}$. Therefore, $\tilde{\beta}_{\pi,0}$ identifies the same $\pi$-LATE, as defined explicitly in Corollary (ref). $\pi$-LATE is the average treatment effect for the sub-population for which a first-stage holds: observations for which $\tilde{D}_{t}^{2}$ is induced to be higher by the announcement (i.e., the sub-population of compliers in $\mathbf{S}_{0,T})$.
If the treatment effect is constant across the population {[}e.g., as in (ref){]}, then the $\pi$-LATE for the sub-population $\mathbf{S}_{0,T}$ is equal to both the LATE and ATE in the full population. To determine which treatment effect is identified, we must determine which parts of the sample belong to $\mathbf{S}_{0,T}$.We discuss this in Sections (ref)-(ref).
In this section, we introduce a test of the null hypothesis that no subpopulation exists for which a LATE can be identified, even weakly. In other words, the test assesses whether identifying a sub-population LATE is possible at all. However, we strongly caution against using this as a pretest before estimation or inference, as doing so may introduce pretest bias and invalidates standard inference unless the inference method is modified to account for the pretest {[}see, e.g., andrews:2018{]}. Instead, the test should be viewed as a diagnostic tool for evaluating whether there is evidence of identifiable sub-population LATEs in a given application. We apply it for this purpose to several existing studies that appear to face identification challenges. Notably, such a pretest is unnecessary for conducting identification-robust inference on sub-population LATEs, which we discuss in Section (ref).
In accord with the analysis of Section (ref), consider an IV regression model with a single endogenous variable and multiple instruments. In matrix format, the structural equation is
where $Y$ is a $T\times1$ vector of outcome variables, $D$ is $T\times1$ vector of endogenous variables, $X$ is a $T\times p$ matrix of $p$ exogenous regressors, $u$ is a $T\times1$ vector of error terms, and $\beta\in\mathbb{R}$ and $\gamma_{1}\in\mathbb{R}^{p}$ are unknown parameters. The reduced-form equation is
where $Z_{t}$ is a $q\times1$ vector of instruments, $e_{t}$ is an error term, and $\theta\in\mathbb{R}^{q}$ and $\gamma_{2}\in\mathbb{R}^{p}$ are unknown parameters. For $t\notin\mathbf{S}_{0,T}$, the instrument $Z_{t}$ is irrelevant. For $t\in\mathbf{S}_{0,T}$, the instrument $Z_{t}$ is relevant if $\theta\neq0$. We assume that $|\mathbf{S}_{0,T}|=\pi_{0}T$ for some $\pi_{0}\in(0,1]$, noting that this is without loss of generality since it does not rule out complete identification failure which occurs when $\theta=0$ for any $\pi_{0}\in(0,1]$. The hypothesis testing problem is \[ H_{\theta,0}:\,\theta=0\quad\mathrm{versus}\quad H_{\theta,1}:\,\theta\neq0. \] We discuss both the cases for which the sub-population $\mathbf{S}_{0,T}$ is known and unknown. For the sake of the exposition, we focus on homogeneous $\theta$ in $\mathbf{S}_{0,T}$.\footnote{We could allow for $\theta_{t}\neq0$ for $t\in\mathbf{S}_{0,T}$ at the expense of additional notation and longer proofs, though the key insights would not change. Actually, the computational procedures we develop to implement our methods allow $\theta_{t}\neq0$ for $t\in\mathbf{S}_{0,T}$.}
Consider the $\left(\pi T\times T\right)$ selection matrix $S_{T}$ that selects the $\pi T$ rows of a matrix corresponding to the indices in $\mathbf{S}_{T}$. That is, for an arbitrary $T\times k$ matrix $A$, $S_{T}A$ is the $\left(\pi T\times k\right)$ matrix whose elements are the rows of $A$ that correspond to the indices in $\mathbf{S}_{T}$. For example, if $\mathbf{S}_{T}=\left\{ 1,\ldots,\,0.25T,\,0.75T+1,\ldots,\,T\right\} $, \[ S_{T}A=\left[A^{\left(1,:\right)\prime}:\cdots:A^{\left(0.25T,:\right)\prime}:A^{\left(0.75T+1,:\right)\prime}:\cdots:A^{\left(T,:\right)\prime}\right]', \] where $A^{\left(r,:\right)}$ denotes the $r^{th}$ row of the matrix $A$. Using the standard projection matrix notation, $P_{A}=A(A^{\prime}A)^{-1}A^{\prime}$ and $M_{A}=I-P_{A}$, let $\widetilde{A}(S_{T})=M_{S_{T}X}S_{T}A$ for any arbitrary $T\times k$ matrix $A$. The following $F$ test statistic is useful for testing whether $\theta=0$ in the regression (ref) when the sub-population $\mathbf{S}_{0,T}$ is known:
for $\mathbf{S}_{T}=\mathbf{S}_{0,T}$ and $Z=[Z_{1}:\cdots:Z_{T}]^{\prime}$ and $\widehat{J}(S_{T})$ a consistent estimate of the long-run variance, \[ \lim_{T\rightarrow\infty}(T\pi)^{-1}\mathrm{Var}(\widetilde{Z}(S_{T})'S_{T}e) \] with $e=[e_{1}:\cdots:e_{T}]^{\prime}$. HAC or DK-HAC estimators can be used to estimate the long-run variance {[}cf. andrews:91, casini_hac and newey/west:87{]}.
For the case of an unknown sub-population, we follow the structural break literature and search for maximal identification strength over all sub-populations of minimal size $\pi_{L}T$ that can be partitioned into $m$ distinct smaller sub-populations, where $\pi_{L}>0$ and $1\leq m\leq m_{+}$ for some upper bound on the number of regimes $m_{+}>0$: \[ F_{T}^{*}=\sup_{\pi\in[\pi_{L},\,1]}\max_{1\leq m\leq m_{+}}\sup_{\mathbf{S}_{T}\in\Xi_{\epsilon,\pi,m,T}}F_{T}\left(\mathbf{S}_{T}\right), \] where $\Xi_{\epsilon,\pi,m,T}$ denotes the set of all possible partitions of a fraction $\pi$ of $\{1,\ldots,T\}$ that involve $m$ regimes $\left(\left(\lambda_{L,1}T,\,\lambda_{R,1}T\right),\ldots,\,\left(\lambda_{L,m}T,\,\lambda_{R,m}T\right)\right)$ for $\lambda_{L,i},\,\lambda_{R,i}\in\left[0,\,1\right]$ such that (i) $\lambda_{L,i}<\lambda_{R,i}$ for all $i$, (ii) $\lambda_{R,i}<\lambda_{L,i+1}$ for $i=1,\ldots,\,m-1$, (iii) $\left|\lambda_{R,i}-\lambda_{L,i}\right|\geq\epsilon$ for all $i$ and some (small) $\epsilon>0$ and (iv) $\sum_{i=1}^{m}(\lambda_{R,i}-\lambda_{L,i})=\pi.$ Conditions (i) and (ii) correspond to $T\lambda_{L,i}$ ($T\lambda_{R,i}$) denoting the start (end) date of regime $i$ within the sub-population $\mathbf{S}_{T}$ while condition (iii) implies that each regime involves a non-negligible fraction of the sample. The statistic $F_{T}^{*}$ thus implicitly searches for maximal identification strength over all possible sub-populations of size $\pi_{L}T$ and larger with less than $m_{+}$ distinct regimes that are at least a $\epsilon$ fraction of the overall sample size.
The tuning parameters $\pi_{L}$ and $\epsilon$ determine the types of sub-populations for which the test can detect identification: smaller values of $\pi_{L}$ allow detection in smaller sub-populations, while smaller values of $\epsilon$ enable detection in sub-populations with shorter regimes. The choice of these lower bounds should be guided by the empirical context, reflecting the smallest sub-population and regime sizes for which LATE inference remains meaningful in the application.\footnote{In the structural break literature, common recommendations for $\epsilon$ are 0.05, 0.10 and 0.15. See casini/perron_Oxford_Survey for a review.} In our simulations and empirical applications we set $\pi_{L}=0.6$ and $\epsilon=0.05$.
For $X_{t}^{\prime}$ the $t^{th}$ row of $X$, let $w_{t}=(X'_{t},\,Z'_{t})'$ and $W_{r}\left(\cdot\right)$ denote a $r$-vector of independent Wiener processes on $\left[0,\,1\right]$. We derive the asymptotic null distributions of $F_{T}\left(\mathbf{S}_{T}\right)$ and $F_{T}^{*}$ under the following standard high-level assumptions that permit both heteroskedastic and serially correlated errors. Sufficient conditions for them can be found in the supplement.
When $\pi=1$ ($\pi_{L}=1$ and $m_{+}=1$), $F_{T}\left(\mathbf{S}_{T}\right)$ ($F_{T}^{*}$) reduces to the usual first-stage $F$-statistic for $\theta=0$ in (ref). For $\pi\in(0,\,1)$ ($\pi_{L}\in(0,\,1)$), the consistency of tests against $H_{\theta,1}$ using $F_{T}\left(\mathbf{S}_{0,T}\right)$ ($F_{T}^{*}$) follows from similar arguments as for the $\pi_{0}=1$ case. The asymptotic null distributions of both $F\left(\mathbf{S}\right)$ and $F_{T}^{*}$ are free of nuisance parameters. The critical values are obtained via simulations and reported in Table (ref) for up to $m_{+}=6$ and up to $q=6$.
We discuss estimation of the LATE parameter $\beta$ in (ref) in both the cases of a known and unknown sub-population $\mathbf{S}_{0,T}$, as well as estimation of $\mathbf{S}_{0,T}$ itself in the latter case. When $\mathbf{S}_{0,T}$ is known, estimation of $\beta$ is an application of IV estimation for which $Z_{t}\mathbf{1}\{t\in\mathbf{S}_{0,T}\}$ is treated as the vector of instruments. Let this estimator be denoted as $\widehat{\beta}(\mathbf{S}_{0,T})$.
On the other hand, when the sub-population $\mathbf{S}_{0,T}$ is unknown, we must estimate it first. Although $\mathbf{S}_{0,T}$ can be estimated consistently in the special case of a binary instrument under the conditions of Proposition (ref) and Theorem (ref), it can also be estimated more generally. We discuss two methods. The first is more computationally straightforward but the second is more efficient because it uses the information in both structural and reduced-form equations (ref)-(ref). We follow the structural change literature and assume that $\pi_{0}$ and $m_{0}$ are known, i.e., the practitioner has previously used the tests from Section (ref) to determine $\pi_{0}$ and $m_{0}$.
We begin with the first estimator. Consider the $T\times T$ matrix $C_{T}$ that selects the $\pi T$ rows of a matrix corresponding to the indices in $\mathbf{S}_{T}$ while setting the remaining $(1-\pi)T$ rows to zero. For example, for a $T\times k$ matrix $A$, if $\mathbf{S}_{T}=\left\{ 1,\ldots,\,0.25T,\,0.75T+1,\ldots,\,T\right\} $, \[ C_{T}A=\left[A^{\left(1,:\right)\prime}:\cdots:A^{\left(0.25T,:\right)\prime}:0_{k\times1}:\cdots:0_{k\times1}:A^{\left(0.75T+1,:\right)\prime}:\cdots:A^{\left(T,:\right)\prime}\right]'. \] Let $\overline{A}(C_{T})=M_{X}C_{T}A$ so that for a given $\mathbf{S}_{T}$, the OLS estimators of $\theta$ and $\gamma_{2}$ in (ref) can be expressed as $\widehat{\theta}_{OLS}(\mathbf{S}_{T})=(\overline{Z}(C_{T})^{\prime}\overline{Z}(C_{T}))^{-1}\overline{Z}(C_{T})^{\prime}D$ and $\widehat{\gamma}_{2,OLS}(\mathbf{S}_{T})=(X^{\prime}M_{C_{T}Z}X)^{-1}X^{\prime}M_{C_{T}Z}D$. Our first estimator of $\mathbf{S}_{0,T}$ minimizes the sum of squared residuals of the reduced-form: \[ \widehat{\mathbf{S}}_{T,OLS}=\underset{\mathbf{S}_{T}\in\Xi_{\epsilon,\pi_{0},m_{0},T}}{\mathrm{argmin}}\left(D-C_{T}Z\widehat{\theta}_{OLS}(\mathbf{S}_{T})-X\widehat{\gamma}_{2,OLS}(\mathbf{S}_{T})\right)^{\prime}\left(D-C_{T}Z\widehat{\theta}_{OLS}(\mathbf{S}_{T})-X\widehat{\gamma}_{2,OLS}(\mathbf{S}_{T})\right). \] Correspondingly, we estimate $\beta$ with $\widehat{\beta}(\widehat{\mathbf{S}}_{T,OLS})$.
For the second estimator of the sub-population $\mathbf{S}_{0,T}$, we propose a GLS criterion that minimizes an efficiently weighted combination of the sum of squared residuals of both the reduced-form representation of the structural equation (ref) and the reduced-form equation (ref). That is, the system of equations (ref)-(ref) can be written in reduced-form as
where $\vec{y}=(Y',\,D')'$, $W(\mathbf{S}_{0,T})=I_{2}\otimes[C_{0,T}Z:X]$, $\xi=(\beta\theta',\gamma_{1}^{\prime}+\beta\gamma_{2}^{\prime},\theta',\gamma_{2}^{\prime})^{\prime}$ and $\varepsilon=(u^{\prime}+\beta e^{\prime},e^{\prime})^{\prime}$ with $C_{0,T}$ defined as $C_{T}$ but corresponding to the indices in $\mathbf{S}_{0,T}$. This is a system of two seemingly unrelated regressions. Let \[ \widehat{\xi}_{FGLS}(\mathbf{S}_{T})=(W(\mathbf{S}_{T})^{\prime}\widehat{\Omega}_{\varepsilon}(\mathbf{S}_{T})^{-1}W(\mathbf{S}_{T}))^{-1}W(\mathbf{S}_{T})^{\prime}\widehat{\Omega}_{\varepsilon}(\mathbf{S}_{T})^{-1}\vec{y}, \] denote a feasible GLS estimator of $\xi$, where $\widehat{\Omega}_{\varepsilon}(\mathbf{S}_{T})$ is a consistent estimator of $\mathbb{E}[\varepsilon\varepsilon^{\prime}|W(\mathbf{S}_{T})]$. Our second estimator of $\mathbf{S}_{0,T}$ minimizes the following GLS criterion based upon (ref): \[ \widehat{\mathbf{S}}_{T,FGLS}=\underset{\mathbf{S}_{T}\in\Xi_{\epsilon,\pi_{0},m_{0},T}}{\mathrm{argmin}}\left(\vec{y}-W(\mathbf{S}_{T})\widehat{\xi}_{FGLS}(\mathbf{S}_{T})\right)^{\prime}\widehat{\Omega}_{\varepsilon,\mathbf{S}}^{-1}\left(\vec{y}-W(\mathbf{S}_{T})\widehat{\xi}_{FGLS}(\mathbf{S}_{T})\right). \] Correspondingly, we estimate $\beta$ with $\widehat{\beta}(\widehat{\mathbf{S}}_{T,FGLS})$. In order for $\widehat{\beta}(\widehat{\mathbf{S}}_{T,FGLS})$ to be provably more efficient than $\widehat{\beta}(\widehat{\mathbf{S}}_{T,OLS})$, $\widehat{\Omega}_{\varepsilon,\mathbf{S}}$ must be a consistent estimator of $\mathbb{E}[\varepsilon\varepsilon^{\prime}|W(\mathbf{S}_{0,T})]$. When $\varepsilon_{t}$ does not exhibit conditional serial correlation or heteroskedasticity, i.e., $\mathbb{E}[\varepsilon\varepsilon^{\prime}|W(\mathbf{S}_{0,T})]=\Sigma_{\varepsilon}\otimes I_{T}$, this is feasible since one could simply use $\widehat{\Omega}_{\varepsilon,\mathbf{S}}=\widehat{\Sigma}_{\varepsilon}\otimes I_{T}$, where $\widehat{\Sigma}_{\varepsilon,i,j}=(T-q-p)^{-1}\hat{\varepsilon}^{i\prime}\hat{\varepsilon}^{j}$ for $i,j=1,2$ with $\hat{\varepsilon}^{1}$ ($\hat{\varepsilon}^{2}$) equal to the first (last) $T$ elements of $\vec{y}-W(\widehat{\mathbf{S}}_{T,OLS})\widehat{\xi}_{OLS}(\widehat{\mathbf{S}}_{T,OLS})$, as is standard in seemingly unrelated regression. For serially dependent $\varepsilon_{t}$, consistent estimation of $\mathbb{E}[\varepsilon\varepsilon^{\prime}|W(\mathbf{S}_{0,T})]$ requires a correctly-specified model for the dependence in $\varepsilon_{t}$, a strong assumption in some empirical applications. In the supplement \textcolor{MyBlue}{Casini et al.} casini/mccloskey/pala/rolla_Dynamic_Late_Supp_Not_Online we present the consistency results about $\widehat{\mathbf{S}}_{T,OLS}$, $\widehat{\beta}(\widehat{\mathbf{S}}_{T,OLS})$, $\widehat{\mathbf{S}}_{T,FGLS}$ and $\widehat{\beta}(\widehat{\mathbf{S}}_{T,FGLS})$.
In model (ref) the LATE parameter $\beta$ is constant, so $\pi$-LATE is the full population LATE and $\widehat{\beta}(\widehat{\mathbf{S}}_{T,OLS})$ and $\widehat{\beta}(\widehat{\mathbf{S}}_{T,FGLS})$ are consistent for the LATE parameter $\beta$. They can be precise estimates even when a first-stage $F$ test detects full sample weak identification because they use the most-strongly identified subsample of the data. When the model (ref) is misspecified, so that LATEs may be nonlinear and time-varying, the estimators $\widehat{\beta}(\widehat{\mathbf{S}}_{T,OLS})$ and $\widehat{\beta}(\widehat{\mathbf{S}}_{T,FGLS})$ are still consistent for a weighted average the of the LATEs in the $\mathbf{S}_{0,T}$ subsample if the $\mathbf{S}_{0,T}$ subsample exhibits strong identification.
The estimators $\widehat{\mathbf{S}}_{T,OLS}$ and $\widehat{\mathbf{S}}_{T,FGLS}$ and the test statistic $F_{T}^{*}$ solve an optimization problem over many partitions. This is computationally more complex than problems in the structural breaks literature, as it involves optimizing both over sample partitions and identification strength. We address this challenge by proposing an efficient algorithm based on dynamic programming, extending the approach of bai/perron:03 to our setting.\footnote{While antonie/boldea:2018 consider the case of a single break, and magnusson/mavroeidis:2014 study a related context, neither provide a computational solution\textemdash referring to the problem as “computationally demanding.”}
We consider tests on $\beta$ in (ref) that are robust to weak identification in both the cases for which the sub-population $\mathbf{S}_{0,T}$ is known and unknown. The hypothesis testing problem is $H_{0}:\,\beta=\beta_{0}$ versus $H_{1}:\,\beta\neq\beta_{0}.$ Here we present results for the case of unknown sub-population $\mathbf{S}_{0,T}$ and weak instruments. We also briefly discuss the case of known $\mathbf{S}_{0,T}$ and strong instruments and defer their formal treatment to the supplement. We rewrite (ref) as
with $v_{1}=u+\beta e$, $\gamma=\gamma_{1}+\phi\beta$ and $\phi=\gamma_{2}+(X^{\prime}X)^{-1}X^{\prime}C_{0,T}Z\theta$. When $\mathbf{S}_{0,T}$ is known, it is straightforward to use existing tests in the identification-robust linear IVs literature to test $H_{0}$ {[}cf. anderson/rubin:1949, andrews/moreira/stock:2006, kleibergen:2002 and moreira:2003{]}. However, Proposition (ref) in the supplement shows that $Z^{\prime}M_{X}y$ is not a sufficient statistic for $(\beta,\theta')'$ but $\overline{Z}(C_{0,T})^{\prime}y$ is, implying that existing tests suffer a loss in efficiency because they treat $Z$ rather than $C_{0,T}Z$ as the matrix of IVs. Efficient tests are therefore functions of $\overline{Z}(C_{0,T})^{\prime}y$. magnusson/mavroeidis:2014 consider a model similar to (ref). Our model specifies that $\theta$ is nonzero in the sub-population $\mathbf{S}_{0,T}$ and is zero in $\mathbf{S}_{0,T}^{c}$ where $\mathbf{S}_{0,T}^{c}$ is the complement of $\mathbf{S}_{0,T}$. magnusson/mavroeidis:2014 allow the first-stage coefficient $\theta_{t}$ to be generally time-varying for some of their tests. Their tests are based on the full sample of observations whereas our tests are based on a lower-dimensional statistic since we do not use the sub-population $\mathbf{S}_{0,T}^{c}$. This allows us to obtain gains in efficiency.
When $\mathbf{S}_{0,T}$ is known we can apply the results of andrews/moreira/stock:2006 to form identification-robust tests of $H_{0}$ vs $H_{1}$ that are functions of $\overline{Z}(C_{0,T})^{\prime}y$ and are robust to both heteroskedasticity and autocorrelation (HAR) in the reduced-form errors $\{v_{t}\}$. Suppose $\widehat{\Sigma}_{N_{1}}(\mathbf{S}_{0,T})$, $\widehat{\Sigma}_{N_{1},N_{2}}(\mathbf{S}_{0,T})$ and $\widehat{\Sigma}_{N_{2}}(\mathbf{S}_{0,T})$ are consistent estimators of $\Sigma_{N_{1}}(\mathbf{S}_{0})$, $\Sigma_{N_{1},N_{2}}(\mathbf{S}_{0})$ and $\Sigma_{N_{2}}(\mathbf{S}_{0})$ under $H_{0}$, where these latter quantities are defined by
for $\Sigma_{v\overline{Z}}\left(\mathbf{S}_{0}\right)=\Sigma_{v\overline{Z}}\left(\mathbf{S}_{0},\mathbf{S}_{0}\right)$, with
for $\mathbf{S}=\lim_{T\rightarrow\infty}T^{-1}\mathbf{S}_{T}$, $\mathbf{S}'=\lim_{T\rightarrow\infty}T^{-1}\mathbf{S}_{T}'$ $b_{0}=(1,-\beta_{0})^{\prime}$ and $a_{0}=(\beta_{0},1)^{\prime}$, where and $v_{t}$ and $\overline{Z}_{t}\left(C_{T}\right)$ are the $t$th rows $v$ and $\overline{Z}(C_{T})$.\footnote{See the supplement for details on how to construct these estimators and for consistency results.} Let $\widehat{\Sigma}_{v}\left(\mathbf{S}_{0,T}\right)=\left(T-q-p\right)^{-1}\widehat{v}\left(\mathbf{S}_{0,T}\right)'\widehat{v}\left(\mathbf{S}_{0,T}\right)$ with $\widehat{v}\left(\mathbf{S}_{0,T}\right)=y-P_{\overline{Z}\left(C_{0,T}\right)}y-P_{X}y$. Define
Consider the following HAR versions of the Anderson-Rubin (AR), Lagrange multiplier (LM) and likelihood ratio statistics based on the sufficient statistic $\overline{Z}(C_{0,T})'y$:
where $M_{1,T}(\mathbf{S}_{0,T})={N}_{1,T}\left(\mathbf{S}_{0,T}\right)^{\prime}{N}_{1,T}\left(\mathbf{S}_{0,T}\right)$, $M_{1,2,T}(\mathbf{S}_{0,T})={N}_{1,T}\left(\mathbf{S}_{0,T}\right)^{\prime}{N}_{2,T}\left(\mathbf{S}_{0,T}\right)$ and $M_{2,T}($ $\mathbf{S}_{0,T})={N}_{2,T}\left(\mathbf{S}_{0,T}\right)^{\prime}{N}_{2,T}\left(\mathbf{S}_{0,T}\right)$. The conditional likelihood ratio (CLR) test of level $\alpha$ rejects $H_{0}$ when $LR_{T}(\mathbf{S}_{0,T})>\kappa_{\alpha}(N_{2,T}(\mathbf{S}_{0,T}))$, where the critical value function $\kappa_{\alpha}(\cdot)$ is defined such that $\kappa_{\alpha}(n_{2})$ is the $1-\alpha$ quantile of the large-sample conditional distribution of $LR_{T}(\mathbf{S}_{0,T})$ under $H_{0}$, given $N_{2,T}(\mathbf{S}_{0,T})=n_{2}$: \[ \frac{1}{2}\left(\mathcal{Z}_{q}'\mathcal{Z}_{q}-n_{2}'n_{2}+\sqrt{\left(\mathcal{Z}_{q}'\mathcal{Z}_{q}-n_{2}'n_{2}\right)^{2}+4(\mathcal{Z}_{q}'n_{2})^{2}}\right), \] where $\mathcal{Z}_{q}\sim\mathscr{N}(0,I_{q})$. The critical value function $\kappa_{\alpha}(\cdot)$ is approximated in moreira:2003. The LM and AR tests reject $H_{0}$ when $LM_{T}>\chi_{1}^{2}(1-\alpha)$ and $AR_{T}>\chi_{q}^{2}(1-\alpha)$, where $\chi_{q}^{2}(1-\alpha)$ denotes the $1-\alpha$ quantile of a chi-squared distribution with $q$ degrees of freedom.
When $\mathbf{S}_{0,T}$ is known the results of \textcolor{MyBlue}{Andrews et al.} andrews/moreira/stock:2006 imply that the CLR, LM and AR tests have limiting null rejection probabilities equal to $\alpha$ under weak IV asymptotics, $\theta=c/T^{1/2}$ for some nonstochastic $c\in\mathbb{R}^{q}$, under a weakening of Assumptions (ref)-(ref) below for which these assumptions need only hold pointwise in $\mathbf{S}_{T}$. These tests are asymptotically similar and therefore have asymptotically correct size in the presence of weak IVs.
For the case of an unknown sub-population, the identification-robust tests in the extant literature no longer apply because the set of instruments $C_{0,T}Z$ is unknown and must be estimated. In this section, we show how to form HAR CLR, LM and AR tests with correct asymptotic null rejection probabilities under both weak and strong IV asymptotics. To estimate the true sub-population $\mathbf{S}_{0,T}$ when constructing these tests let
Proposition (ref) in the supplement shows that the process $\{\overline{Z}(C_{T})'y\}_{\mathbf{S}_{T}\in\mathcal{S}}$ is sufficient for $(\beta,\theta')'$ in a canonical Gaussian setting analogous to that in \textcolor{MyBlue}{Andrews et al.} andrews/moreira/stock:2006 so that there is no loss in efficiency from using the unknown sub-population AR, LM and LR statistics, $LR_{T}(\widehat{\mathbf{S}}_{T})$, $LM_{T}(\widehat{\mathbf{S}}_{T})$ and $AR_{T}(\widehat{\mathbf{S}}_{T})$, which are only functions of the process $\{\overline{Z}(C_{T})'y\}_{\mathbf{S}_{T}\in\mathcal{S}}$.
We establish the asymptotic validity of the HAR CLR, LM and AR tests in the unknown sub-population setting under a weak set of high-level sufficient conditions on the IVs, exogenous variables and errors. Define $w\left(\mathbf{S}_{T}\right)=\left[C_{T}Z:X\right]$.
In Assumption (ref), $\mathrm{vec}\left(\cdot\right)$ denotes the vec operator. The quantities $Q\left(\cdot\right)$, $\Sigma_{v}$, and $\Psi\left(\cdot\right)$ are assumed to be unknown. Assumptions (ref)-(ref) hold under suitable conditions by a (uniform) law of large numbers. Assumption (ref) holds under suitable conditions by a functional central limit theorem. Assumptions (ref)-(ref) are consistent with non-normal, heteroskedastic, autocorrelated errors and IVs and regressors that may be random or non-random.\footnote{In the supplement we provide primitive sufficient conditions for Assumptions (ref)-(ref).}
We assume that we can consistently estimate $\Sigma_{v\overline{Z}}\left(\mathbf{S}\right)\equiv\Sigma_{v\overline{Z}}\left(\mathbf{S},\mathbf{S}\right)$ uniformly in $\mathbf{S}_{T}$.
Note that this assumption immediately implies the uniform consistency of $\widehat{\Sigma}_{N_{2}}(\mathbf{S}_{T})=\widehat{\Sigma}_{N_{2}}^{*}(\mathbf{S}_{T})-\widehat{\Sigma}_{N_{1}N_{2}}(\mathbf{S}_{T})\widehat{\Sigma}_{N_{1}}^{-1}(\mathbf{S}_{T})\widehat{\Sigma}_{N_{1}N_{2}}(\mathbf{S}_{T})'$ as well. Consistent estimators of $\Sigma_{v\overline{Z}}$ are HAC and DK-HAC estimators.\footnote{In the supplement we provide weak sufficient conditions, even allowing for certain forms of nonstationarity, that ensure this assumption holds.}
Finally, we impose a second-order stationarity condition for $v'_{t}b_{0}\overline{Z}_{t}\left(C_{T}\right)$ and $v'_{t}\Sigma_{v}^{-1}a_{0}\overline{Z}_{t}\left(C_{T}\right)$.
Assumption (ref) is implied by a uniform law of large numbers and functional central limit theorem for partial sum processes under second-order stationarity. Under weak IV asymptotics, $T^{-1}\widehat{\mathbf{S}}_{T}$ is not consistent for $\mathbf{S}_{0}$. Assumption (ref) is needed in order to show that $N_{1,T}(\cdot)$ and $N_{2,T}(\cdot)$ are asymptotically independent processes. Under strong IV asymptotics we can dispense with Assumption (ref) because $T^{-1}\widehat{\mathbf{S}}_{T}\overset{\mathbb{P}}{\rightarrow}\mathbf{S}_{0}$ and the limit of the processes $N_{1,T}(\cdot)$ and $N_{2,T}(\cdot)$ have zero covariance when evaluated at a fixed $\mathbf{S}_{0}$.
Define the LR, LM and AR statistics in this context according to (ref), replacing $\mathbf{S}_{0,T}$ with $\widehat{\mathbf{S}}_{T}$. We now establish the correct asymptotic null rejection probabilities of the sub-population-estimated plug-in HAR CLR, LM and AR tests under weak identification.
The key to establishing these asymptotic validity results is to show that each of the above statements hold conditional on the realization of $N_{2,T}(\cdot)$. This can be readily established from the facts that the stochastic processes $N_{1,T}(\cdot)$ and $N_{2,T}(\cdot)$ are asymptotically independent by construction, $\widehat{\mathbf{S}}_{T}$ is a function of $N_{2,T}(\cdot)$ and $N_{1,T}(\mathbf{S}_{T})\Rightarrow\mathscr{N}\left(0,\,I_{q}\right)$ under $H_{0}$.\footnote{In addition to identification-robust tests of $H_{0}$ vs $H_{1}$, since the causal interpretation of $\beta$ depends upon the sub-population $\mathbf{S}_{0,T}$, practitioners may wish to simultaneously report the result of these tests along with a corresponding estimate of the sub-population. More specifically, failure to reject $H_{0}$ should be interpreted as failure to reject that the estimand is equal to $\beta_{0}$, where the estimand is interpreted as a weighted average of the LATEs for the estimated sub-population $\widehat{\mathbf{S}}_{T}$. Given that the tests of $H_{0}$ remain asymptotically valid conditional on the realization of $N_{2,T}(\cdot)$ and the fact that $\widehat{\mathbf{S}}_{T}$ is a function of $N_{2,T}(\cdot)$, the tests remain asymptotically valid when interpreted conditional on the value of $\widehat{\mathbf{S}}_{T}$.}
We illustrate our methods by revisiting the identification of monetary policy effects in the framework of nakamura/steinsson:2018, introduced in Section (ref). They use a bivariate model (ref) to estimate the causal effect of $\widetilde{D}_{t}$ on $\widetilde{Y}_{t}$, employing both event-study and heteroskedasticity-based identification approaches. The dependent variable is the daily change in instantaneous U.S. Treasury forward rates. For the policy news $\widetilde{D}_{t}$ they use three variables: the daily change in nominal 2-Year Treasury yields, and the 30-minute or 1-day change in a “policy news” series\textemdash constructed as the first principal component of the unanticipated 30-minute changes in five selected interest rates. Heteroskedasticity-based identification assumes the variance of the monetary shock rises on FOMC announcement days, while the variance of other shocks remains constant {[}cf. eq. (ref){]}. FOMC dates define the policy sample $\mathbf{P}$, and analogous non-FOMC dates define the control sample $\mathbf{C}.$ We consider specifications where $\widetilde{D}_{t}$ is either the 30-minute policy news series or 1-day change in Treasury yields, and $\widetilde{Y}_{t}$ is either the nominal or real 2-Year instantaneous Treasury forward rate. Nakamura and Steinsson's instrument for $\widetilde{D}_{t}^{2}$ is defined as $Z_{t}=\mathbf{1}\left\{ t\in\mathbf{P}\right\} $, corresponding to the model in Section (ref). We focus on the same period: January 1, 2004, to March 19, 2014.
lewis:2020 recently analyzes this problem by developing a first-stage $F$-test for weak identification. He finds that weak identification is not rejected when $\widetilde{D}_{t}$ is the 1-day change in nominal 2-Year Treasury yields, but is strongly rejected when $\widetilde{D}_{t}$ is the 30-minute policy news series. This supports nakamura/steinsson:2018's nakamura/steinsson:2018 observation that the daily policy variable may suffer from weaker identification. Unlike nakamura/steinsson:2018, lewis:2020 estimates the model using GMM and does not impose the assumption that the non-monetary policy shock $\eta_{t}$ has equal variance across the treatment and control samples.
Section (ref) reports results of our test for full sample identification failure. Section (ref) presents causal effect estimates based on the most strongly-identified subsample. Section (ref) provides identification-robust inference results, and Section (ref) estimates compliers at the individual level and tests the exclusion restriction.
We present the results of our test for identification failure over all sub-populations from Section (ref) in Table (ref) considering values of $\pi_{L}$ from 0.6 to 1. For the 30-minute policy news variable, the $F_{T}^{*}$ statistic is very large and identification failure is rejected at any common significance level. This supports the finding in lewis:2020 and intuition in nakamura/steinsson:2018 that the 30-minute policy news variable leads to stronger identification in the full sample. In contrast, for the 1-day change in nominal Treasury yields, identification failure cannot be strongly rejected in the full sample: the $F_{T}^{*}$ statistic at $\pi_{L}=1$ (i.e., full sample) is only slightly larger than the 1% critical value. The $F_{T}^{*}$ statistic increases substantially as $\pi_{L}$ decreases and it is very far from the critical values. This is clear evidence that identification is much stronger over subsamples. At $\pi_{L}=0.9$ it reaches 33.87, clearly rejecting identification failure in the $\pi$-subsample (with $\pi=0.9$ or $0.95$) over which the supremum of $F_{T}\left(\mathbf{S}_{T}\right)$ is computed. The $F_{T}^{*}$ statistic increases monotonically with smaller $\pi_{L}$ due to the increasing number of partitions considered. For example, at $\pi_{L}=0.8$, $F_{T}^{*}$ is 54.78\textemdash nearly seven times the full sample value. Overall, the results indicate that strong identification may hold when using a 1-day window, but only within subsamples comprising at most 90% of the data. The weak identification reported by lewis:2020 using a 1-day window around FOMC announcements likely does not stem solely from volatility returning to normal after announcements. Rather, a small subsample (10\textendash 20% of the data) exhibits weak or failed identification, contributing to the weaker identification exhibited in the full sample.
We turn to estimation of $\pi_{0}$ and $\mathbf{S}_{0,T}$ using the methods from Section (ref), and then to estimating the LATE of monetary policy based on the strongly-identified subsample, $\widehat{\beta}(\mathbf{\widehat{S}}_{T,OLS})$, or simply, $\widehat{\pi}$-sample, where $\widehat{\pi}=|\widehat{\mathbf{S}}_{T,OLS}|/T$. We focus on $\widehat{\beta}(\widehat{\mathbf{S}}_{T,OLS})$; results using $\widehat{\beta}(\mathbf{\widehat{S}}_{T,FGLS})$ are similar. Figure (ref) plots the 1-day changes in 2-Year yields for the control and policy samples and highlights the regimes included in the strongly-identified subsample $\mathbf{\widehat{S}}_{T,OLS}$. The estimate $\widehat{\pi}=0.8$ implies that in 80% of the sample, the first-stage is strong and identification holds. In the control sample, the excluded periods include the first seven months of 2005 and the regime surrounding the financial crisis (2007-2009). As shown in the figure, volatility during the crisis period is much higher than in the rest of the control group and higher than the average volatility in the treatment group. This subsample appears to drive the apparent full sample weak identification. Since our method searches for maximum identification strength, it correctly excludes this period when computing $\pi$-LATE.\footnote{The other excluded period (January to July 2005) does not display obviously high volatility but shows some persistence, with a short-duration cluster below the mean toward the end.} The interpretation is that in both excluded regimes\textemdash especially during the financial crisis\textemdash market uncertainty was elevated even on non-FOMC days, violating the identification assumption.
We now estimate the causal effect of monetary policy using the $\widehat{\pi}$-sample, where by construction the LATE is most strongly-identified. We compare these results with full sample estimates obtained using two-stage least squares (TSLS) and GMM, following nakamura/steinsson:2018 and lewis:2020, respectively. Table (ref) presents the results. Starting with the full sample estimates: when the policy variable is the 30-minute policy news series, TSLS and GMM yield very similar point estimates for both nominal and real forward rates, and both are statistically significant using standard and robust confidence intervals.\footnote{The robust confidence intervals for the GMM estimates are based on the subset $K$-test in lewis:2020.}
As noted by lewis:2020, the assumption that non-monetary shocks have equal variance across treatment and control groups does not bias the TSLS estimates, as they closely match the GMM ones. One explanation is that the GMM estimate of $a$ (capturing reverse causality from forward rates to policy news) is both near zero and statistically significant (not reported). Since potential bias from this assumption is proportional to $a(\sigma_{\eta,P}^{2}-\sigma_{\eta,C}^{2}),$ and $a$ is close to zero, the resulting bias is negligible even if the variances $\sigma_{\eta,P}^{2}$ and $\sigma_{\eta,C}^{2}$ differ.
Turning to the case where the policy variable is the 1-day change in 2-Year Treasury yields, the TSLS and GMM estimates differ markedly from each other and from those based on the 30-minute policy news series. Notably, the GMM estimate of $\beta$ is negative for nominal forwards and positive for real forwards, but in neither case is it statistically significant\textemdash whether using standard or robust confidence intervals.
As discussed by lewis:2020, these estimates are difficult to interpret in economically meaningful terms. He also shows that the GMM estimates of $a$ are nonzero and proposed a second dimension of policy news to account for the findings. However, the opposing signs of $\beta$ across nominal and real forwards complicate this interpretation. Ultimately, he concludes that these results are inconsistent with nakamura/steinsson:2018's nakamura/steinsson:2018 “background noise” view of the non-monetary shock $\eta_{t}$ which assumes that its volatility remains unchanged between FOMC and non-FOMC days.
We contribute to this discussion by presenting TSLS and GMM estimates based on the most strongly-identified $\widehat{\pi}$-sample. We focus first on standard confidence intervals and defer weak identification-robust inference to Table (ref). The bottom panel of Table (ref) shows that, for the 30-minute policy news variable, the TSLS and GMM estimates, including their statistical significance, are virtually unchanged. As expected\textemdash given the apparent strong identification in the full sample\textemdash results are broadly similar when using the $\widehat{\pi}$-sample.\footnote{The confidence intervals in the $\widehat{\pi}$-sample are even slightly tighter.}
Finally, we turn to the $\widehat{\pi}$-sample estimates using the 1-day window for the policy. The GMM estimates differ sharply from those in the full sample: for both nominal and real forwards, they now have the same sign and are statistically significant. This suggests that the opposite signs reported by lewis:2020 likely stemmed from weak identification, rendering those estimates unreliable.\footnote{While the TSLS estimates are nearly unchanged from the full sample, this should not be taken as evidence of their reliability. Under weak IVs, their similarity to the $\widehat{\pi}$-sample results may simply be coincidental.} Notably, the GMM estimates are now similar in magnitude to those based on the 30-minute policy variable, supporting a more meaningful interpretation.\footnote{We also verified that the GMM estimate of $a$ is 0.70 for nominal forwards and -0.91 for real forwards. It is intuitive that the estimate of $a$ is close to zero when using a 30-minute window but significantly different from zero with a 1-day window. In the narrow 30-minute window around an FOMC announcement, reverse causality from $\widetilde{Y}_{t}$ to $\widetilde{D}_{t}$ is limited, as monetary news is more pronounced than other shocks\textemdash though some endogeneity may still arise from omitted factors affecting both. In contrast, over a full day, asset price movements can influence short-term interest rates, making reverse causality more likely.}
Overall, this analysis highlights the advantage of using the most strongly-identified $\widehat{\pi}$-sample. Given weak identification in the full sample when using 1-day Treasury yields as the policy variable, the corresponding estimates should be discarded. In contrast, evidence from the $\widehat{\pi}$-sample shows that TSLS and GMM produce similar, positive estimates for $\beta,$ consistent with monetary policy affecting real forward rates, as predicted by New Keynesian models, and supporting the existence of a forward guidance channel.\footnote{However, the results do not yet support a second meaningful dimension of news, as proposed by{ }lewis:2020, since the sign of the GMM estimate of $a$ is unstable across nominal and real forwards. Regarding nakamura/steinsson:2018's nakamura/steinsson:2018 “background noise” interpretation of non-monetary shocks, we find no clear evidence against it: in the $\widehat{\pi}$-sample, identification appears strong, and TSLS and GMM estimates consistently share the same sign and similar magnitudes.}
We apply the weak identification-robust tests proposed in Section (ref) and compare them to existing full sample tests $LM_{T}$ and $LR_{T}$.\footnote{We do not report the $AR_{T}$ test since for $q=1$ it is equivalent to the $LM_{T}$ test.} We test the the null hypothesis $H_{0}:\,\beta=0$ against $H_{1}:\,\beta\neq0$, and extend the analysis to include 5-Year forward rates, in addition to the 2-Year forwards. Results are shown in Table (ref). When the policy variable is the 30-minute policy news, identification is strong in the full sample. Accordingly, both the proposed and existing tests yield similar results: all tests reject at the 5% level for both nominal and real forwards. nakamura/steinsson:2018 showed that the effect of policy news peaks at the 2-Year maturity and declines with longer maturities. Consistent with this, we find weaker statistical significance for the 5-Year. In line with theoretical predictions, the long-run impact of monetary policy shocks on real interest rates (i.e., the 10 Year forwards) approaches zero (not reported). Our proposed tests confirm this, showing some rejection for the 5-Year real forwards but not for the 10-Year.
Let us instead consider the 1-day change in 2-Year yields as the policy variable. The existing $LM_{T}$ and $LR_{T}$ tests do not reject the null at any standard significance level for nominal forwards, and at the 1% level for real forwards. In contrast, our proposed tests based on $\widehat{\mathbf{S}}_{T}$ show much stronger rejections, aligning with the results using the 30-minute policy news series, which indicate a positive causal effect on 2-Year forwards.
We now identify compliers individually by applying Theorem (ref). Under heteroskedasticity-based identification, the sample rolling window averages in Theorem (ref) correspond to rolling window variances, i.e., $\overline{D}_{P,t,n_{1}}$ and $\overline{D}_{C,t,n_{0}}$ are equal to $\overline{\sigma}_{P,t,n_{1}}^{2}$ and $\overline{\sigma}_{C,t,n_{0}}^{2}$ in this context, where $\overline{\sigma}_{P,t,n_{1}}^{2}$ and $\overline{\sigma}_{C,t,n_{0}}^{2}$ are defined analogously but using $\tilde{D}_{t}^{2}$ for $D_{t}$.\footnote{More specifically, we have $\overline{\sigma}_{C,t_{0}-1,n_{0}}^{2}=\frac{1}{n_{0}}\sum_{s\in N_{0}\left(t_{0}\right)}\tilde{D}_{s}^{2},$ and $\overline{\sigma}_{P,t_{0},n_{1}}^{2}=\frac{1}{n_{1}}\sum_{s\in N_{1}\left(t_{0}\right)}\tilde{D}_{s}^{2}$.\textcolor{blue}{}} We use two-sided rolling windows with $n_{0}=101$ and $n_{1}=15$. For each $t_{0}$ we test the null hypothesis $H_{0}:\,\mathbb{E}(D_{t_{0}}^{2}\left(1\right))-\mathbb{E}(D_{t_{0}}^{2}\left(0\right))=0$ ($t_{0}$ is a non-complier) versus the one tailed alternative $H_{1}:\,\mathbb{E}(D_{t_{0}}^{2}\left(1\right))-\mathbb{E}(D_{t_{0}}^{2}\left(0\right))>0$ ($t_{0}$ is a complier). We use the $t$-statistic
where $J_{\mathrm{HAC},t_{0}}$ is the Newey-West estimator with $\left\lfloor n_{0}^{1/3}\right\rfloor $ lags applied to $\tilde{D}_{s}^{2}-n_{0}^{-1}\sum_{k\in N_{0}\left(t_{0}+1\right)}\tilde{D}_{k}^{2}$.
The results are shown in Figure (ref). Approximately 75% of observations are classified as compliers. The non-compliers are mostly concentrated in the period from 2010 to mid-2011, which corresponds to the early phase of the zero lower bound (ZLB) period following the 2008\textendash 09 recession. During this time, the Fed relied primarily on qualitative forward guidance\textemdash e.g., stating that economic conditions were "likely to warrant exceptionally low levels of the federal funds rate for some time." In August 2011, the Fed shifted to more explicit, calendar-based guidance, stating that such conditions were "likely to warrant exceptionally low levels of the federal funds rate at least through mid-2013." Thus, the non-complier period aligns with the phase of the ZLB when forward guidance was less aggressive as the policy announcements by then only imply a near zero-rate horizon for the following three to four quarters, significantly shorter than what the ZLB constraint would actually have implied.\footnote{The set of compliers does not coincide with the set of observations in the strongly-identified $\widehat{\pi}$-sample. However, this does not necessarily imply a violation of monotonicity {[}cf. Proposition (ref){]}. First, the complier status is determined via a $t$-test whereas the strongly-identified $\widehat{\pi}$-sample is determined via estimation. Second, the complier status is determined by the rolling window variances at each $t$, whereas inclusion in the $\widehat{\pi}$-sample depends on how these variances contribute to the average volatility in the control sample relative to that in the policy sample.}
Finally, we use Theorem (ref) and Proposition (ref) to test the exclusion restriction (cf. Assumption (ref)). We consider the whole set of compliers $\mathcal{NC}.$ We test the null hypothesis that the exclusion restriction holds by using the following $t$-statistic:
where $\overline{Y}_{\mathcal{NC}_{\mathbf{P}}^ {}}=\frac{1}{|\mathcal{NC}_{\mathbf{P}}^ {}|}\sum_{t\in\mathcal{NC}_{\mathbf{P}}^ {}}Y_{t}$, $\overline{Y}_{\mathcal{NC}_{\mathbf{C}}^ {}}=\frac{1}{|\mathcal{NC}_{\mathbf{C}}^ {}|}\sum_{t\in\mathcal{NC}_{\mathbf{C}}^ {}}Y_{t}$, $Y_{t}=\tilde{D}_{t}\tilde{Y}_{t}$ and $J_{\mathrm{HAC},\mathcal{NC}^{s}}$ is the Newey-West estimator applied to $\overline{Y}_{\mathcal{NC}_{\mathbf{P}}^ {}}-\overline{Y}_{\mathcal{NC}_{\mathbf{C}}^ {}}$. For the real (nominal) 2-Year forward rate, we find $t_{\mathrm{exclusion}}=0.91$ ($t_{\mathrm{exclusion}}=1.02$), and thus fail to reject the exclusion restriction.
This paper discusses identification, estimation and inference on dynamic LATE. We show that compliers can be identified individually and the exclusion restriction can be tested using a $t$-test. While weak identification is common in the full sample in practice, strong identification often appears to hold in a sizable subsample. We propose a method to isolate this strongly-identified subsample, enabling consistent estimation and inference.
\paragraph*{Supplemental Materials:}
The online supplement {[}cf. \textcolor{MyBlue}{Casini et al.} casini/mccloskey/pala/rolla_Dynamic_Late_Supp{]} includes Monte Carlo simulations, proofs of the results of Sections (ref)-(ref) and (ref). The non-online supplement {[}cf. \textcolor{MyBlue}{Casini et al.} casini/mccloskey/pala/rolla_Dynamic_Late_Supp_Not_Online{]} contains the theoretical results and corresponding proofs for the estimators in Section (ref) and additional results.
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