Anticipation and Consumption Chapter 1

1 Introduction Many policies throughout the world involve directly providing households with cash. Non-contributory cash transfer programs reach over 700 million households in over 130 countries, accounting for the largest share of spending among social safety net programs in developing countries (Honorati, Gentilini and Yemtsov, 2015). Direct cash payments also play an important role in developed economies to restore growth during economic downturns; the United States, for example, spent almost 1 percent of GDP in 2008 to put $120 billion in the hands of households at the onset of the Great Recession. These policies use the same tool for contrasting goals: long-term objectives such as poverty alleviation, and short-term objectives such as boosting consumer spending. Their effectiveness in achieving these goals has been an active subject of debate by both academics and policymakers (Greenstone and Looney, 2012; Ingram and McArthur, 2018). The life-cycle and permanent income models (Modigliani and Brumberg, 1954; Friedman, 1957) prescribe that households may respond to “unanticipated” changes in income but should respond little, if at all, to “anticipated” changes. Yet effective policymaking often requires households to behave in ways that deviate from this prediction. Fiscal stimulus policies that announce direct payments to households best exemplify the tension that can arise between policy objectives and this theoretical benchmark. More generally, the use of cash payments to achieve different policy goals further highlights the need to understand the design of transfer systems both theoretically and empirically. The basic economic intuition that spending responses depend on the timing of information about changes in income suggests an important role for anticipation as a policy instrument. Perhaps surprisingly then, very little empirical evidence characterizes the impulse response of spending to transitory variation in income arriving at different time horizons, which provides a crucial input for evaluating the general equilibrium effects of fiscal shocks and policies (Auclert, Rognlie and Straub, 2018). The literature instead considers “two distinct questions,” namely how consumption responds to anticipated income changes and how consumption responds to unexpected shocks (Jappelli and Pistaferri, 2010). This dichotomy between anticipated and unanticipated income changes may be misleading if consumption responses depend on the duration between when a household learns about an income change and when the income change occurs. This paper investigates how the time horizon over which a household anticipates receiving a transfer impacts spending decisions. We systematically survey the literature and arrive at three settings that consist of exogenous variation in when households learn about a windfall payment relative to when they receive it.1 The first consists of a natural experiment provided by the randomized disbursement dates of a U.S. fiscal stimulus payment (Parker et al., 2013). Characterizing how consumption responds before, at the time of, and after income shocks anticipated over different time horizons allows us to test central predictions of theories of consumption. The second and third involve variation induced by randomized controlled trials (RCTs) on unconditional cash transfers Appendix A.1 documents that, to the best of our knowledge, other settings with consumption data lack exogenous variation in the timing of information. 1 1 in Kenya (Haushofer and Shapiro, 2016) and Malawi (Brune et al., 2017), respectively. Although these settings have been explored in previous work, our empirical findings in each case—greater consumption responses among households that receive payments sooner after announcement—are new. In our first empirical setting, we use Nielsen Consumer Panel data to study consumption expenditure responses to the tax rebates sent to low- and middle-income American households as part of the Economic Stimulus Act of 2008 (Broda and Parker, 2014; Parker, 2017). Our identification strategy relies on the fact that the last two digits of the recipient’s Social Security number (SSN) determined the timing of payment. Previous papers use this strategy to estimate an impulse response function of consumption to the receipt of payment by comparing households a given number of weeks since receiving a stimulus payment with households that will receive payments later. By contrast, our work additionally exploits variation in waiting times across households. The results show that consumption responds strongly to the receipt of additional income, with a magnitude that depends on the duration of anticipation. First, consistent with previous work, we find no evidence that households increase spending in advance of receiving their stimulus payment. Second, we find that households in the earliest payment group increase spending in the month after receiving their payment by twice as much as the average household does. Third, faster disbursement of stimulus payments leads to a continuing shift in spending behavior: In a given calendar week, spending among households in earlier payment groups exceeds that of households in later payment groups who have received their payment more recently. These patterns emerge for households with different levels of liquidity, financial planning tendencies, and savings habits. Additional tests rule out explanations relying on a direct relationship between waiting time and spending needs or saving ability as well as those relying on intrahousehold or social interactions. In the next pair of settings, we present new analyses of raw data from published RCTs. The first is an impact evaluation of unconditional cash transfers by a non-governmental organization (GiveDirectly) using a sample of households in Rarieda, Kenya (Haushofer and Shapiro, 2016). The second is a windfall experiment in partnership with a commercial bank (NBS Bank) using a sample of households in villages near Mulanje, Malawi to understand how households manage cash without formal financial products (Brune et al., 2017). The Kenya study contains a set of treatments to compare lump-sum payments with a series of nine monthly installments. To facilitate that comparison, the lump-sum transfers take place at randomly selected but pre-announced times within nine months of enrollment in the program. This previously unexploited random variation in the timing of lump-sum transfers thus provides an ideal experiment for evaluating the role of anticipation. Among households that wait longer to receive their transfer payments, we find increases in savings and investments. We find a concave relationship between anticipation duration and these outcomes, showing substantial consequences of the shortest waiting times. The Malawi study contains payment-delay treatments to understand whether time preferences provide scope for financial products such as savings defaults to improve welfare. While the authors 2 find little evidence that delaying payments affects expenditure, our analysis leads to new conclusions. In particular, we find a significant increase in savings in response to receiving a delayed windfall payment. Effects are largely driven by in-kind savings, a common form of savings that is incidentally included in measures of expenditure. A model based on mental accounting explains the four key patterns in our data. We observe (i) a lack of consumption response to information about future payments (excess smoothness) and (ii) a strong response to receiving anticipated payments (excess sensitivity), including among households that do not face binding liquidity constraints, which implies that households treat windfall income differently from their current wealth (Shefrin and Thaler, 1988). In addition, our data show (iii) differential consumption response to additional income based on the duration of anticipation, and (iv) greater spending among households in earlier payment groups conditional on calendar week, which requires the way that households make spending allocations out of windfall income to depend on the time dimension. To describe how consumers mentally categorize windfalls, we present a model in which the MPC depends both on the magnitude of the windfall and on how long the decision maker has known about the windfall. This extends the seminal work on the behavioral life-cycle hypothesis (Shefrin and Thaler, 1988), which posits that spending decisions depend only on the magnitude of income changes. Shefrin and Thaler (1988) describe wealth as separated into three mental accounts (current income, current assets, and future income) each having a different MPC, with larger windfalls feeling more “wealth-like” and with a tendency to “leave perceived ‘wealth’ alone.” Our approach highlights how the duration of anticipation also plays an important role in determining how wealth-like a windfall feels to consumers, so that the time dimension matters beyond the classification of income as “future” vs. “current” (or “anticipated” vs. “unanticipated”). As multiple possible channels can operate in conjunction with mental accounting to generate MPCs that exhibit this novel form of history dependence, we use a reduced-form approach (Mullainathan, Schwartzstein and Congdon, 2012) to model the dependence of the MPC on the time dimension, which allows us to characterize robust policy implications of our findings without heavily relying on a specific set of modeling assumptions.2 The estimates of the model match not only the monthly and weekly spending moments in our data but also the MPCs reported in related work showing that one-time stimulus payments boost spending by more than equivalent reductions in income tax withholding (Sahm, Shapiro and Slemrod, 2012). We discuss implications for the design of fiscal stimulus policies, focusing on payment frequency, amounts, and targeting. Our empirical results in the domain of tax rebates make several contributions to the extensive literature in household finance, public economics, and macroeconomics on tests of intertemporal consumption models.3 First, we formulate the predictions of the benchmark model through the intertemporal marginal propensity to consume (iMPC) framework, including a stationarity We illustrate how our approach can capture channels involving reference dependence (Kőszegi and Rabin, 2009; Thakral and Tô, 2021), self-control (Noor, 2007), planning (Gollwitzer, 1993), attention (Bordalo, Gennaioli and Shleifer, 2020), utility from anticipation (Thakral and Tô, 2020), or uncertainty about optimal actions (Ilut and Valchev, forthcoming); see Appendix E.1. 3 The most closely related papers in this literature to ours are those that use household-level data to estimate the consumption impacts of stimulus payments (e.g., Johnson, Parker and Souleles, 2006; Parker et al., 2013). 2 3 property—that the MPC following a shock does not depend on when the shock occurs—that does not appear in previous work. We also elucidate conditions under which testing the stationarity property can distinguish among various theories of consumption. Second, our work goes beyond the anticipated-unanticipated distinction by positing the importance of the duration over which an income shock is anticipated. Our approach is therefore able to reconcile seemingly conflicting results that consumption responds to anticipated payments in some settings but not others by emphasizing the timing of information and the time horizon over which households anticipate changes in income.4 Third, we build on existing empirical work methodologically by using a two-step estimation approach.5 Finally, our findings point toward a novel role for the timing of information in designing effective stabilization policies. In addition, our paper contributes to existing work that estimates MPCs. Previous research uses hypothetical survey (e.g., Shapiro, Slemrod et al., 1995; Shapiro and Slemrod, 2003; Jappelli and Pistaferri, 2014; Christelis et al., 2019; Fuster, Kaplan and Zafar, 2021), quasi-experimental (e.g., Parker, 1999; Souleles, 1999, 2002; Johnson, Parker and Souleles, 2006), and structural (e.g., Blundell, Pistaferri and Preston, 2008) approaches to estimate MPCs. The resulting MPCs constitute sufficient statistics for partial equilibrium analysis of fiscal policy (Kaplan and Violante, 2014) and monetary policy (Auclert, 2019). Our work fits within the quasi-experimental approach but provides evidence on intertemporal MPCs, which characterize general equilibrium responses to fiscal shocks (Auclert, Rognlie and Straub, 2018) and monetary policy (Wolf, 2021). This also relates to a broader literature in macroeconomics establishing the importance of current consumption responses to future shocks for the effectiveness of fiscal policy (Hagedorn, Manovskii and Mitman, 2019) and monetary policy (Kaplan, Moll and Violante, 2018).6 This paper also relates to an expansive body of research in development economics on cash transfers as a tool for alleviating poverty (Hanlon, Barrientos and Hulme, 2012). A systematic review of experiments on cash transfers yields a long list of design features (Bastagli et al., 2016): complementary interventions, conditionality, duration, frequency, main recipient, predictability and reliability, size, and timing of transfer payments.7 We propose a new design feature—waiting times—and evaluate its impact in multiple settings.8 A unique aspect of our work is the use of existing data from published studies that aim to answer a different set of research questions from See Appendix A.2 for a meta-analysis of consumption responses to “anticipated” payments, which shows stronger evidence of deviations from consumption smoothing for payments that follow a shorter anticipation duration. 5 Gardner (2021) also proposes this methodology in independent and contemporaneous work. 6 See Fagereng, Holm and Natvik (2021) for further references and discussion on how the “dynamics of households’ consumption responses to windfall income are essential to address longstanding macroeconomic questions about shock propagation and economic policy.” 7 Timing refers to making funds available to households at specific instances when needs arise, such as the time to pay school fees or to acquire agricultural inputs (Duflo, Kremer and Robinson, 2011). 8 Several experiments analyze the effect of waiting times in one-time decisions among small, well-defined choice sets involving monetary amounts, specific consumption goods, or effort allocations at different time periods (Dai and Fishbach, 2013; DeJarnette, 2020; Imas, Kuhn and Mironova, forthcoming). These studies find that waiting before making a decision causes subjects to prefer larger delayed payoffs over smaller sooner payoffs. Our analysis of waiting times in the case of cash transfers poses the conceptually distinct question of how receiving a payment with a longer or shorter anticipated delay affects spending and saving decisions. 4 4 our paper. Our empirical approach has several notable advantages. First, analyzing experimental as well as naturally occurring variation in policy-relevant contexts provides greater generalizability (Rodrik, 2009) and makes progress toward mitigating concerns regarding the external validity of laboratory experiments and randomized controlled trials (Duflo, Glennerster and Kremer, 2007). Second, and relatedly, our approach exemplifies how experiments can yield more general lessons when combined with theory (Banerjee, 2005; Mookherjee, 2005; Duflo, Glennerster and Kremer, 2007; Deaton and Cartwright, 2018). Third, the use of existing experiments reduces unintended researcher bias that may arise in designing and implementing new experiments (Rosenthal and Fode, 1963). Fourth, relying on strong existing institutions to generate credible variation in payment timing as opposed to running new experiments limits the possible influence of a lack of trust, which can distort conclusions resulting from variation in payment timing (Beam et al., 2022). Fifth, while many studies on MPCs and mental accounting make use of hypothetical surveys (Shefrin and Thaler, 1988; Fuster, Kaplan and Zafar, 2021), research in psychology suggests that survey-based approaches may fail to capture the effects we analyze since “mimicry of the passage of time is extremely difficult to accomplish in a questionnaire study” (Arkes et al., 1994).9 Finally, our approach makes the conceptual contribution of highlighting the connection between disparate areas of work that study fiscal policy in high-income countries and cash transfer programs in developing countries (also see Egger et al. forthcoming) and analyzing them in parallel. Our work also has significant implications for models of mental accounting. Existing theories leave unresolved the question of how consumers allocate funds to different mental accounts and whether the time dimension matters beyond “future income” and “current income.” Correspondingly, research on how consumption responds to changes in income treats anticipated and unanticipated changes as dichotomous (Jappelli and Pistaferri, 2010). Our results shed light on the dynamics of the mental-accounting process by which consumers classify additional income differently based on its source. Theoretical models of mental accounting (Galperti, 2019; Kőszegi and Matějka, 2020; Lian, 2021) shed light on uses of income in the form of budgets (e.g., for different goods, categories of goods, or total expenditure); however, these models cannot explain how consumers distinguish between different sources of income. Existing empirical models of mental accounting capture the intuition behind violations of fungibility in classifying funds based on their uses (“gas money” in Hastings and Shapiro 2013) or sources (“food money” in Hastings and Shapiro 2018) in static environments but do not consider how consumers set or revise their categorizations. We complement the existing literature by incorporating dynamics and thus enriching the description of the mental-accounting process. Our work also complements lab experiments demonstrating that As Arkes et al. (1994) elaborate, “we tried to manipulate anticipation in a questionnaire. This was a very difficult thing to do. We found ourselves writing questionnaires for the anticipated group that contained lines like, ‘Two months pass during which you anticipate your rebate check.’ While subjects are reading that sentence, only 5 s pass, not 2 months. The point is that the mimicry of the passage of time is extremely difficult to accomplish in a questionnaire study. The actual passage of time may be necessary for anticipated funds to be ‘worked into’ an account, thereby making them less spendable.... Our recommendation is that “real-time” studies rather than questionnaire studies may be the best way to test the role of anticipation in the spending of windfall gains.” 9 5 decision makers exercise some discretion in assigning expenses to different mental accounts, i.e., that mental accounts can be flexible (Soman and Cheema, 2001; Soman and Gourville, 2001; Cheema and Soman, 2006), by contributing policy-relevant evidence of flexibility in how decision makers classify additional income. This suggests that models elucidating how decision makers move money between different mental accounts or further considering the time dimension may provide additional insights. The paper proceeds as follows. Section 2 presents an organizing framework for our empirical analyses. Section 3 analyzes consumer responses to the timing of the 2008 Economic Stimulus Payments in the US. Section 4 and Section 5 analyze the timing of payments in cash transfer experiments in Kenya and Malawi, respectively. Section 6 presents and estimates a mental-accounting model to interpret our results and discuss their implications. Section 7 concludes. 2 Framework for interpreting consumption patterns We start by describing how consumption responds to predictable income changes in a standard benchmark model in which agents choose consumption to maximize discounted expected utility subject to an intertemporal budget constraint (Deaton et al., 1992). We enumerate the model’s core predictions, including a new stationarity property that we define, and describe conditions under which testing the stationarity property can distinguish among various theories of consumption. In particular, we establish that when no anticipatory spending occurs in response to a future income shock, a violation of stationarity rejects forward-looking theories of consumption. We then use the framework of intertemporal marginal propensities to consume (Auclert, Rognlie and Straub, 2018) to define the empirical quantities of interest, state our hypotheses, and characterize the empirical strategies. 2.1 Predictions of benchmark model With a time-separable utility function 𝑢(⋅), assuming that consumers can borrow and lend at interest rate 𝑟 and have intertemporal discount rate 𝛿, consumption 𝑐𝑖,𝑡 for individual 𝑖 at time 1 𝑡 satisfies the standard Euler equation: 𝑢′ (𝑐𝑖,𝑡 ) = 1+𝛿 𝔼𝑡 [(1 + 𝑟)𝑢′ (𝑐𝑖,𝑡+1 )]. If the interest rate equals the intertemporal discount rate, then marginal utility follows a martingale process: 𝑢′ (𝑐𝑖,𝑡 ) = 𝔼𝑡 [𝑢′ (𝑐𝑖,𝑡+1 )]. In other words, given the information available in period 𝑡, the individual chooses 𝑐𝑖,𝑡 to equate the marginal utility of present consumption with the expected marginal utility of future consumption. Any change in the marginal utility of consumption from period 𝑡 to period 𝑡 + 1 must therefore result from new information in period 𝑡 + 1. In particular, past information cannot predict changes in marginal utility: Consumers incorporate expectations of income changes in their optimal consumption plans as soon as they learn about such changes, and the marginal utility of consumption does not change when predictable changes in income occur. This benchmark model thus makes a clear prediction about the consumption response to a transitory income shock: Upon learning about a transitory income shock, consumption changes 6 immediately and remains constant thereafter, with individuals consuming only the annuity value of the income shock (Jappelli and Pistaferri, 2010, 2017). This has straightforward implications for how consumption responds before the shock, at the time of the shock, and after the shock: Implication 1: Upon learning about the shock (period 0), consumption immediately changes, with no further changes before the shock occurs. Implication 2: Consumption does not change from the period preceding the shock to the period when the shock occurs (period 𝑡 − 1 to period 𝑡). Implication 3: The marginal propensity to consume in the periods following the shock does not depend on when the shock occurs. In this case, as in “the Barro (1974) definition of Ricardian equivalence, the time path of (lump-sum) taxes used to finance any given fiscal expenditure is irrelevant for consumption” (Wolf, 2021). Canonical tests of theories of consumption focus on the first two implications, using the term excess smoothness to describe a failure of Implication 1 (Deaton, 1987; West, 1988; Campbell and Deaton, 1989) and the term excess sensitivity to describe a failure of Implication 2 (Hall, 1978; Flavin, 1981). The third implication is the main subject of this paper. We propose the term stationarity to describe Implication 3 and the term non-stationarity to describe its failure.10 Several factors help explain why Implication 3, despite its simplicity, does not receive attention in previous work.11 First, this prediction holds under a large class of alternative models, including models that accommodate failures of Implications 1 and 2 (see Section 2.2). Second, testing Implication 3 imposes more demanding data requirements (see Section 2.3). Third, the theoretical framework that clarifies its importance for macroeconomic policy has only recently been developed (Auclert, Rognlie and Straub 2018; Wolf 2021; also see Section 2.3). 2.2 Predictions of alternative models The benchmark model above captures the basic intuition of the life-cycle and permanent income hypothesis (Modigliani and Brumberg, 1954; Friedman, 1957; Hall, 1978) that consumption responds little, if at all, to anticipated income changes. Likewise, in models that incorporate precautionary savings (Leland, 1968; Sandmo, 1970; Dreze and Modigliani, 1972), e.g., due to incomplete markets and income risk, consumers use savings to smooth income fluctuations. In these models, Implications 1–3 continue to hold. Implications 1 and 2 may fail to hold in models that incorporate liquidity constraints (Hayashi, 1985; Zeldes, 1989), e.g., due to imperfect credit markets, and therefore also in models that combine 10 Analogously, the stationarity property in the decision theory literature states that intertemporal preferences do not change when shifting a tradeoff in time (Koopmans, 1960; Fishburn and Rubinstein, 1982; Halevy, 2015). 11 As Jappelli and Pistaferri (2017, p. 149) note in their textbook when discussing excess sensitivity, “Another factor that is potentially relevant but neglected in the literature is the time that elapses between the announcement and the actual income change.” 7 precautionary saving motives and liquidity constraints (Aiyagari, 1994) such as buffer-stock models (Deaton, 1991; Besley, 1995; Carroll, 1997). Even if Implications 1 and 2 fail, Implication 3 continues to hold when no anticipatory consumption takes place because these models predict that consumers respond to changes anticipated over any duration the same as they would to an unexpected income change. Of course, models based on liquidity constraints can only explain violations of Implications 1 and 2 for a subset of consumers: They explain neither the lack of an aggregate response to information about future income changes nor the evidence that households with high levels of liquidity also respond to predictable income changes (Olafsson and Pagel, 2018; Kueng, 2018; Ganong and Noel, 2019; McDowall, 2019; Baugh et al., 2021).12 The same holds for a large class of models that explain excess sensitivity by adding heterogeneity, for example in discount factors (Krusell and Smith, 1998) or by adding a fraction of “rule of thumb” consumers (Campbell and Mankiw, 1989). This also applies to models with wealthy hand-to-mouth agents who hold illiquid assets that have transaction costs (Kaplan and Violante, 2014) and models with consumption adjustment costs more generally (Grossman and Laroque, 1990; Flavin and Nakagawa, 2008). These extensions of the benchmark model cannot explain violations of Implication 1 in the aggregate or violations of Implication 2 for households with liquidity. A key feature of all the models discussed above is that consumption decisions are forward-looking (Browning and Lusardi, 1996). This also applies to many popular extensions incorporating persistent household behavioral characteristics. For example, models of time-inconsistent preferences (Laibson, 1997; Angeletos et al., 2001), temptation (Gul and Pesendorfer, 2004; Bucciol, 2012), and reference dependence (Kőszegi and Rabin, 2009; Pagel, 2017) maintain forward-looking decision making (see Appendix E.3). Under the wide range of theories in which consumers make forward-looking decisions, when households do not respond to information about future income changes, consumers react to predictable income changes as if those changes were unexpected. In other words, Implication 3 holds in a broad class of models in which Implications 1 and 2 fail. Implication 3 therefore distinguishes forward-looking behavior from alternatives. A violation of Implication 3 requires a theory that incorporates backward-looking elements; we return to this discussion in Section 6. 2.3 Intertemporal MPCs The general equilibrium effects and policy implications of failures of Implications 1–3 depend on a set of empirical quantities that Auclert, Rognlie and Straub (2018) refer to as the intertemporal marginal propensities to consume (iMPCs). Letting 𝐶𝑡 and 𝑍𝑡 denote period-𝑡 aggregate consumption and real after-tax income, respectively, define the intertemporal marginal propensities to consume as 𝑀𝑡,𝑠 ≔ 𝜕𝐶𝑡 . 𝜕𝑍𝑠 The first column (𝑀𝑡,0 )𝑡 of the resulting iMPC matrix captures the impulse These papers present evidence from personal finance apps or household financial accounts. Also see earlier evidence using survey data, e.g., Poterba (1988); Heim (2007); Mertens and Ravn (2012); Stephens and Unayama (2011); Broda and Parker (2014). 12 8 response of consumption to an unexpected increase in income. The 𝑠th column, (𝑀𝑡,𝑠 )𝑡 , describes how consumption changes in response to an additional unit of income that is known as of period 0 to arrive in period 𝑠. In other words, 𝑠 = 0 corresponds to an unanticipated windfall and 𝑠 > 0 corresponds to an anticipated windfall. Varying 𝑠 corresponds to varying the duration of anticipation of an income shock. The quantity 𝐴𝑠 ≔ ∑𝑡<𝑠 𝑀𝑡,𝑠 represents the total anticipatory spending response, with 𝑀0,𝑠 being the immediate change in consumption that occurs upon learning 𝑠+𝑡−1 about the additional period-𝑠 income. The quantity Γ𝑠𝑡 ≔ ∑𝑡′=𝑠 𝑀𝑡′,𝑠 captures the cumulative 𝑡-period spending response upon receiving additional income in period 𝑠, and Γ𝑠1 = 𝑀𝑠,𝑠 represents the spending response on impact. Stated in the iMPC framework, failures of Implications 1–3 correspond to the following: 1. Excess smoothness—No change in spending upon learning about a windfall: 𝑀0,𝑠 = 0. 2. Excess sensitivity—Increase in spending after receiving an anticipated windfall: 𝑀𝑠,𝑠 > 𝑀𝑠−1,𝑠 . 3. Non-stationarity—Spending responses upon receiving additional income depend on the duration of anticipation: Γ𝑠𝑡 is not independent of 𝑠. Testing these implications requires observing how consumption changes in response to news about future income (Implication 1) and the onset of previously expected changes in income (Implications 2 and 3). Moreover, testing Implication 3 requires exogenous variation in 𝑠, i.e., the duration between when a consumer learns about an income shock and when the shock occurs. As Section 2.2 highlights, when no anticipatory spending occurs, testing Implication 3 provides a way to differentiate between classes of consumption theories based on whether they impose forward-looking behavior. We cannot rely on existing empirical estimates of the iMPC matrix to test the stationarity property (Implication 3). Existing estimates use exogenous variation to estimate the first column of this matrix (𝑀𝑡,0 , the impulse response of spending to an unanticipated increase in income) and calibrate a heterogeneous-agent model with illiquid assets to extrapolate the response to future anticipated income shocks (Auclert, Rognlie and Straub, 2018). Our systematic survey of the literature reveals three settings with exogenous variation in the timing of payment (see Appendix A.1), which we analyze in Sections 3 to 5. We also present results from a meta-analysis of the literature estimating MPCs in response to anticipated payments, examining how estimated consumption responses vary with the time horizon over which households anticipate receiving a payment, in Appendix A.2. 3 Tax rebates in the US This section analyzes our first empirical setting: the natural experiment provided by the randomized disbursement dates of the 2008 Economic Stimulus Payments (Parker et al., 2013; Broda and Parker, 2014; Parker, 2017). 9 3.1 Setting In response to the start of the recession in December 2007, the U.S. federal government approved an economic stimulus package in February 2008. All households with positive net income tax liability or at least $3,000 of qualifying income (Social Security, Veterans Affairs, or Railroad Retirement benefits) in 2007 were eligible for the Economic Stimulus Payments (ESPs). In total, about 130 million U.S. tax filers received approximately $100 billion in tax rebates. Eligible taxpayers received a base payment of $600 ($1,200 for couples filing jointly) if their 2007 federal income tax liability exceeded that amount. Those with tax liabilities between $300 and $600 ($600 and $1,200 for couples) received a base payment equal to their tax liability, and those with tax liabilities of less than $300 ($600 for couples filing jointly) received a base payment of $300 ($600 for couples). Households received an additional $300 for each child that qualified for the child tax credit in 2007. Payments were reduced by 5 percent of the amount by which adjusted gross income exceeded $75,000 ($150,000 for couples). Payment dates followed a pre-announced timeline. The Internal Revenue Service (IRS) announced a disbursement schedule on March 17, with the earliest payments scheduled for the first week of May and further batches of payments scheduled in the following weeks. Appendix Table 3 shows the ESP disbursement schedule for on-time filers.13 Although the payment schedule and amounts were known in advance, households received notification letters from the IRS several days prior to their payment date. Payment dates were staggered because of the infeasibility of mailing all notification letters at the same time. The last two digits of a taxpayer’s Social Security Number (SSN), which are effectively randomly assigned, determined their scheduled payment date.14 On April 25, President Bush stated that the Treasury would start distributing stimulus payments several days earlier than expected, consistent with households in the earliest payment group treating the payments as a surprise (Kaplan and Violante, 2014). The 2008 ESPs were the first large tax rebate to use electronic funds transfers (EFTs). About 80 million individual income tax returns were filed electronically in 2007, and tax filers who had provided the IRS with a personal bank account number for their income tax refunds received ESPs through direct deposit into their bank accounts. For tax returns that either provided no bank information or a tax preparer’s bank information (e.g., due to a refund anticipation loan, or due to using the refund amount to pay tax preparation fees), the IRS sent paper checks in the mail. 3.2 Data A multi-wave survey designed by Broda and Parker (2014) provides information about stimulus payments linked with detailed consumer expenditure data from the Nielsen Consumer Panel (NCP, formerly Homescan Consumer Panel). 13 See Martinez, Meier and Sprenger (2017) for evidence that the 2008 ESPs induce earlier filing in a sample of low-income tax filers. 14 SSNs assigned prior to June 25, 2011 consist of an area number (first three digits), a group number (middle two digits), and a sequentially assigned serial number (last four digits). The serial number is assigned sequentially within each group. 10 The NCP data contain information on household demographics (e.g., household size and composition, income, and race) as well as daily spending of about 60,000 active households collected electronically from handheld barcode scanners. NCP households track spending on household items that primarily fall in the grocery, drugstore, and mass-merchandise sectors (see Broda and Weinstein 2010 for additional information). The spending data are aggregated to a weekly level to line up with the frequency of ESP disbursement. The survey asks households whether they received a tax rebate via direct deposit or check, the dollar amount, the month and day they received their payment, and several questions related to general household financial planning. About 48,000 households provided responses to the survey, of which about 39,000 report receiving a stimulus payment. Among these, Broda and Parker (2014) note that some households do not report a payment date, report a payment date outside the randomized disbursement period, or provide inconsistent responses across multiple waves of the survey. Removing such observations, the remaining sample consists of about 29,000 households. We obtain the same analysis sample thanks to the replication files provided by Parker (2017). We further restrict the sample to households that report receiving a stimulus payment of at least $300. We interpret our results as internally valid estimates for the subsample of NCP panelists or the population that they represent (Bronnenberg et al., 2015). To examine the consistency of payment dates in our sample with the randomization, we test whether households receiving ESPs at different times have similar characteristics in Appendix B.1. The sample of households receiving ESPs by direct deposit appears to be randomly distributed across the scheduled payment dates in the first three weeks of May (Appendix Table 4). However, among the sample of households receiving ESPs by paper check, our balance tests (Appendix Table 5) reveal systematic differences by payment date across a wide range of characteristics (see Appendix B.1 for further discussion). Our analysis therefore focuses on the sample of households receiving payments by direct deposit. 3.3 Estimation 3.3.1 Methodology The goal of this section is to develop an econometric framework for investigating the relationship between anticipation duration and expenditures induced by the tax rebate. To facilitate the exposition, we begin by describing our empirical strategy as applied to the standard question in this literature: estimating the impulse response function of consumption to the receipt of payment. This allows for a test of predictions (i) and (ii) from the framework in Section 2. Credible identification hinges on the presence of not-yet-treated units for constructing counterfactuals: Under random assignment of treatment timing, causal estimates obtain from comparing households a given number of weeks since receiving a stimulus payment with households that will receive payments later. Our analysis therefore focuses primarily on shorter-term impacts. We use a two-step estimation approach. First we estimate time and household fixed effects independently of the causal effect of treatment by using only pre-treatment data. Then we estimate 11 dynamic treatment effects—i.e., the impact on spending 𝑘 periods after receiving an ESP for 𝑘 ≥ 0—after partialling out the estimated time and household fixed effects. Formally, denote by 𝐸𝑖 the time period of the event that 𝑖 becomes treated, let 𝐷𝑖𝑡 = 𝟙{𝑡≥𝐸𝑖} be an indicator for being treated, and define 𝐾𝑖𝑡 = 𝑡 − 𝐸𝑖 to be time relative to treatment. Let Θ be a set of time-invariant household characteristics, and let 𝑌𝑖𝑡 denote an outcome at time 𝑡 for household 𝑖 with time-invariant characteristics Θ𝑖 ⊂ Θ. The first step consists of a regression of the outcome 𝑌𝑖𝑡 on group-specific time effects 𝛽𝜃𝑡 using pre-treatment data: 𝑌𝑖𝑡 = 𝛼𝑖 + ∑ 𝛽𝜃𝑡 + 𝜈𝑖𝑡 , {𝑖, 𝑡 ∶ 𝐾𝑖𝑡 < −𝑘} (1) 𝜃∈Θ𝑖 where 𝛼𝑖 are household fixed effects and 𝛽𝜃𝑡 are characteristic-specific time trends. Note that we also exclude data within 𝑘 periods from the treatment date to avoid estimating possible changes in outcomes resulting from the upcoming treatment. In the second step, we model 𝑘 𝑌𝑖𝑡 = 𝛼 ̂𝑖 + ∑ 𝛽̂ 𝜃𝑡 + ∑ 𝛾𝑘 𝟙{𝐾𝑖𝑡 =𝑘} + 𝜀𝑖𝑡 , 𝜃∈Θ𝑖 (2) 𝑘=−𝑘̃ where 𝛼 ̂𝑖 and 𝛽̂ 𝜃𝑡 are the estimated parameters from Equation (1), 𝛾𝑘 is the effect of treatment 𝑘 periods after being treated, 𝑘̃ is the number of periods of pre-rebate treatment effects to estimate, and 𝑘 is the number of periods of post-treatment effects. We define the cumulative spending impact 𝑡−1 over a 𝑡-week period as Γ𝑡 ≔ ∑𝑘=0 𝛾𝑘 . Note that the set of post-treatment effects that can be causally identified (i.e., for which 𝛽̂ 𝜃𝑡 exists to construct a counterfactual) corresponds to periods {0, … , max𝑖 𝐸𝑖 − min𝑖 𝐸𝑖 − 𝑘 − 1}. We use a block-bootstrap procedure to compute standard errors adjusted for clustering at the household level. We proceed to adapt this framework to test whether spending responses vary based on when households receive payments relative to when they are informed. This corresponds to testing implication (iii) from the framework in Section 2. Since households in our data receive payments according to a pre-announced disbursement schedule, variation in anticipation duration reduces to variation in treatment time. We therefore incorporate heterogeneous treatment effects as follows by modifying the second step in our estimation: 𝑌𝑖𝑡 = 𝛼𝑖 + ∑ 𝛽𝜃𝑡 + 𝜈𝑖𝑡 , {𝑖, 𝑡 ∶ 𝐾𝑖𝑡 < −𝑘} (3) 𝜃∈Θ𝑖 𝑘 𝐸𝑖 𝑌𝑖𝑡 = 𝛼 ̂𝑖 + ∑ 𝛽̂ 𝜃𝑡 + ∑ 𝛾𝑘 𝟙{𝐾𝑖𝑡 =𝑘} + 𝜀𝑖𝑡 . 𝜃∈Θ𝑖 (4) 𝑘=0 The parameter 𝛾𝑘𝜏 represents the causal impact of receiving a rebate 𝑘 periods ago among households 𝑡−1 treated in period 𝜏. Analogous to before, we define Γ𝜏𝑡 ≔ ∑𝑘=0 𝛾𝑘𝜏 . To understand whether households receiving rebate payments sooner after the announcement exhibit higher spending responses (Γ𝜏𝑘 > Γ𝜏𝑘 for 𝜏 < 𝜏 ′ ), we test the null hypothesis of implication (iii). ′ 12 3.3.2 Assumptions Operationalizing the two-step econometric procedure from Section 3.3.1 requires making assumptions such as how spending would have evolved over time for treated households in the absence of the stimulus payment. For our main results, the treatment group consists of households that report receiving a stimulus payment by direct deposit within two days of the scheduled payment date, and the comparison group consists of all households that report receiving a stimulus payment within the disbursement period associated with their reported payment method (direct deposit or paper check) as in Broda and Parker (2014) and Parker (2017). We make the following assumptions in estimating Equation (1). First, to determine the counterfactual time trend for spending, the set of characteristics Θ consists of income groups (less than $15,000; $15,000–$30,000; $30,000–$50,000; $50,000–$70,000; $70,000–$100,000; over $100,000) and deciles of average expenditure by household size in the first quarter of 2008. Second, receiving a rebate check does not affect household spending two weeks in advance (𝑘 = 1). Section 3.4.3 shows that our results are not sensitive to any of the above assumptions. 3.4 Impact of stimulus payments on spending 3.4.1 Average spending impacts Before presenting our main results on the timing of stimulus payments, we discuss the average impact of receiving a stimulus payment on spending as a benchmark. This corresponds to estimating the Γ𝑡 parameters derived from Equation (2). To put the cumulative spending impacts into perspective, note that the Nielsen data account for approximately 30 percent of household expenditure (Coibion, Gorodnichenko and Koustas, 2021), and the average ESP for direct deposit households is approximately $1,000. We find broadly similar magnitudes to those in Broda and Parker (2014) when estimating Equation (2) for three subsamples of EFT households: our main estimation sample consisting of households receiving EFTs near the scheduled payment date, the subset of households receiving EFTs exactly on the scheduled payment date, and all other households that report receiving EFTs. Across these subsamples, our point estimates for Γ1 range from $6.67 to $11.24, and our point estimates for Γ4 range from $24.98 to $44.04, as shown in Figure 1 and appendix table 6; we also find insignificant spending responses after the month of payment receipt, with point estimates for Γ8 − Γ4 ranging from −$12.06 to $11.59.15 Consistent with their results, we find no spending response in weeks prior to receiving payment. 15 In estimating the impact of ESPs on spending in the week of receiving payment (Γ1 ), Broda and Parker (2014) report point estimates ranging from $12.8 to $13.8. They obtain point estimates of the four-week or one-month cumulative increase in spending (Γ4 ) ranging from $27.9 to $47.6. See Tables 3 and 4 in Broda and Parker (2014) and the discussion therein regarding the differences in magnitudes between their weekly and monthly analyses. They also report an insignificant average increase in spending of $9.3 one month later (Γ8 − Γ4 ) in their preferred specification. 13 3.4.2 Impact of timing of stimulus payments We proceed to test whether households exhibit greater spending responses to payments that arrive earlier. Thus we estimate Equation (4) and test whether the cumulative 4-week spending impacts Γ𝑤 4 vary across groups. Households received EFTs during the 18th, 19th, and 20th weeks of the year, which we denote as periods 𝑤 = 1, 𝑤 = 2, and 𝑤 = 3, respectively (Appendix Table 3). These dates correspond to 6, 7, and 8 weeks after the original IRS announcement, but using the IRS announcement as a point of reference likely understates the extent to which the payments come as a surprise to the first group, especially in light of President Bush’s April 25 announcement that the payments would begin sooner than originally stated. The data show a clear pattern of lower spending impacts for households that wait longer to receive their payments. Figure 2 summarizes our main results for various samples of households.16 The left panel displays estimates of Γ𝑤 4 for households receiving payments in different weeks, as well as 𝑝-values from testing the null hypotheses that Γ14 = Γ24 = Γ34 , while the right panel displays the confidence interval for the difference in spending between the first and last groups. We begin by discussing the full sample of households receiving EFTs near the scheduled payment date. Among households randomly assigned to receive payments in the first week, we estimate a $65.25 increase in spending during the four weeks after receiving the ESP, about twice as large as the increase in spending for the average household. The monthly spending impact for a household receiving payment in the first week is similar in magnitude to combining the impact on a household receiving payment one week later ($45.24) with the impact on a household receiving payment two weeks later ($18.73). This suggests an important role for the timing of payments in designing effective fiscal stimulus. The remaining rows of Figure 2 examine subsamples based on survey responses to questions pertaining to liquid assets and behaviors related to financial planning and spending as explored by Parker (2017). To investigate the importance of liquidity, we divide the sample into two groups based on whether the household reports having at least two months of income available in cash, bank accounts, or easily accessible funds in case of an unexpected decline in income or increase in expenses, and we reestimate Equation (1) and Equation (4). Parker (2017) reports point estimates of the marginal propensity to consume NCP goods in the four weeks following ESP receipt ranging from 2.04 to 2.08 percent for households with sufficient liquid wealth and 4.87 to 6.57 percent for households without sufficient liquid wealth. Consistent with these findings as well as other prior literature (Zeldes, 1989; Johnson, Parker and Souleles, 2006; Agarwal, Liu and Souleles, 2007), the results in the second and third rows of Figure 2 show higher spending responses among households without liquidity. In addition, we find significant heterogeneity based on the timing of payment for both constrained and unconstrained households. Among households receiving payments in the third week, we find a spending response of close to zero for those with sufficient liquidity. Randomly assigning more liquid households to receive payments at the beginning of the disbursement period leads to Appendix Figure 3 displays cumulative spending effects during the four weeks following ESP receipt. Also see Appendix Table 7 for the main results in the form of a table. 16 14 substantial increases in spending of about $50 over the four weeks after receiving their ESP. We find a similar effect size for the subset of liquidity-constrained households that have to wait until the third week of the disbursement period to receive their payments. Our estimates thus imply an effect of waiting times large enough to close the gap in spending responses between households with and without sufficient liquid wealth. We next examine heterogeneity in ESP spending responses by financial planning tendencies. We divide households into two groups based on whether they report reviewing their household’s financial information in the last few years and formulating a financial plan for their long-term future. Intuitively, we might expect households that formulate consumption plans to exhibit lower propensities to spend out of windfalls (Reis, 2006). Indeed Parker (2017) finds a negative relationship between financial planning and ESP spending responses, and we find a similar relationship on average. In a possible exception to this general pattern, households that make financial plans and receive ESPs in the first week exhibit the largest spending responses ($74.58 for planners compared to $58.06 for non-planners). The finding that the largest spending responses come from households that engage in financial planning highlights the importance of timing and suggests that models in which planning generically correlates with higher savings do not provide a complete explanation for the evidence. The last pair of rows in Figure 2 separately consider households that characterize themselves as spending types and saving types, a measure of impatience.17 We find, consistent with the results in Parker (2017), that more patient households spend less in response to the ESPs. Moreover, both self-reported spending types and saving types exhibit stronger responses to payments that arrive earlier. The consistency across these groups corroborates the notion that more time to anticipate future consumption impacts intertemporal decision-making through channels distinct from impatience. In addition to analyzing spending responses across households with different self-reported financial circumstances, we estimate heterogeneity in spending impacts by objective household characteristics. The relationship between anticipation duration and spending responses persists for households receiving different rebate amounts (see the MPC estimates in Appendix Figure 4 and Appendix Table 8, and see Appendix B.2 for details on estimation). The same pattern also emerges for high- and low-expenditure households as well as high- and low-income households (Appendix Figure 5 and Appendix Table 9). 3.4.3 Robustness This section explores the sensitivity of our results to the assumptions for determining the counterfactual spending trend in Equation (1), the comparison group of not-yet-treated households, and alternative sample restrictions. The survey question asks, “In general, are you or other household members the sort of people who would rather spend your money and enjoy it today or save more for the future?” As Parker (2017) notes, the phrasing attempts to elicit a stable household characteristic rather than their response to the stimulus payments. 17 15 We begin by considering alternative sets of characteristics in the first step of the estimation (Panel A of Figure 3 and appendix table 10). In our baseline specification, these characteristics include deciles of pre-rebate average expenditure and six income categories. Removing the income categories from the set Θ does not change the magnitudes of the estimated ESP spending impacts. Instead removing the expenditure deciles leads to slightly smaller estimates, though the differences across households receiving ESPs in different weeks remains equally substantial. The same holds if we remove both sets of characteristics and include only household fixed effects and period fixed effects. Allowing for differential spending trends based on the rebate amount leads to similar magnitudes as our main specification, as does replacing contemporaneous income with lagged values of income (for which the data contain much fewer missing values). Omitting household fixed effects leads to somewhat larger estimates. We next consider alternative sets of comparison households (Panel B of Figure 3 and appendix table 10). The baseline specification uses all households that receive ESPs within the disbursement period associated with their reported payment method to estimate counterfactual spending, using only data from at least two weeks before their reported payment weeks. Excluding one, two, or three additional weeks of data preceding ESP receipt slightly increases our estimates of the spending impacts. We also examine the sensitivity of our estimates to alternative specifications of the set of comparison households. Restricting the set of households to only those receiving paper checks, or further restricting to those that receive paper checks near the scheduled payment dates, leads to similar estimates of the ESP spending impacts. We obtain slightly larger point estimates if we use households receiving paper checks in July to ensure that the composition of households used to estimate each of the week fixed effects in Equation (1) remains stable. In our main specification as well as each of these alternative specifications, we find no significant spending responses in the weeks prior to receiving the ESP, providing evidence to support the validity of the estimated counterfactual spending trend (Appendix Table 11). Lastly, we examine how our estimates change under different sample restrictions (Panel C of Figure 3 and appendix table 10). Excluding households that report no spending for a consecutive four-week period does not change the magnitudes of our estimates. Restricting the sample of direct deposit households to those that report receiving their ESP on the exact day specified by the disbursement schedule also leads to similar point estimates. 3.5 Alternative explanations To interpret the results, Section 6 posits a mental-accounting framework that captures the intuition that households spend more in response to more surprising windfalls. The fact that liquidity constrained and unconstrained households exhibit similar patterns suggests an important role for this channel. In the rest of this section, we assess the plausibility of various alternative explanations for the results. The alternatives naturally fall into two groups: threats to establishing that a longer anticipation duration leads to lower ESP spending, and other reasons why households that face longer 16 waiting times would spend less. In addressing some of these alternatives, we present additional evidence that spending in a given calendar week among households in earlier payment groups significantly exceeds that of households in later payment groups who have received their payment more recently (Figure 4). 3.5.1 Anticipatory spending Smaller spending responses among households that wait longer before receiving payments may arise if more time allows households to spend more of their ESPs in advance. However, our data show no significant differences in spending prior to ESP receipt, with the total spending response in the month before receiving an ESP ranging from -$8.10 to $2.43 across the various specifications in Appendix Table 11.18 Explaining the difference in spending we observe between the first and last payment groups would require an average excess spending prior to ESP receipt of $3.32 per day ($46.52 over 14 days) or about $100 in monthly NCP spending. This is over five times as large as the anticipatory spending response implied by the Kaplan and Violante (2014) model, which implies a 6 percent marginal propensity to consume one quarter in advance of receiving a $500 tax rebate (see their Table IV). 3.5.2 Borrowing, debt, and non-Nielsen spending Since our consumption data only consist of spending on household items (Broda and Weinstein, 2010), changes in other forms of spending could potentially occur. Although our data show no evidence of additional spending in advance, households might either increase debt payments or increase non-NCP consumption (e.g., by borrowing, assuming that households have access to credit or are more likely to have access to credit if they have more time). The former possibility appears inconsistent with previous work on the 2001 and 2008 tax rebates (Agarwal, Liu and Souleles, 2007; Bertrand and Morse, 2009) documenting increases in debt payments upon receiving ESPs as opposed to in advance, while evidence on responses to state tax rebates from the Consumer Expenditure Survey (Heim, 2007) rejects the latter. Alternatively, we might also observe a relationship between anticipation duration and spending responses if longer waiting times simply lead to a compositional shift toward non-NCP expenditures. The question on self-reported ESP spending from the Broda and Parker (2014) survey provides evidence against this concern. The survey asks households to think about the “extra amount” they are spending because of the tax rebate and report how much of the additional spending falls in the following categories: household products, entertainment, durable goods, clothing, and other. Interpreting these data may present some difficulties because they reflect a combination of spending responses and households’ awareness of their spending responses. With this caveat in mind, we find that households in later payment groups do not report higher ESP spending on average than Using daily-level data on 17.2 million households from a large U.S. financial institution, McDowall (2019) also finds highly precise and insignificant anticipatory spending responses. 18 17 households in earlier payment groups.19 3.5.3 Time effects Evaluating the role of anticipation duration requires exogenous variation in when households learn about a windfall payment relative to when they receive it. In the context of the 2008 stimulus payments, since households receive information about payments at the same time, the duration of anticipation does not vary independently of calendar time. This could pose a concern if variation in the MPC arises either due to generic week-of-month effects or due to factors specific to the EFT disbursement period. If the marginal propensity to consume varies over the course of a month with fluctuations in cash on hand, we might expect to find larger spending responses in weeks when households must make rent payments or pay other bills, which tend to occur at the beginning of the month. On the other hand, we might expect to find smaller spending responses in weeks when households receive paychecks, which tends to push in the opposite direction. For a household making rent payments at the beginning of the month and receiving weekly paychecks, this would plausibly lead to larger spending responses to payments received in the first week of May and similar (smaller) responses to payments received in later weeks.20 We do not find any evidence of larger consumption responses to payments received at the beginning of the month for households receiving ESPs in June and July.21 The finding that households with different levels of income and liquidity exhibit similar patterns further limits the plausibility of explanations relying on week-of-month effects such as interactions with the paycheck cycle. Next we address the possibility of variation in MPCs arising due to calendar-time effects specific to the EFT disbursement period. In particular, new information over time about the severity of the financial crisis could lead to smaller absolute spending responses for households in later payment groups. We would expect this channel to be particularly relevant for states that experience higher levels of job loss during the recession. However, when analyzing differences in spending responses across states, we find that those in the top and bottom quartiles of the distribution exhibit similarly strong MPC reductions in response to longer waiting times (Appendix Figure 6). For a more direct test of the relevance of such calendar-time effects, we hold fixed calendar time and analyze differences in spending behavior across groups (to compare households when they would have access to the same information). Comparing the spending response of households in different payment groups within the same calendar week, those receiving EFT payments in later weeks spend significantly less 19 This holds for all five spending categories. Compared to households receiving ESPs in the first week of May, those receiving ESPs in the second week report spending $5 to $45 less and those receiving ESPs in the third week report spending $35 to $64 less. 20 Similarly, for households receiving biweekly paychecks, we would expect a non-monotonic pattern, with the largest response to receiving payments in the second week, and the smallest response to receiving payments in the third week. For households receiving monthly paychecks, we would expect to find larger responses to ESPs received in later weeks of the month. 21 As a caveat, note that this test does not use the ideal source of random variation in payment dates; see Appendix Table 5 and the discussion in Section 3.2. 18 on average per week in the four weeks after receiving payment compared to those in earlier payment groups (Figure 4). This occurs despite the fact that households in earlier payment groups would have less of their ESPs remaining to spend. 3.5.4 Other mechanisms for anticipation duration to affect spending We also consider individual- and group-level channels through which greater anticipation could potentially affect spending. Longer waiting times may make it possible for consumers to find ways to save or to find other ways to spend the money. Intrahousehold or social interactions could also potentially explain why anticipation duration matters. We elaborate on why channels based on external commitments, myopia, intertemporal consumption complementarities, rational inattention, and rational illiquidity do not suffice to explain the key patterns in our data in Appendix E.2. The evidence that liquidity unconstrained households exhibit the same effect (Figure 2) suggests that explanations based on waiting times enabling consumers to find ways to save or other external commitments cannot fully explain the patterns in the data. If the effect arises because the passage of time allows households to accumulate or remember expenses that would dampen their spending response (e.g., having more time for long-term needs to arise, having more time to remember high-value investments), then we would expect to find that households in earlier payment groups spend no more than households in later payment groups when holding the calendar week fixed, contrary to the evidence in Figure 4. The results replicate for single individuals, couples, households with and without children (Appendix Figure 7), suggesting that the effects do not reflect specific forms of intrahousehold decision-making. Finally, if the patterns arise from households observing and learning from others’ behavior or receiving external advice as time passes, we again would not expect to see the findings in Figure 4. 4 Cash transfers in Kenya This section analyzes our second empirical setting: an impact evaluation of unconditional cash transfers from the non-profit organization GiveDirectly, which delivers tens of millions of dollars in donations each year via the mobile-phone-based payment service M-Pesa to households in extreme poverty. 4.1 Setting and data Haushofer and Shapiro (2016) conduct an RCT to evaluate the impacts of unconditional cash transfers by GiveDirectly in rural Kenya from June 2011 to January 2013 on a wide range of outcomes including assets and consumption. The participants consist of 1,008 households from 120 villages in the Rarieda province of Western Kenya who meet the simple means-test criterion of living in a home with a thatched roof. The villages chosen for the study were those that had the highest proportion of thatched roofs in Rarieda. The average village in the sample consists of 100 households. 19 The researchers randomized 503 households into treatment arms that vary by whether households receive KES 24,000 (USD 384 PPP) or KES 94,000 (USD 1,505 PPP).22 Among the 366 households receiving the smaller transfer amount, 193 households received one-time lump-sum transfers.23 The magnitude of these one-time payments equates to about six months of revenue for the average household. Households learned of the transfers during a visit from a GiveDirectly representative. During these visits, the representative announced the amount and timing of the payments. Households receiving one-time lump-sum transfers would receive their payment on the first day of a randomly selected month among the nine months following the date of the visit.24 The outcome measures come from an endline survey which takes place about 14 months after the baseline survey. Eliminating 7 households for which transfer dates do not appear in the data, 8 attriting households for which the data do not contain endline survey outcomes, and 6 households that receive transfers after the endline survey (primarily due to registration issues with M-Pesa), our remaining sample consists of 172 households.25 We use random variation in payment dates among households in the lump-sum treatment to estimate the impact of longer waiting times, which we define as more than 𝑘 ∈ {2, … , 8} weeks from the announcement visit. Since previous research using the GiveDirectly data does not utilize this source of variation in anticipation duration, we conduct balance tests before proceeding. Consistent with random assignment, household characteristics and baseline measures do not significantly differ across households experiencing different waiting times (Appendix Table 12 and appendix figure 9). While the Haushofer and Shapiro (2016) experimental design involves randomizing the timing of the lump-sum transfers to facilitate comparability with their monthly-transfer treatment, our paper uses a distinct, previously unexploited source of variation—experimentally induced random variation in the extent to which households anticipated their transfer payments—to examine how anticipation affects decision-making. 4.2 Estimation and results To estimate the impact of longer waiting times, we follow the econometric strategy in Haushofer and Shapiro (2016) by conditioning on baseline levels of the outcome variables to improve statistical 𝑘 indicate a waiting time of 𝑘 ∈ {2, … , 8} weeks or less since the announcement, power. Letting 𝑇𝑣ℎ we estimate 𝐸 = 𝛼 + 𝛽 𝑇 𝑘 + 𝛾𝑦 𝐵 + 𝜀𝐵 , 𝑦𝑣ℎ 𝑣 𝑘 𝑣ℎ 𝑣ℎ 𝑣ℎ (5) 22 As in Haushofer and Shapiro (2016), we report all USD values at purchasing power parity using the World Bank PPP conversion factor of 62.44 KES/USD for private consumption in 2012. The transfer amounts roughly correspond to USD 300 nominal and USD 1,000 nominal. 23 The remaining 173 households received monthly transfers over a nine month period. The 137 treated households receiving the larger transfer amount received the bulk of their payments at a monthly frequency as well, as Appendix C.1 explains. 24 Households also received an initial transfer of KES 1,200 immediately following the announcement visit. 25 The attrition and non-compliance rates in our sample are similar to but slightly lower than in the complete sample of 1,008 households. See Appendix C.1 for additional details on the samples. 20 𝑡 represents the baseline (𝑡 = 𝐵) or endline (𝑡 = 𝐸) outcome of interest for household ℎ where 𝑦𝑣ℎ 𝑘 indicates treatment with a shorter waiting in village 𝑣, 𝛼𝑣 captures village-level fixed effects, 𝑇𝑣ℎ 26 The parameter 𝛽 represents the causal impact of time, and 𝜀𝐵 𝑘 𝑣ℎ is an idiosyncratic error term. a waiting time of 𝑘 weeks or less relative to a longer waiting time. We test the null hypothesis of Implication 3 from Section 2, which corresponds to 𝛽𝑘 = 0.27 We consider four broad outcome measures: savings, assets, durables, and investments. The measure of savings consists of the total value of savings in all savings accounts, including M-Pesa. Assets consist of various types of livestock (cattle; small livestock such as pigs, sheep, and goats; birds such as chicken, turkeys, doves, and quails) and durables. Durables include furniture, agricultural tools, appliances, and other movable assets such as bicycles and cell phones. Investments consist of durable investment (durable assets and non-agricultural business investment in durables) and non-durable investment (agricultural inputs, enterprise expenses, educational expenses, and savings). We present all values in 2012 USD PPP. These measures from Haushofer and Shapiro (2016) capture outcomes at the time of the endline survey, unlike the results in Section 3.4 which constitute an impulse response of spending to windfalls. Figure 5 displays the main results, which support the hypothesis that shorter waiting times, of a similar duration as in the setting from Section 3, lead to significant reductions in future-oriented decision-making. We present results under a variety of specifications, varying the definitions of the treatment group (shorter waiting times) and comparison group (longer waiting times). Each dot in the figure corresponds to an estimate of the treatment effect from Equation (5) and the associated 95 percent confidence interval for a given definition of shorter and longer waiting times. We vary the definition of a shorter waiting time between 2 weeks and 8 weeks, and we vary the regression sample to include waiting times between 90 days and 270 days as the comparison group. For example, the first specification compares households receiving transfers within 14 days of the announcement date with households receiving transfers up to 90 days after the announcement date. We find substantial decreases in the probability of having nonzero savings among households randomly assigned to receive cash transfers sooner after the announcement visit. The decrease in savings does not arise due to substitution into other stores of value such as durables or other assets and investments. Households facing the shortest waiting times—those receiving transfers in the first month after the announcement—exhibit the strongest reductions in endline savings, assets, durables, and investments. Varying the range of waiting times in the comparison group does not affect our results, suggesting that the estimates reflect the impact of differences in waiting times rather than differences in endline survey timing. Figure 6 corroborates this by plotting outcomes across the distribution of waiting times. If shorter waiting times lead to lower savings solely because households can experience a For the small set of outcomes with a few missing baseline measures, we encode missing values and control for an 𝐵 𝐸 𝐵 𝐵 indicator 𝑀𝑣ℎ for missing values: 𝑦𝑣ℎ = 𝛼𝑣 + 𝛽𝑇𝑣ℎ + 𝛾𝑦𝑣ℎ + 𝛿𝑀𝑣ℎ + 𝜀𝐵 𝑣ℎ . 27 Liquidity constraints play an important role in this setting (Haushofer and Shapiro, 2016). As we outline in Section 2, incorporating liquidity constraints into the benchmark models leads to violations of Implications 1 and 2 but not Implication 3. In addition, these data do not contain high-frequency measures of consumption as Section 3 does. Our analysis in this section thus focuses on Implication 3. 26 21 longer period of elevated consumption before the endline survey takes place, we would expect to see a linear relationship between waiting times and the various outcomes. The binned scatterplots instead confirm that households facing the shortest waiting times exhibit especially strong reductions in endline savings, assets, durables, and investments, consistent with a substantive shift in decisionmaking.28 We obtain similar results under various alternative estimation approaches. Equation (5) uses an analysis of covariance (ANCOVA) approach (Frison and Pocock, 1992; McKenzie, 2012). As an alternative, we analyze differences-in-differences, and we find similar impacts of short waiting times when defining the outcome variable as the difference between the endline and baseline measure (Appendix Figure 11). We also obtain similar estimates when altering the ANCOVA approach by adding quadratic controls for baseline outcomes (Appendix Figure 12) or removing village fixed effects (Appendix Figure 13). We also document similar patterns for other outcomes variables: value of savings, durable investment, non-durable investment, and total assets including non-thatched roofs (Appendix Figure 14). 4.3 Alternative explanations This section considers alternative individual- and group-level factors that may result in anticipation duration influencing savings and investment decisions.29 First, consumers may find ways to save or to find other ways to spend the money with longer waiting times. Second, intrahousehold or social interactions may result in a role for waiting times. To address the possibility that finding ways to save or spend as time passes may explain our results, we estimate the impact of short waiting time separately for households that report having no savings at baseline and those that report having no loans at baseline.30 We investigate the importance of intrahousehold interactions by examining heterogeneity by the gender of the randomly assigned recipient of the transfer, household size, children, and marital status. To evaluate whether receiving external advice or demands from others or observing and learning from others’ behavior as time passes might play a role, we re-estimate the model on the following subsamples: households that are net senders of remittances, villages in which an above-median fraction of treated households receive lump-sum transfers, villages in the bottom half of the distribution of the waiting time for the first lump-sum transfer, villages in the bottom half of the distribution of the waiting time for the first transfer, and households that receive their lump-sum transfer before the median household in their village. 28 All specifications contain controls for baseline outcomes and village fixed effects. Plotting the difference between endline and baseline outcomes gives the same pattern (Appendix Figure 8). Plotting only baseline outcomes provides evidence of balance (Appendix Figure 9). Appendix Figure 10 presents a formal test which rejects the null hypothesis of a linear relationship between waiting times and outcomes. 29 Section 3.5.4 discusses these channels in the context of our results on the 2008 stimulus payments in the US. The other possible explanations in Section 3.5 pertain to specific features of the tax-rebate setting. 30 Moreover, if the effects were driven by having more time for long-term needs to arise, then we would expect the difference between 5 and 6 months of waiting to be the same as the difference between 1 and 2 months of waiting, but Figure 6 shows that the latter is much larger. 22 Estimates of the impact of waiting less than four weeks on savings, assets, durables, and investment for the subsamples described above appear in Figure 7. In each case, we obtain estimates of roughly the same magnitude as the estimates from the full sample, with none of the subsamples showing systematic differences relative to the full sample. 5 Cash transfers in Malawi This section analyzes our final empirical setting: a field experiment in Malawi among several (orthogonal) interventions in partnership with the commercial bank NBS to encourage savings. 5.1 Setting and data Brune et al. (2017) conduct an experiment to examine how formal financial products influence consumption decisions by making windfall payments to a sample of 474 randomly selected households living in villages within six kilometers of the NBS bank branch in Mulanje, Malawi. The researchers randomly vary whether households receive transfer payments of MK 25,000 (USD 176.50 PPP) via cash or direct deposit in March–April 2014.31 The magnitude of the transfers equates to about four times the baseline average formal savings among households in the sample. The research team informs households during baseline surveying of their eligibility for a cash prize of up to MK 25,000 if they visit the branch exactly two days later, so households have some awareness of the scope of the transfers prior to the visit. During the in-person visit to the bank branch, households receive information about whether and when they will receive transfers. Participants either receive payments immediately or with a delay, randomized independently of the main treatment arm (i.e., whether the household receives the transfer via cash or direct deposit). The stated goal of the payment delay was to “test the presence of time inconsistency” to shed light on the mechanisms through which formal bank accounts affect spending, though we discuss in Appendix E.3 how payment delays do not necessarily provide a test of time-inconsistent preferences or quasi-hyperbolic discounting. In the experiment, 160 households receive payments after an eight-day delay, 158 households receive payments after a one-day delay, and the remaining 156 households receive payments immediately. This setting thus allows us to examine the effect of variation in anticipation duration both on a comparable scale to the variation in anticipation for which the settings in Sections 3 and 4 show effects, as well as on a significantly shorter time horizon that the previous settings did not allow us to examine.32 Consistent with random assignment, baseline characteristics do not significantly differ among households receiving payments with different delays (Appendix Table 13); 31 We report USD values at purchasing power parity using the conversion factor 141.64 MK/USD as in Brune et al. (2017). The transfer amounts correspond to about USD 60 nominal. 32 While we report estimates for each treatment arm, we note that Brune et al. (2017) caution that specifications that separately estimate the impacts of different payment delays tend not to have enough power to detect small effect sizes. 23 Brune et al. (2017, Table 3) also show that baseline characteristics across the treatment arms appear balanced. We use the experimentally induced variation in payment delays to examine effects on expenditures and savings. All outcome measures derive from a survey containing questions based on Malawi’s Third Integrated Household Survey (IHS-3), which each household completes one week after their transfer payment date. The survey includes an expenditure module and a savings module. Focusing on broad categories of expenditures (food, non-food, planned, and unplanned), Brune et al. (2017) find no substantial differences across treatment arms, with the exception of the longest payment delay leading to a significant reduction in unplanned food expenditures (see their Table A3). Our analysis of the data instead focuses on various forms of savings. 5.2 Estimation and results To obtain the causal impact of anticipated payment delays, we estimate an analog of Equation (5) as in Brune et al. (2017): 8 𝐸 1 𝐵 𝑦𝑣𝑤ℎ = 𝛼𝑣 + 𝛽1 𝑇𝑣𝑤ℎ + 𝛽8 𝑇𝑣𝑤ℎ + 𝛾𝑦𝑣𝑤ℎ + 𝛿𝑤 + 𝜀𝐵 𝑣𝑤ℎ , (6) 𝑡 where 𝑦𝑣𝑤ℎ represents the baseline (𝑡 = 𝐵) or endline (𝑡 = 𝐸) outcome of interest for household ℎ in village 𝑣 surveyed in week 𝑤, 𝛼𝑣 and 𝛿𝑤 capture village and week-of-first-survey fixed effects, 𝑘 𝑇𝑣𝑤ℎ indicates treatment with a 𝑘-day payment delay, and 𝜀𝐵 𝑣𝑤ℎ is an idiosyncratic error term. The parameters 𝛽𝑘 represent the causal impact of a 𝑘-day delay relative to an immediate windfall. We test the null hypothesis of Implication 3 from Section 2, which corresponds to 𝛽𝑘 = 0.33 The outcomes consist of various forms of savings. The main results, appearing in Table 1, show that an anticipated eight-day payment delay significantly increases total savings, and this increase arises largely due to in-kind savings. In-kind savings consist of advance purchases of farm inputs, business inventory, and bags of maize (see the questionnaire in Appendix Figure 15). The analysis in Brune et al. (2017), by contrast, focuses on expenditure rather than savings and finds little influence of payment delays. As a possible explanation for the discrepancy between the large impact on savings that we observe and the previous results on spending, note that the expenditure survey asks how much households paid in total for various consumption goods over the past seven days (Appendix Figure 16); these consumption goods include maize, which households also purchase as a form of in-kind savings.34 We can rule out large effects on other forms of savings. This includes financial assets, which consist of both formal savings (accounts at NBS or other banks) and informal savings (village savings groups, ROSCAs, cash not for daily living expenses kept at home or in a secret hiding place). Overall the results support the hypothesis that waiting periods As in Section 4, we focus on Implication 3 since liquidity constraints predict violations of Implications 1 and 2 but not Implication 3, and the data do not contain high-frequency measures of consumption. 34 This contrasts with the original question from the Malawi IHS-3 questionnaire, which asks specifically about how much households consume (“food both eaten communally in the household and that eaten separately by individual household members”) over the past seven days (Appendix Figure 17). See Browning, Crossley and Winter (2014) for a discussion of the well-known challenges of measuring household consumption using survey data. 33 24 cause substantial shifts in household decision-making. The estimates for eight-day delays corroborate the findings from Sections 3 and 4 that short delays on the order of a week can lead to greater savings. The Malawi setting further allows us to examine the impact of much shorter delays. For all forms of savings, we find insignificant effects of one-day delays in Table 1. While we can rule out large effects of short delays on savings, the lack of precision presents difficulties in learning more about the shape of the relationship between savings and delay duration using these data. 5.3 Alternative explanations This section follows Section 4.3 by considering alternative mechanisms that could potentially explain the relationship between waiting times and savings. We find similar point estimates for the impact of a delayed windfall for households receiving direct deposit payments into an account with the NBS Bank rather than cash (Appendix Table 14); this suggests that the results are not driven by waiting times enabling households to find ways to save. Our results hold across married and unmarried households (Appendix Table 15) as well as large and small households (Appendix Table 16), suggesting that the mechanism does not rely on intrahousehold interactions. Finally, the relatively small share of treated households limits the scope for social interactions to provide a plausible explanation in this setting. 6 Mental accounting and timing of windfalls Section 2 enumerates a set of implications following from the standard benchmark model: Consumption changes immediately upon learning about a transitory income shock (Implication 1) and remains constant thereafter (Implication 2); and therefore consumption exhibits stationarity, i.e., the timing of the shock does not affect spending (Implication 3). Consistent with prior work (e.g., McDowall, 2019; Fuster, Kaplan and Zafar, 2021), our data show no evidence of anticipatory spending in response to a future income shock, including among households with sufficient liquidity. With no anticipatory spending, forward-looking theories of consumption predict that stationarity still holds, so a violation of stationarity points toward the relevance of backward-looking elements. The behavioral life-cycle model of Shefrin and Thaler (1988) provides a central explanation for excess smoothness and excess sensitivity of consumption by positing that consumers treat their current assets differently from windfall income, even if they do not face binding liquidity constraints. We extend this model to describe how consumers categorize windfalls based on the duration of anticipation, i.e., the time elapsed since learning about the windfall. We discuss how other classes of models, including models based on external commitments, myopia, intertemporal consumption complementarities, rational inattention, and rational illiquidity, do not explain the data (see Appendix E.2 for more details). We estimate the model using the weekly spending NCP data from Section 3. The estimated model fits the monthly and weekly spending moments in our data, including the fact that the 25 passage of time leads to smaller decreases in spending among groups receiving payments sooner after learning about them (Figure 4). We show how the model also matches out-of-sample moments and discuss implications for the design of fiscal stimulus policies, focusing on payment frequency, amounts, and targeting. 6.1 Evidence for mental accounting In our data, households—including those that do not face binding liquidity constraints—treat windfall income as separate from their current wealth, as in models based on mental accounting (Shefrin and Thaler, 1988). Mental accounting provides a broad description of how consumers mentally categorize windfalls, which can be shaped by phenomena such as self-control (Galperti, 2019), internal commitments (Bénabou and Tirole, 2004), goal setting (Koch and Nafziger, 2016), narrow bracketing (Lian, 2021), planning (Kőszegi and Rabin, 2009), and attention (Kőszegi and Matějka, 2020). Within the literature on consumption smoothing, and more broadly in macroeconomics, various authors invoke mental accounting to explain otherwise puzzling phenomena. This includes the relationship between liquid wealth and MPCs (Kueng, 2018; McDowall, 2019; Fuster, Kaplan and Zafar, 2021; Boutros, 2022), consumption smoothing in response to losses but not gains (Ganong et al., 2020; Baugh et al., 2021; Massenot, 2021), the relationship between wealth accumulation and capital gains (Fagereng et al., 2019), price stickiness (Angelis, 2021), and the co-holding of savings and debt (Gathergood and Olafsson, 2022).35 In our setting, mental accounting provides an explanation for the four key patterns in the data. First, the lack of anticipatory spending in response to information about a future income shock (excess smoothness) among households with liquid wealth suggests that households treat future income differently from current wealth. Second, the high MPC in response to the arrival of predictable windfall gains (excess sensitivity) suggests that households treat current assets differently from current income. These first two facts align closely with the idea from Shefrin and Thaler (1988) that households separate wealth into three mental accounts, each with a different MPC: current income (highest MPC), current assets, and future income (lowest MPC). Third, the differential consumption response to additional income based on the duration of anticipation (non-stationarity) suggests that households classify additional income based on the time when they learned about the change. Fourth, the larger decrease over time in the spending response among households that wait longer to receive their payments than among households that have already received their payments (Figure 4) suggests that the way households classify additional income depends on the interaction between payment timing and the (remaining) windfall amount. The latter two facts require a dependence of MPCs on payment magnitude and timing. The intuition behind mental accounting suggests a role for both magnitude and timing. Shefrin and Thaler (1988), in their work on the behavioral life-cycle hypothesis, emphasize that households Massenot (2021); Lian (2022) also explain high MPCs for liquid consumers by invoking violations of fungibility as in models of mental accounting. 35 26 classify additional income based on magnitude: “People tend to consume from income and leave perceived ‘wealth’ alone. The larger is a windfall, the more wealth-like it becomes.” Arkes et al. (1994), in the psychology literature, emphasize the role of timing: “unanticipated money may be in no account. Planning for its expenditure takes time. Until some reasonable target is decided upon, the money remains uncommitted and therefore available for extravagant, frivolous, or speculative use. When funds are anticipated, the budgeting process occurs before receipt of the funds. When the funds eventually arrive, they are not available to be spent on some whim.” We introduce a simple model that incorporates both of these features and discusses how they interact. The idea to incorporate the time dimension in modeling mental accounting is new and therefore warrants further discussion. Non-stationarity in consumption responses to windfalls, combined with a lack of anticipatory spending, necessitates a theory of consumption that incorporates backwardlooking elements (see Section 2). We formalize several possible channels through which MPCs may exhibit such history dependence in conjunction with mental accounting in Appendix E.1. First, consumers may form reference-dependent consumption plans as in models of news utility (Kőszegi and Rabin, 2009). Second, temptation may exhibit a greater influence on decision making in the presence of sooner opportunities to consume (Noor, 2007; Fudenberg and Levine, 2012). Third, consumers may find deviating from long-held goals or internal commitments more costly (Gollwitzer, 1993, 2015). Fourth, decision makers may put more weight on consumption in response to more recent information that draws their attention (Bordalo, Gennaioli and Shleifer, 2020). Fifth, consumers may experience utility from anticipating future consumption, which results in more forward-looking behavior in response to longer waiting times (Thakral and Tô, 2020; Thakral, 2022). Sixth, the passage of time may also allow decision makers to learn about the optimal action (Ilut and Valchev, forthcoming). As our main conclusions do not rely on a specific interpretation of the relationship between MPCs and timing, we take a reduced-form approach (Mullainathan, Schwartzstein and Congdon, 2012) to model the dependence of the MPC on the time dimension.36 6.2 Descriptive model of mental accounting We model the decision making of a consumer who learns of a windfall and processes it through three mental accounts: a current income account, an intermediate account, and a future income account. For simplicity, assume that the consumer has a positive MPC only for current income and narrowly brackets the windfall separately from other sources of income (Read, Loewenstein and Rabin, 1999). Information about a windfall of magnitude 𝑚 arrives at time 𝑡 = 0. Before the windfall arrives, the consumer thinks of it as future income. Once the windfall arrives, it enters a separate intermediate or windfall account. In each period 𝑡, consumers transfer a fraction 𝜇(𝑚, 𝑡) of Some attempts to incorporate backward-looking elements fail to account for the main patterns in our data; this includes explanations based on external commitments, myopia, intertemporal consumption complementarities, rational inattention, and rational illiquidity, as Appendix E.2 elaborates. We also note that purely forward-looking theories of consumption, such as models of discounted utility (Laibson, 1997) and temptation disutility (Gul and Pesendorfer, 2004), do not explain the non-stationarity and lack of anticipatory spending in our data; this also applies to models of expectations-based reference dependence (Kőszegi and Rabin, 2009), unless we additionally impose a mental accounting assumption. See Appendix E.3 for further details. 36 27 the amount that remains in their windfall account to their current income or spending account.37 If 𝜇𝑚 < 0, then consumers treat smaller windfall amounts as current income to a greater extent than as wealth. If 𝜇𝑡 < 0, then consumers treat windfalls that they learned about more recently as current income to a greater extent than as wealth. The following expressions describe the model-implied spending out of a windfall of size 𝑚 = 𝑤𝑡 that the consumer anticipates for 𝑡 periods. Let 𝑦𝜏 = 𝜇(𝑤𝜏 , 𝜏 ) ⋅ 𝑤𝜏 (7) denote windfall spending in period 𝜏 ≥ 𝑡. The amount 𝑤𝑡+𝑘 = 𝑤𝑡+𝑘−1 − 𝑦𝑡+𝑘−1 (8) remains in the windfall account in period 𝑡 + 𝑘 for 𝑘 > 0. Our main specification assumes that households in the earliest payment group treat the payments as a surprise; in other words, Group 1 anticipates the windfall for 0 periods, Group 2 for 1 period, and Group 3 for 2 periods.38 6.3 Nonlinear least squares estimation To estimate the model, we propose a simple functional form: 𝜇(𝑚, 𝑡) = 𝛽 𝑚 𝛼𝑡 . (9) While we do not constrain the values of 𝛼 or 𝛽 in the estimation, note that if 𝛼, 𝛽 ∈ (0, 1), then the consumer treats smaller windfalls and more recent windfalls as more spendable (𝜇𝑚 < 0 and 𝜇𝑡 < 0). In addition, under this condition, actual windfall spending (𝑦) will not exceed the amount that remains in the windfall account. Equations (7) to (9) recursively define windfall spending in each period as a nonlinear function of parameters (𝛼 and 𝛽) and data (𝑚 and 𝑡).39 We assume that idiosyncratic shocks may result in deviations between observed and predicted spending, so in the data we would observe ̃ 𝑦𝑖𝑡 = 𝑦𝑖𝑡 + 𝜖𝑖𝑡 , i.i.d. 2 where 𝜖𝑖𝑡 ∼ 𝒩(0, 𝜎 ). We use nonlinear least squares to estimate the resulting specification. Since estimating the model requires high-frequency consumption data, we use the weekly spending NCP data from Section 3. Assuming that non-windfall NCP spending equals pre-rebate average spending, we obtain a measure of total windfall spending (the outcome variable ̃ 𝑦𝑖𝑡 ) by taking the difference between observed weekly NCP spending and pre-rebate average spending and then 37 This heuristic could arise from a model in which the consumer maximizes in each period a Cobb-Douglas utility function where the expenditure shares depend on the magnitude and timing of the windfall, but the microfoundation of such a model remains a topic for future research. A recent paper by Boutros (2022) makes a similar modeling assumption: “the mental account for the shock is the residual saving after consuming out of the shock in the previous period, not the exogenous shock as in the first period.” 38 This is consistent with the modeling choice by Kaplan and Violante (2014), which they refer to as the “intermediate informational assumption:” All households learn about the rebate payments upon disbursement of the first set of payments. 𝑚 𝑡 39 The resulting expression for 𝑦𝜏 has the form 𝛽𝑚 𝛼𝑡 𝑚𝟙{𝜏=𝑡} + (𝛽(1−𝛽 𝛼 )𝑚 𝛼𝑡+1 (1 − 𝛽𝑚 𝛼𝑡 )𝑚)𝟙{𝜏=𝑡+1} + ⋯. 28 applying a scaling factor to convert from NCP windfall spending to total windfall spending. Our main specification uses a scaling factor of 3.33 since the NCP data account for about 30 percent of household spending (Coibion, Gorodnichenko and Koustas, 2021). 6.4 Model fit 6.4.1 Parameter estimates We present estimates of the model in Table 2. In our preferred specification (Column 1, which uses a scaling factor of 3.33) we obtain 𝛽 = 0.9984 and 𝛼 = 0.5789. To interpret these magnitudes, note that increasing the size of a windfall by $100 reduces the marginal propensity to consume out of that windfall by 15 percent. We also calculate that the MPC decreases by the same amount from an additional one week of waiting as it would from increasing the size of the windfall by $340, a quantity we refer to as the waiting equivalent.40 The bottom panel of the table shows how closely the estimated model matches the monthly spending moments in the U.S. data (see Figure 2). 6.4.2 Interaction between magnitude and duration The estimated model also reproduces key features of the weekly spending data. For groups that face shorter waiting times, the estimated model predicts that spending remains somewhat elevated as time passes, as Appendix Table 18 documents. This pattern arises due to the interaction between magnitude and timing within the mental-accounting model: Since a shorter waiting time leads to a higher initial spending response, a smaller amount remains in the consumer’s windfall account, and the higher MPC out of a smaller magnitude partly mitigates the MPC reduction in the subsequent period. This provides an explanation for the finding that spending among households receiving stimulus payments in the earliest payment group exceeds that of households receiving payments in later groups even when conditioning on calendar week (Figure 4). 6.4.3 Sensitivity analysis and heterogeneity To assess the sensitivity of our results, we vary the scaling factor and the informational assumptions. Varying the scaling factor corresponds to making different assumptions about the fraction of spending that the NCP data account for. We consider a range between 1 and 10 to encompass our preferred specification and an alternative from Broda and Parker (2014); they propose to use the share of self-reported ESP spending on household goods (13.7 percent), which would imply a scaling factor of 7.3. Although larger scaling factors result in larger estimates of 𝛼, the value of the waiting equivalent remains relatively stable across specifications, as the various columns of Table 2 show. The preferred specification provides the closest fit for the monthly spending moments in the U.S. data, as the bottom panel shows. Varying the informational assumptions corresponds to shifting the number of periods that households anticipate receiving the windfall. In particular, we consider the possibility that households in the earliest payment group anticipate receiving the payment starting We calculate the waiting equivalent by setting 𝛼 = 𝛽𝑤 and solving for 𝑤. 40 29 at the time of the original IRS announcement, which ignores President Bush’s announcement soon before the payment dates that the Treasury would start distributing payments sooner than expected (see Section 3.4.2 for a reminder of the timeline). We find that the waiting equivalents remain stable under the alternative specification, though the baseline informational assumption provides a better fit for the monthly spending moments (see Appendix Table 17). We also estimate the model separately for the subsamples in Figure 2 and document substantial heterogeneity in waiting equivalents. As Table 3 shows, for households that are liquidity constrained, those that do not make financial plans, and those that classify themselves as spenders, an additional week of waiting time reduces the MPC by as much as an additional $450 to $750 in the size of the windfall. By contrast, the waiting equivalents for unconstrained households, those that make financial plans, and those that classify themselves as savers range between $150 and $250.41 Predicted spending estimates, shown in the bottom panel, generally follow the data reported in Figure 2 (and Appendix Table 7). According to the estimates, households that do and households that do not make financial plans exhibit similar spending responses after two weeks of waiting, as do households that classify themselves as savers or spenders, consistent with the data. Perhaps not surprisingly, our model tends to underpredict the spending response of liquidity-constrained households. 6.4.4 Consumption responses across settings The parameter estimates enable us to calculate the predicted consumption response to income shocks anticipated over different horizons. To synthesize our results, we plot the model-implied MPC in response to windfalls of different magnitudes as a function of duration in Figure 8 and the total consumption response in Appendix Figure 18. These figures plot the response to a $1,000 payment (approximately the average size of the U.S. tax rebate from Section 3), a $404 payment (the size of the cash transfer in Kenya from Section 4), and a $176.50 payment (the size of the windfall in Malawi from Section 5) over a range of waiting times less than one month to encompass the common domain across all three settings. The data in each of these settings align with the predictions of the model. The four-week consumption responses estimated using the U.S. data for households receiving payments in the first, second, and third week of May appear alongside the model predictions in Appendix Figure 19. We also produce analogous figures depicting the total consumption response estimated using the Kenya data (Section 4) for households receiving payments less than 1 month after the announcement (Appendix Figure 20) and the one-week consumption responses estimated using the Malawi data (Section 5) for households receiving payments immediately or after waiting about one week, along with the predictions of the model.42 In all cases, the confidence intervals overlap with the predictions of the model. This suggests that the consistency in findings across the three settings extends beyond 41 These characteristics (liquidity constraints, financial planning, and spender/saver tendency) are not highly correlated; their pairwise correlations are less than one-third. 42 Since the Kenya data do not contain direct measures of the consumption response to receiving the payment, we use the difference between the windfall amount and the change in assets to proxy for consumption. 30 the qualitative similarities. We note two caveats in applying our estimates to other settings. First, the simple model we estimate does not incorporate liquidity constraints, which surely plays an important role and may lead to higher MPCs and decreased sensitivity to anticipation duration. Second, we caution against extrapolating the estimates beyond the range of waiting times present in the U.S. data due to the functional form assumption in Equation (9). 6.5 Policy implications We discuss the conclusions of our estimated model for three design features of fiscal stimulus policies— payment duration/frequency, payment amounts, and targeting—as well as broader implications for policy and welfare. We also discuss implications for the 2020–2021 stimulus payments in Appendix B.4. 6.5.1 One-time payment vs. flow of payments Our model provides a possible explanation for the greater effectiveness of one-time payments (e.g., stimulus check) over flows of payments (e.g., reductions in withholding). Sahm, Shapiro and Slemrod (2012) describe arguments from academics and policymakers suggesting that a series of small payments may induce greater spending.43 Their survey evidence on the 2008 stimulus payments and the 2009 reduction in withholding in the US shows the opposite result, contrary to the prediction of a mental-accounting framework based on the idea of smaller MPCs from larger payment amounts. Our work helps to resolve this tension by pointing out the crucial role of anticipation and timing, which suggests that a lower spending response to a series of smaller payments may result from having more time to anticipate receiving those payments. Quantitatively, the estimated model matches the difference in MPCs between the one-time payment and the reduction in withholding implied by the data from Sahm, Shapiro and Slemrod (2012). Their survey contains data on the fraction of households that use the additional income to mostly spend, mostly save, or mostly pay off debt, and we apply three methods from the literature, following recent work by Feldman and Heffetz (2021), to convert these data to MPC estimates. These methods imply an MPC ranging from 0.22 to 0.41 for the reduction in withholding and ranging from 0.29 to 0.44 for the one-time payment. Despite the wide range across methods, all three approaches imply a difference in MPCs of only 0.03 to 0.07. Consistent with these data, when we model the reduction in withholding as a series of small windfalls of varying levels of anticipation, our estimates imply an MPC of 0.27 for the reduction in withholding compared to an MPC of 0.32 for the one-time payment (Table 4). 6.5.2 Consumption-maximizing payment size With some caveats, the model can also provide guidance on the optimal size of stimulus payments. On net, lower MPCs resulting from larger windfalls may decrease the total spending response. Feldman (2010), for example, documents an increase in consumption in response to the 1992 decrease in US federal income tax withholding, which shifts lump-sum tax-refund income to additional monthly income. 43 31 The model implies that the payment amounts that maximize spending are $757, $696, and $664, respectively, for windfalls that arrive one, two, and three weeks after the announcement. For a windfall that arrives completely by surprise, the spending-maximizing amount implied by the model is $872. These calculations abstract from differences in household characteristics, income, and other financial circumstances which would likely alter these conclusions.44 In addition, whether the functional form we assume for 𝜇 constrains substantively important interactions between the time and magnitude of payment remains an open question that future work, given sufficiently detailed data, can investigate using our approach. Extensions of our methodology applied to larger datasets may provide further guidance on targeted payment amounts. 6.5.3 Targeting Our results echo previous work supporting the common practice of providing broad-based stimulus payments over more narrowly targeted payments to increase aggregate consumption (e.g., see McDowall 2019 and Andreolli and Surico 2021). The addition of the time dimension does not alter this conclusion since MPCs in our model decrease with windfall size for any given waiting time. 6.5.4 Value of faster disbursement The estimates imply a substantial value for investing in new technologies that speed up the disbursement of fiscal stimulus payments. Consider a $757 windfall that is anticipated for one week (i.e., the consumption-maximizing payment size). A completely unanticipated windfall of $346 would increase aggregate consumption by the same amount. The model thus implies a willingness to pay for infrastructure to support unanticipated payments on the order of about half of the value of the payments themselves. 6.5.5 Welfare At an aggregate level, understanding how household spending responds to transitory variation in income at different time horizons (i.e., intertemporal MPCs) provides a crucial input for evaluating the macroeconomic impact of tax and labor-market policies and for designing effective stabilization policies (Auclert, Rognlie and Straub, 2018). At an individual level, failure to perfectly smooth consumption in response to small, transitory income fluctuations entails small utility costs and second-order welfare losses, as a large literature in macroeconomics notes (Akerlof and Yellen, 1985; Cochrane, 1989; Browning and Crossley, 2001). 7 Conclusion We document a consistent set of new results across multiple settings using existing observational and experimental data. In the context of both developed and developing countries, additional The MPC may depend on the size of a windfall relative to income. See Kueng (2018) for evidence of higher MPCs among higher-income households in the context of the Alaska Permanent Fund Dividend payments. 44 32 time spent anticipating a windfall payment leads to lower consumption responses. This robust pattern holds across consumers differing by levels of income, liquidity, access to formal financial products, demographic characteristics, and the magnitude of windfall payments. A meta-analysis of the literature on marginal propensities to consume in response to receiving anticipated payments also provides support for these results (Appendix A.2). The empirical results suggest a novel role for the timing of information in the design of tax and transfer programs. When policymakers intend to stimulate spending, as in the case of tax rebates, our results highlight the importance of rapid disbursement of payments. To encourage longer-term investments, as policymakers may desire when delivering cash transfers to impoverished households, announcing payments in advance may lead to more future-oriented decision-making. Testing the underlying properties of how consumption responds to transitory variation in income and making progress toward obtaining credible iMPC estimates has significant macroeconomic policy implications. As highlighted in the macroeconomics literature, intertemporal MPCs constitute sufficient statistics for general equilibrium responses to fiscal shocks and policies (Auclert, Rognlie and Straub, 2018). Moreover, the properties of iMPCs determine whether lump-sum transfer payments serve as a perfect substitute for conventional monetary policy (i.e., interest rate changes), which has particularly important policy implications when the effective lower bound on nominal interest rates binds (Wolf, 2021). Our finding that a longer anticipation duration can dampen spending suggests that responses to predictable increases in income may look meaningfully different from commonly used model-based extrapolations from the response to unexpected income changes. More broadly, our work highlights the importance of developing richer models of intertemporal preferences and incorporating them into macroeconomic analyses. Understanding how spending responses vary with time to anticipate receiving a windfall can also inform the design of other public policies that involve payments anticipated over different time horizons. This includes policies such as universal basic income, automatic stabilizers, tax refunds, social security, and unemployment insurance, among many others that would have important welfare implications. Consequences for the structure of compensation within firms, such as bonuses and pay frequency, would also be valuable to explore in future research. Anticipation likely also has implications for a broader set of outcomes beyond consumption and savings. Our study provides a path for future work in characterizing the effects of time-delayed transfers on a broad range of outcomes such as human capital acquisition, health-related decision making, labor productivity, risk-taking, and business investment. Designing experiments to study these outcomes in addition to consumption would be especially useful. Finally, our work provides a step toward elucidating the dynamic elements underlying the broad set of phenomena that constitute mental accounting. Developing theoretical frameworks that capture these dynamics seems particularly promising. 33