metadata: authors: 0: author: Bergstrom,Katy Ann
1: author: Dodds,William
2: author: Robles Rios,Juan Carlos
count: Brazil
docna: 0: docna: Welfare Analysis of Changing Notches:
            Evidence from Bolsa Família
docty: Policy Research Working Paper
abstracts: cdata!: This paper develops a framework to bound
            the welfare impacts of reforms to notches using two
            sufficient statistics: (1) the number of households bunching
            at the old notch who move toward the new notch, and (2) the
            number of households who &#x201c;jump&#x201d; down
            to the new notch. The bounds hold in a wide class of models,
            highlighting a new way to use reduced-form bunching evidence
            for welfare analysis without strong assumptions on the
            economic environment. These two statistics are estimated
            using a difference-in-difference strategy for a  reform to
            the anti-poverty program Bolsa Fam&#x131;lia, finding
            that the reform&#x2019;s marginal value of public funds
            lies between 0.90 and 1.12.
display_title: Welfare Analysis of Changing
            Notches: Evidence from Bolsa Família
listing_relative_url: /research/2022/07/33862059/welfare-analysis-changing-notches-evidence-bolsa-família
topicv3: Social Assistance m1327201 1466,Cash Transfers m1327437 1608,Growth, Poverty and Inequality m1327633 1091,Targeting Methods in Social Assistance
            m1584020 4409
publishtoextweb_dt: 2022-07-05T00:00:00Z
dois: 10.1596/1813-9450-10117
origu: Off of Sr VP Dev Econ/Chief Econ (DECVP)
author_keys: 0: author_key: 1811674
1: author_key: NA
2: author_key: 1076546
model_extractions: Policy Research Working Paper 10117

# Welfare Analysis of Changing Notches Evidence from Bolsa Família

_Katy Bergstrom William Dodds Juan Rios_ Development Economics Development Research Group July 2022
Policy Research Working Paper 10117

# **Abstract**

This paper develops a framework to bound the welfare impacts of reforms to notches using two sufficient statistics: (1) the number of households bunching at the old notch who move toward the new notch, and (2) the number of households who “jump” down to the new notch. The bounds hold in a wide class of models, highlighting a new way to use reduced-form bunching evidence for welfare analysis without strong assumptions on the economic environment. These two statistics are estimated using a difference-in-difference strategy for a reform to the anti-poverty program Bolsa Famılia, finding that the reform’s marginal value of public funds lies between 0.90 and 1.12.

This paper is a product of the Development Research Group, Development Economics. It is part of a larger effort by the World Bank to provide open access to its research and make a contribution to development policy discussions around the world. Policy Research Working Papers are also posted on the Web at http://www.worldbank.org/prwp. The authors may be contacted at kbergstrom@worldbank.org.

_The Policy Research Working Paper Series disseminates the findings of work in progress to encourage the exchange of ideas about development issues. An objective of the series is to get the findings out quickly, even if the presentations are less than fully polished. The papers carry the names of the authors and should be cited accordingly. The findings, interpretations, and conclusions expressed in this paper are entirely those of the authors. They do not necessarily represent the views of the International Bank for Reconstruction and Development/World Bank and its affiliated organizations, or those of the Executive Directors of the World Bank or the governments they represent._ Produced by the Research Support Team
Welfare Analysis of Changing Notches: Evidence from Bolsa Fam ́ılia<sup>_∗_</sup> Katy Bergstrom<sup>_†_</sup> , William Dodds<sup>_‡_</sup> , and Juan Rios<sup>_§_</sup> _Keywords: bunching, jumping, notches, MVPF, bounds, sufficient statistics JEL: H31, H53, I38, O12_

> _∗_ Some of the ideas in this paper were part of a chapter of Juan’s dissertation at Stanford University, titled “Welfare Analysis of Transfer Programs with Jumps in Reported Income: Evidence from the Brazilian Bolsa Fam ́ılia”. We are grateful to members of Juan’s dissertation committee Douglas Bernheim, Raj Chetty, Luigi Pistaferri and Florian Scheuer for their advice and guidance. We also want to thank Pierre Bachas, Jose Maria Barrero, Alexander Gelber, David McKenzie, Berk Ozler,<sup> ̈</sup> Peter Phillips, and seminar participants at the NBER Public Economics Meeting, Stanford University, the World Bank, the University of Auckland, and Brookings for their comments and suggestions. This research was supported in part using high performance computing (HPC) resources and services provided by Technology Services at Tulane University, New Orleans, LA. The findings, interpretations, and conclusions expressed in this paper are entirely those of the authors. They do not necessarily represent the views of the International Bank for Reconstruction and Development/World Bank and its affiliated organizations, or those of the Executive Directors of the World Bank or the governments they represent.

> _†_ World Bank. Email: kbergstrom@worldbank.org.

> _‡_ Tulane University. Email: wdodds@tulane.edu.

> _§_ Uber. E-mail: juanriosriver@gmail.com
1 Introduction Throughout developed and developing countries, tax and transfer schedules often feature notches wherein incremental changes in behavior lead to discrete changes in benefits or tax liabilities (Slemrod (2010); Kleven (2016)). For example, Saving and Viard (2021) document numerous notches in the United States tax code including the well-known Medicaid eligibility notch (Yelowitz, 1995), Kleven and Waseem (2013) document notches of up to 4 percentage points in average personal income tax rates in Pakistan, and Bachas and Soto (2021) document 10 percentage point jumps in the average corporate tax rate in Costa Rica. Given this prevalence, it is important for economists and policymakers to understand the welfare impacts of policy reforms that change the structure of notches in tax and transfer systems.

Typically the behavioral and welfare impacts of notches are analyzed using the standard bunching approach whereby one non-parametrically estimates the mass of agents bunching around a notch and then translates this bunching mass into a structural parameter(s) (Kleven, 2016). One can then use these structural parameters to gauge the welfare impacts of previous policy changes or to predict the impacts of future policy reforms.<sup>1</sup> However, the chief limitation of this approach is that translating a bunching mass into a structural parameter typically relies heavily on the modeling assumptions of the agent problem. For example, assumptions on preferences, the types of behavioral responses available to agents, and the degree of optimization frictions can all greatly impact the mapping between a bunching mass and a structural parameter.<sup>2</sup> Consequently, Kleven (2016) states “although bunching provides compelling non-parametric evidence of a behavioral response, moving from observed bunching to a structural parameter that can be used to predict the effects of policy changes is difficult.” This paper develops a technique that uses changes in bunching to assess the welfare impacts of changes to notches in transfer schedules while imposing minimal structure on the agent problem. In particular, we show how to bound the welfare impact of such a reform using two sufficient statistics: (1) the number of agents bunching at the original threshold who move towards the new threshold as a result of the reform, and (2) the number of agents who “jump” down to bunch at the new threshold as a result of the reform. Importantly, our bounds require only minimal structure on the agent problem: agents can have arbitrary preference heterogeneity, agents can have any number of choice variables, and agents may face optimization frictions such as limited choice sets and/or adjustment costs. Thus, our approach overcomes a key limitation of the standard bunching approach by using reduced-form bunching evidence to inform welfare analysis without making strong assumptions about the agent’s optimization problem.

We then use our method to bound the welfare impacts of a reform that expanded a notch in one of the world’s largest cash transfer programs, Bolsa Fam ́ılia (BF). Our bounds suggest that the marginal value of public funds for this reform lies between 0.90 and 1.12, which implies that the reform was welfare improving if the government values giving R$0.90 to BF recipients (in a non-distortionary way) more than spending one dollar on their next best alternative and welfare decreasing if the government values giving R$1.12 to BF recipients (in a non-distortionary way) less than spending one dollar on their next best alternative. Because recipients of Bolsa Fam ́ılia are typically very poor (Bastagli (2008), Lindert et al. (2007)), we argue that it is 1. Note that while one could, in principle, evaluate the welfare impacts of particular notch reforms using the structural parameters estimated from the standard bunching approach, it is more common for papers in this literature to use these structural parameters to identify hypothetical schedules that would improve or maximize welfare (see, for example, Best et al. (2015) or Bachas and Soto (2021)).

> 2. This is not always the case: in some applications, structural parameters appear robust to model augmentations, e.g., Best et al. (2020).

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very likely to be the case that the government is willing to spend R$1 to get R$0.90 to BF recipients. While the welfare impact of this reform is important in its own right, our application also highlights more generally how our approach can be used to conduct meaningful welfare analyses.

The paper begins by building intuition in a simple, static model in which a government provides a constant transfer only to households who report an income below a certain threshold; hence, the transfer schedule features a notch. Households are endowed with an income and choose how much income to report to the government subject to misreporting costs. We derive bounds on the marginal value of public funds (MVPF) of changing the notch, comprising both an increase in the benefit level and eligibility threshold. The MVPF is the ratio of households’ willingness-to-pay (WTP) for the reform relative to the government’s budgetary cost of the reform (Hendren and Sprung-Keyser, 2020). We show that aggregate WTP for the reform (and, in turn, the MVPF) can be bounded using two empirical objects: (1) the number of “bunching households” who bunch at the old notch and move towards the new notch as a result of the reform, and (2) the number of “jumping households” who jump down to bunch at the new notch as a result of the reform. To calculate WTP for the reform, we first note that for households who do not jump or bunch, their WTP is simply equal to the amount of additional money they receive as a result of the reform. However, for the jumping and bunching households, their WTP for the reform differs from their increase in benefits; this is because we cannot simply appeal to the envelope condition in our setting as we consider arbitrary discrete reforms. In particular, by jumping down to the new notch, jumping households receive the new benefit but also incur a misreporting cost. By revealed preference, jumping households’ utility is improved by changing their behavior; hence their WTP is weakly positive. Moreover, their WTP cannot exceed the size of the new benefit given that misreporting costs are weakly positive. Thus, each jumping household has a WTP between 0 and the size of the new benefit. On the other hand, bunching households see an increase in the size of their benefit as well as a reduction in their misreporting costs as they move toward the new, higher notch. Thus, bunching households’ WTP for the reform is at least as large as their increase in benefits; moreover, by revealed preference, their WTP cannot exceed the size of the new benefit level because if it did, it would not have been optimal for these households to bunch at the original notch in the first place. We can use these bounds on household WTP to bound aggregate WTP for the reform (and, in turn, the MVPF) as long as we can observe the number of bunching and jumping households. Because the welfare impact of a reform is equal to the MVPF multiplied by a normative welfare weight, our bounds on the MVPF enable us to make welfare statements about the impacts of changing a notch using estimable, reduced-form objects.

While our results are initially stated in the context of a simple, static misreporting model to build intuition, we show that our welfare bounds are highly robust to the agent problem. In particular, our bounds hold in models with any sort of behavioral response margin (e.g., labor supply responses instead of misreporting responses), arbitrary preference heterogeneity, adjustment costs, limited choice sets (e.g., labor supply frictions), and (non-extreme) misperceptions of the benefit schedule. Moreover, we discuss how our bounds can be augmented to allow for dynamic decision making with uncertainty and for more complex policy environments such as in-kind transfers and the presence of other tax and transfer schedules. We view this generality as a key contribution: the number of jumping and bunching households can be used to bound the MVPF of a notch change in a wide class of models. We therefore refer to the number of jumping and bunching households as the sufficient statistics to bound the MVPF, and in turn, the welfare impact of a notch change.

The second part of this paper is concerned with bounding the welfare impacts of a reform to a notch 2
in one of the world’s largest cash transfer programs, Bolsa Fam ́ılia (BF). BF is a Brazilian anti-poverty program that started in 2003 and gave benefits to around 14 million households as of 2014 (Gazola Hellmann, 2015). Eligibility for BF benefits is based on self-reported household income, likely generating substantial scope for misreporting given that approximately 50% of economically active individuals work in the informal sector (Henley, Arabsheibani and Carneiro, 2009). Importantly, the BF schedule features a pronounced notch that was expanded in June 2014. Prior to June 2014, households reporting a per-capita income below the extreme-poverty threshold of R$70 per-month were eligible for an unconditional monthly benefit of R$70 per-month, whereas households reporting an income above this threshold were not.<sup>3</sup> In June 2014, both the eligibility threshold and benefit were raised by 10%: the eligibility threshold increased from R$70 per-capita, per-month to R$77 per-capita, per-month, while the unconditional benefit increased from R$70 per-month to R$77 per-month.

We have access to administrative data spanning December 2011 to September 2016 from Cadastro Unico,<sup> ́</sup> which is the Brazilian government’s national registry used to determine eligibility for all federal social welfare programs. Using this data, we seek to estimate the number of original bunching households who move towards the new notch and the number of households jumping down to the new notch as a result of the reform. The number of bunching households is simply equal to the reduction in the bunching mass at the old notch (as a result of reform), while the number of jumping households is equal to the increase in the bunching mass at the new notch less the reduction in the bunching mass at the old notch (as a result of the reform). However, when looking at the raw data, there are clear time trends in the number of households locating at the old and new notch in the pre-reform period. Thus, our identification challenge is to understand how the number of households reporting incomes at the old and new notch would have evolved in the post-reform period had the reform not occurred.

At a high level, our identification strategy is based on the following insight: the incentives to report an income at and above the original notch are affected by the reform, but the incentives to report an income below the original notch are unaffected by the reform. Hence, we can use portions of the reported income distribution below the original notch as control groups for underlying time trends in the reported income distribution at and above the original notch. To do so, we use a generalized difference-in-difference strategy as employed in, for example, Wolfers (2006) or Mora and Reggio (2013). A standard difference-in-difference estimator requires that the control groups and treatment groups have “parallel trends” pre-reform that would have persisted in the post-reform period had the reform not occurred. Similarly, the generalized difference-indifference estimator requires that there exist stable relationships, which are well approximated by relatively low order polynomials, between treatment and control groups which existed pre-reform that would have persisted in the post-reform period had the reform not occurred. In our setting, we discretize the reported income distribution into bins, using bins below the original notch as control bins while using bins that include the original and new notches as treatment bins. We then use the estimated relationships between treatment and control bins in the pre-reform period to create counterfactuals for how the treatment bins would have evolved absent the reform. Fundamentally, there are complex structural relationships between the number of people reporting in each income bin; these relationships are determined by how the true income distribution is evolving over time, how the true income distribution is mapped to the reported income distribution, as

> 3. BF also includes a conditional variable benefit for households with children. To receive this variable benefit, households must make specified health and education investments in their children and have a reported per-capita income below the “poverty threshold” (which is higher than the extreme-poverty threshold). We restrict our attention to the _unconditional_ component of BF in this paper.

3
well as growth in applicants to the BF program over time. Our generalized difference-in-difference strategy essentially assumes that the differences over time between the number of people reporting in each income bin are well approximated by (low-order) polynomials which would have persisted in absence of the reform; this assumption appears to hold in the pre-reform period, lending credence to our identification assumptions. Moreover, we implement a number of placebo tests which further support the validity of our identification assumptions.

Using this generalized difference-in-difference strategy, we find that the number of households reporting incomes at the new notch increased by approximately 49,000 and the number of households reporting incomes at the old notch decreased by approximately 27,000 as a result of the reform. Hence, the reform induced 27,000 bunching households to move toward the new threshold and an additional 22,000 households to jump down to the new threshold. This translates into a lower bound for the MVPF of the reform of approximately 0.9 and an upper bound for the MVPF of approximately 1.12. In terms of welfare implications, as long as the government values giving R$0.90 (in a non-distortionary manner) to the BF households more than spending R$1 on their next best alternative, the reform was welfare improving. We argue that this is likely the case given that BF has high coverage of households in extreme poverty and given that the households misreporting to get the benefit typically fall in the poorest half of the population (Bastagli (2008) and Lindert et al. (2007)). A back-of-the-envelope calculation suggests that the welfare effect of spending R$1 on the BF reform is at least as high as the welfare effect of spending R$1.50 on a non-distortionary universal transfer. Hence, our empirical findings contribute to the debate around targeted vs. universal transfers in developing settings (Hanna and Olken, 2018): we find that even in a setting with a highly pronounced notch and substantial scope for misreporting, the efficiency cost generated by behavioral responses is simply not large enough to outweigh the equity gain associated with the increased generosity of benefits targeted to poor households (relative to a universal transfer).

_Relationship to the literature:_ We believe it is helpful to further compare and contrast our paper with the growing literature that explores bunching at notches and kinks. Papers in this literature typically use reduced-form bunching evidence to pin down parameters of interest by making structural assumptions on agent optimization problems. For example, Kleven (2016) notes that inferring a structural parameter from reduced-form bunching evidence requires structural assumptions and that “changing any of these model features will in general change the mapping between bunching and structural parameters.” Conversely, our approach uses reduced-form bunching evidence in a sufficient statistics approach (i.e., without making substantive parametric assumptions on the agent optimization problem). In line with Chetty (2009), we view our approach as a complement rather than a substitute to standard bunching approaches because they have opposing strengths and weaknesses. The strength of our approach lies in obviating the need for strong parametric assumptions while the weaknesses are that our bounds are only relevant for the reform in question and that our approach is more data intensive because to estimate changes in bunching masses without structural assumptions, one requires cross-sectional data in both the pre- and post-reform period.

Our empirical strategy also differs from standard bunching analyses despite being conceptually similar insofar as both methods use portions of the distribution which are unimpacted by the notch (or, in our case, the notch change) to infer properties about portions of the distribution which are impacted by the notch (or notch change). In particular, we focus on estimating _changes_ in bunching that result from a reform, whereas standard bunching analysis typically focuses on estimating bunching at a given notch or 4
kink. Using a difference-in-difference strategy, we use portions of the distribution unimpacted by the reform to control for underlying time trends in portions of the distribution which are impacted by the reform. Conversely, the standard bunching approach uses portions of the distribution unimpacted by the notch combined with smoothness assumptions on the underlying counterfactual distribution to non-parametrically identify bunching induced by the notch. One may wonder if we could have adapted the standard bunching approach to estimate changes in bunching while controlling for underlying time trends as done in Carril (2022);<sup>4</sup> however, as discussed further in Section 4.3, our distribution of reported incomes is extremely nonsmooth (we have extreme bunching at numbers equal to 0 mod 50, substantial bunching at numbers which were notches many years earlier, and less extreme bunching at numbers equal to 0 mod 10). While bunching estimation methods have been augmented to deal with “round-number” bunching and bunching at “referencepoints” (e.g., Kleven and Waseem (2013) and Best and Kleven (2017)), we believe that the pervasiveness and the variability of round-number and reference-point bunching in our setting will make it too difficult to precisely identify the counterfactual distributions around our notches (in particular, around the original notch of R$70 which is equal to 0 mod 10). Thus, our empirical strategy highlights an alternative way to estimate changes in bunching when smoothness assumptions cannot be used to estimate counterfactual distributions.<sup>5</sup> Finally, on the theoretical side, our paper contributes to the sufficient statistics approach for welfare analysis (Chetty, 2009). One broad contribution to this literature is showing how to apply a sufficient statistics framework to settings with large, discrete policy reforms when the envelope condition cannot be applied. Kleven (2021) discusses how to do approximate welfare analysis using an expanded set of sufficient statistics when reforms are large; however, he argues that these additional statistics may not be easily estimable. We overcome this need to estimate difficult statistics by focusing on welfare bounds. This paper is also related to Lockwood (2020) who observes that in the presence of notches, the sufficient statistic approach for the welfare analysis of tax systems needs to be augmented to include a correction term which captures the change in bunching at a notch in response to a tax reform. Our key theoretical contribution relative to Lockwood (2020) is the generality of our results. Whereas Lockwood (2020) characterizes the welfare impacts of particular infinitesimal reforms to notches in a model with quasi-linear utility, one dimension of agent heterogeneity, and one choice variable, our approach allows us to bound the welfare impacts of reforms to programs with notches of any size while placing very little structure on the agent problem.<sup>6</sup> The remainder of the paper is organized as follows. Section 2 introduces the theoretical framework for welfare analysis of changing notches, Section 3 discusses the structure of the Bolsa Fam ́ılia program, Section 4 discusses our strategy to empirically identify the number of jumping and bunching households for the June 2014 reform, Section 5 presents our results and robustness analysis, and Section 6 concludes. 4. Carril (2022) uses standard bunching techniques to estimate the counterfactual distributions that would ensue in absence of a notch in both the pre- and post-reform periods and then uses changes in these counterfactual distributions to control for underlying dynamics. In contrast, we use portions of the observed distribution that are unimpacted by the reform to control for underlying dynamics.

5. While methodologically different, our approach is conceptually similar to Best et al. (2020) who also use the behavior of non-bunching individuals to make inferences about the counterfactual behavior of bunching individuals.

6. We also allow for changes in the location of the notch, which turns out to be more technically complicated.

5
# 2 Theoretical Framework for Welfare Analysis of Changing Notches

This section derives bounds for the welfare impact of changing a notch in a transfer program. We begin by deriving bounds in a simple, static misreporting model. This simple setup is useful not only for building intuition but also because misreporting responses are likely common in our empirical application. We show that we can bound the welfare impact of a notch change using two empirical objects: (1) the number of households bunching at the old notch who move towards the new notch as a result of the reform, and (2) the number of households who jump down to the new notch as a result of the reform. Finally, we show that our results still hold in a much more general model which puts minimal structure on the household problem, thereby arguing that our two empirical objects are “sufficient statistics” to bound the change in welfare from a notch change.

## _2.1 Baseline Model Set-Up_

To begin, we consider a static world in which households choose how much income to report, _y_ ˆ, subject to a policy **p** = _{b, τ }_ where _b_ denotes the level of the benefit and _τ_ denotes the cut-off level of reported income s.t. those reporting _y_ ˆ _≤ τ_ receive _b_ and those reporting _y_ ˆ _> τ_ receive nothing.<sup>7</sup> Households have two dimensions of heterogeneity: (1) endowed income _y_ distributed according to CDF _F_ ( _y_ ), and (2) aversion to misreporting governed by _μ ∈{_ 1 _,_ 2 _}_ with probability mass function _π_ ( _μ_ ). Type _μ_ = 1 households are “truth-telling” households who never misreport, whereas type _μ_ = 2 households are willing to misreport their income. For simplicity, we assume there is no fixed cost of reporting an income and that all households know the policy **p** . We also assume households have quasi-linear utility in consumption. Type _μ_ = 1 households therefore have utility under policy **p** given by: Utility for type _μ_ = 2 households under policy **p** is equal to: ˆ ˆ ˆ where _v_ ( _y − y_ ) 1 ( _y > y_ ) captures the disutility of reporting _y_ when true income is _y_ . We assume _v_<sup>_′_</sup> _>_ 0 and _v_<sup>_′′_</sup> _≥_ 0 so that the cost of misreporting is increasing and convex in the discrepancy between true and reported income.<sup>8</sup> If a household is indifferent between reporting truthfully and over-reporting, we break their indifference by assuming they report truthfully.

Optimal reported incomes, _y_ ˆ<sup>_∗_</sup> , for type _μ_ = 2 households are characterized as follows (see Appendix A.1

> 7. For the sake of parsimony, our theoretical framework ignores other aspects of the tax and transfer system. Thus, we assume that behavioral responses to changes in the notch do not have budgetary impacts on other programs. We discuss how our framework can account for other aspects of the tax and transfer schedule in Section 2.3 and how potential fiscal externalities impact our findings in Section 5.2.

> 8. Modeling evasion using a convex and deterministic cost function _v_ ( _·_ ) dates back to Mayshar (1991) and Slemrod (2001).

6
for a formal derivation): where _y_<sup>_c_</sup> ( **p** ) is the income level for which households are indifferent between misreporting at _τ_ and reporting truthfully, implicitly defined by _y_<sup>_c_</sup> ( **p** ) + _b − v_ ( _y_<sup>_c_</sup> ( **p** ) _− τ_ ) = _y_<sup>_c_</sup> ( **p** ). In words, type _μ_ = 2 individuals with _y < τ_ report truthfully and get the benefit, those with _y ∈_ ( _τ, y_<sup>_c_</sup> ( **p** )] get the benefit by misreporting and bunching at the notch, and those with _y > y_<sup>_c_</sup> ( **p** ) report their income truthfully and do not get the benefit.

Next, we define _G_ ( _x_ ; **p** ) to capture the number of households reporting an income less than or equal to _x_ under policy **p** : Hence, _G_ ( _τ_ ; **p** ) captures the number of households locating under the eligibility threshold _τ_ . Finally, we assume that total social welfare under policy **p** , _W_ ( **p** ), is given by a weighted sum of household utilities evaluated at optimal choices under policy **p** less the budgetary cost of the policy multiplied by the shadow value of public funds _λ_ , which captures the welfare gain of spending a dollar on the government’s next best alternative. In other words, we assume that spending $1 on the program comes at the cost of spending $1 less on some other program which decreases welfare by a constant value _λ_ . Welfare under policy **p** is therefore given by: where _φ_ ( _y, μ_ ) denotes the government’s welfare weight on a household with income _y_ and type _μ_ .

# _2.2 Welfare Effect of the Reform in the Baseline Model_

Our goal is to evaluate the welfare impact of a reform from policy **p** = _{b, τ }_ to **p**<sup>_′_</sup> = _{b_<sup>_′_</sup> _, τ_<sup>_′_</sup> _}_ , defining _{_ ∆ _b,_ ∆ _τ }_ = **p**<sup>_′_</sup> _−_ **p** . For ease of exposition, let us assume ∆ _b >_ 0 and ∆ _τ >_ 0 (i.e., we increase the level and location of the notch). Note that we are _not_ restricting to infinitesimal reforms; the bounds we derive allow for arbitrary, discrete reforms to _b_ and _τ_ . Our goal is to derive bounds for _W_ ( **p**<sup>_′_</sup> ) _−W_ ( **p** ) in terms of empirically observable objects (we discuss the advantages of focusing on bounding the welfare impact as opposed to characterizing the exact impact in Section 2.3). Hendren and Sprung-Keyser (2020) show that the welfare impacts of any policy reform can be expressed in terms of a _normative_ welfare weight along with a _positive_ sufficient statistic, denoted the marginal value of public funds (MVPF), which captures households’ willingness-to-pay (WTP) for the reform relative to the total budgetary cost of the reform. Our goal then is to derive bounds for the MVPF.

Because the utility function is quasi-linear, a household with income _y_ and misreporting type _μ_ has a WTP for the reform implicitly defined by: Equivalently, WTP is simply equal to the compensating variation. We now heuristically derive bounds on the WTP for all households impacted by the reform (we formally derive these bounds in the proof to Lemma 7
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most the bunching households can value this reduction in misreporting costs is _b_ dollars. If they value this reduction by more than _b_ dollars, it would not have been optimal for these households to bunch at _τ_ under policy **p** .<sup>11</sup> Thus, the bunching households’ WTP for the reform is in [∆ _b,_ ∆ _b_ + _b_ ] = [∆ _b, b_<sup>_′_</sup> ].

The threshold households are the households who report in ( _τ, τ_<sup>_′_</sup> ] under policy **p** . Thus, the number of threshold households is given by _T_ = _G_ ( _τ_<sup>_′_</sup> ; **p** ) _− G_ ( _τ_ ; **p** ). Notably, these households will not update their behavior in response to the reform. This is because all households reporting above _τ_ given policy **p** are reporting truthfully regardless of their type _μ_ . Under **p**<sup>_′_</sup> the optimal choice for these households is to continue reporting truthfully as doing so allows them to receive _b_<sup>_′_</sup> and not incur any misreporting costs. These households go from receiving no benefits to receiving _b_<sup>_′_</sup> in benefits. Hence their WTP is equal to _b_<sup>_′_</sup> .

Finally, the jumping households are the households who report above _τ_<sup>_′_</sup> given policy **p** but who report at _τ_<sup>_′_</sup> given policy **p**<sup>_′_</sup> . In particular, households who were previously close-to-indifferent between misreporting at the threshold and truthfully reporting above the threshold but opted for the latter (i.e., type _μ_ = 2 households with _y ∈_ ( _y_<sup>_c_</sup> ( **p** ) _, y_<sup>_c_</sup> ( **p**<sup>_′_</sup> )]) will now jump and misreport to the new threshold _τ_<sup>_′_</sup> .<sup>12</sup> Notably, we describe the behavioral response of these households as a “jump” because these households experience a discontinuous change in their optimal reported income as we move from **p** to **p**<sup>_′_</sup> . The number of jumping households, _J_ , is given by _J_ = _G_ ( _τ_<sup>_′_</sup> ; **p**<sup>_′_</sup> ) _− G_ ( _τ_<sup>_′_</sup> ; **p** ), which is equivalent to the increase in households reporting at or below the new threshold _as a result of the reform_ (note, the number of jumping households is not equal to the mass of households locating at _τ_<sup>_′_</sup> given policy **p**<sup>_′_</sup> as some of the households locating at _τ_<sup>_′_</sup> may be original bunching households who moved with the notch). By revealed preference, jumping households’ utility is improved by changing their behavior; hence, their WTP is weakly positive.<sup>13</sup> Moreover, after the reform, jumping households get _b_<sup>_′_</sup> more dollars but incur misreporting costs. Therefore jumping households’ WTP cannot exceed _b_<sup>_′_</sup> as misreporting costs are weakly positive. Hence the WTP of jumping households is in [0 _, b_<sup>_′_</sup> ].

Table 1 summarizes the bounds on the WTP for each of our four groups along with the number of households falling into each group and the cost that each group imposes on the government.

Table 1: WTP and Cost to the Government of the Reform

|Group|Number of households|WTP (per-household)|Cost to Govt. (per-household)|
|---|---|---|---|
|Mechanical Households|_M_ =_G_(_τ_;**p**<sup>_′_</sup>)|∆_b_|∆_b_|
|Bunching Households|_B_ =_G_(_τ_;**p**)_−G_(_τ_;**p**<sup>_′_</sup>)|_∈_[∆_b, b_<sup>_′_</sup>]|∆_b_|
|Threshold Households|_T_ =_G_(_τ _<sup>_′_</sup>;**p**)_−G_(_τ_;**p**)|_b_<sup>_′_</sup>|_b_<sup>_′_</sup>|
|Jumping Households|_J_ =_G_(_τ _<sup>_′_</sup>;**p**<sup>_′_</sup>)_−G_(_τ _<sup>_′_</sup>;**p**)|_∈_[0_, b_<sup>_′_</sup>]|_b_<sup>_′_</sup>|

_Note:_ This table shows the willingness-to-pay (WTP) and cost to the government for all the households impacted by the reform of moving from policy **p** to **p**<sup>_′_</sup> . We split the households into four groups: mechanical, bunching, threshold, and jumping households.

This brings us to Lemma 1 which bounds the total WTP for the reform:

**Lemma 1.** _If individuals solve Problem (2), the total WTP of the reform from_ **p** _to_ **p**<sup>_′_</sup> _with_ **p**<sup>_′_</sup> _−_ **p** =

> 11. Suppose bunching households have a WTP for the relaxation in their misreporting costs greater than _b_ : _v_ ( _y−τ_ ) _−v_ ( _y−τ_<sup>_′_</sup> ) _> b_ . This implies _v_ ( _y − τ_ ) _> b_ . However if _v_ ( _y − τ_ ) _> b_ , bunching households would have preferred to report truthfully above _τ_ over misreporting at _τ_ under policy **p** .

> 12. For large changes in _τ_ s.t. _y_<sup>_c_</sup> ( **p** ) _< τ_<sup>_′_</sup> , only _μ_ = 2 households with _y ∈_ ( _τ_<sup>_′_</sup> _, y_<sup>_c_</sup> ( **p**<sup>_′_</sup> )] jump and misreport to the new notch.

> 13. For an infinitesimal reform, jumping households have a WTP of 0 as the only households who jump are those that are indifferent between locating at the notch and reporting truthfully. Thus, our lower bound for the WTP for jumping households is exact for an infinitesimal reform. Note, however, that the jumping households still have a first order impact on social welfare through their effect on the government’s budget as each jumping household costs the government _b_<sup>_′_</sup> dollars (despite the fact that the mass of jumpers is measure 0 for an infinitesimal reform; see Bergstrom and Dodds (2021) for further discussion).

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_{_ ∆ _b,_ ∆ _τ } >_ 0 _can be bounded as follows:_ _where M, B, T and J denote the mass of mechanical, bunching, threshold and jumping households mathematically defined in Table 1._

# _Proof._ See Appendix A.2.

Moreover, using the cost per-household to the government given in Table 1, we can express the total budgetary cost of the reform as follows: Hence, we can construct bounds for the MVPF of the reform as follows:

**Proposition 1.** _If individuals solve Problem (2), the marginal value of public funds of the reform from_ **p** _to_ **p**<sup>_′_</sup> _with_ **p**<sup>_′_</sup> _−_ **p** = _{_ ∆ _b,_ ∆ _τ } >_ 0 _can be bounded as follows:_

_Proof._ This follows directly from Lemma 1 and Equation (4).

The lower bound for the MVPF captures the fact that the lower bound for the WTP of the jumping households is 0 while the cost they impose on the government is _b_<sup>_′_</sup> each (whereas the lower bound for the WTP of bunching households is exactly equal to the cost they impose on the government). Hence, if all jumping households value the reform at their lower bound, _b_<sup>_′_</sup> _J/_ (Total Cost) of each dollar of spending is “wasted”. Meanwhile, the upper bound for the MVPF captures the fact that the upper bound for the WTP of the bunching households is _b_<sup>_′_</sup> while the cost they impose on the government is only _b_<sup>_′_</sup> _− b_ (whereas the upper bound for the WTP of jumping households is exactly equal to the cost they impose on the government). Hence, if bunching households all value the reform at their upper bound, the government “gains” _bB/_ (Total Cost) for each dollar of spending. We can then use these bounds on the MVPF to construct bounds on the money metric welfare gain relative to the budgetary cost of the reform using Proposition 2:<sup>14</sup>

**Proposition 2.** _If individuals solve Problem (2) and social welfare is given by Equation (3), then the money metric welfare gain relative to the budgetary cost of the reform from_ **p** _to_ **p**<sup>_′_</sup> _with_ **p**<sup>_′_</sup> _−_ **p** = _{_ ∆ _b,_ ∆ _τ } >_ 0 _can be bounded as follows:_

> 14. Note, that the welfare change is expressed in dollar units (as opposed to welfare units) as we divide through by the shadow value of public funds, _λ_ .

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_where ωL (ωU ) captures the weighted average money-metric welfare gain from giving a dollar to mechanical, bunching, threshold, and jumping households, where the weights are determined by the relative size of each group’s lower bound (upper bound) for WTP._ _Proof._ We do not provide a separate proof for Proposition 2; we only provide a proof for Proposition 3, which nests Proposition 2 (see Appendix A.3).

Proposition 2 bounds the increase in total welfare from spending $1 on the reform. In particular, _MV PFL_ captures our lower bound on the total WTP of the mechanical, bunching, threshold, and jumping households when we spend $1 on the reform, while _ωL_ denotes the welfare gain, measured in dollars, of splitting $1 among the mechanical, bunching, threshold, and jumping households (where the split is determined by the lower bounds on each group’s WTP for the reform). Subtracting the budgetary cost of $1 from _ωLMV PFL_ gives a lower bound for the total welfare gain of spending $1 on the reform. Symmetric logic explains why _ωU MV PFU −_ 1 is an upper bound for the increase in total welfare, measured in dollars, of spending $1 on the reform.

Finally, in light of Proposition 1, we can express _MV PFL_ and _MV PFU_ in terms of two positive objects: (1) the number of bunching households, and (2) the number of jumping households. Thus, the number of bunchers and jumpers are the empirical objects needed to construct bounds for the welfare impact of the reform.<sup>15</sup>

# _2.3 Robustness to Model Specification_

To highlight the robustness of our bounds for the welfare impact, we now show that we actually require very little structure on preferences or behavioral responses of agents. Suppose households have several decisions variables denoted by the vector _x_ within a choice set _X_ . Household decisions are made conditional on primitives denoted by the vector _θ ∈_ Θ and the policy **p** . Households get the benefit _b_ if their reported ˆ income _y_ , which can be a decision variable or a function of decision variables and primitives, is below _τ_ . Household income, denoted _y_ , is also potentially a function of decisions _x_ .<sup>16</sup> Households solve: where _c_ denotes consumption. We assume total welfare is given by a weighted sum of utilities, with welfare weights given by _φ_ ( _θ_ ): where _λ_ represents the shadow value of public funds and _G_ ( _τ_ ; **p** ) = � _θ_ :ˆ _y_ ( _θ,_ **p** ) _≤τ_<sup>_dF_(</sup><sup>_θ_) represents the number of</sup> households receiving the benefit under policy **p** . More generally, we define _G_ ( _z_ ; **p** ) = � _θ_ :ˆ _y_ ( _θ,_ **p** ) _≤z_<sup>_dF_(</sup><sup>_θ_).This</sup> setup allows us to substantially generalize Proposition 1 and Proposition 2:

> 15. Technically, we also need to know the total cost of the reform; however, Equation (4) shows that the total cost is a function solely of _G_ ( _τ_<sup>_′_</sup> ; **p**<sup>_′_</sup> ) and _G_ ( _τ_ ; **p** ), which are needed to construct _J_ and _B_ .

> 16. For example, in a labor supply model, _x_ could equal household labor supply _l_ , _θ_ could include productivity _n_ , and _y_ ˆ = _y_ = _nl_ .

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**Proposition 3.** _Suppose households solve Problem (5), welfare is given by Equation (6), and τ_<sup>_′_</sup> _> τ . Defining:_

_Then as long as b_<sup>_′_</sup> _G_ ( _τ_<sup>_′_</sup> ; **p**<sup>_′_</sup> ) _− bG_ ( _τ_ ; **p** ) _>_ 0 _have:_ _where ωL (ωU ) captures the weighted average money-metric welfare gain from giving a dollar to mechanical, bunching, threshold, and jumping households, where the weights are determined by the relative size of each group’s lower bound (upper bound) for WTP._

# _Proof._ See Appendix A.3.

Proposition 3 highlights that we can bound the MVPF and, consequently, bound the welfare impacts of the reform using empirically observable objects while only putting limited structure on the household problem.<sup>17</sup> 18 In particular, to bound the MVPF we simply need to estimate how the number of people locating below the new notch changes as a result of the reform, _J_ = _G_ ( _τ_<sup>_′_</sup> ; **p**<sup>_′_</sup> ) _− G_ ( _τ_<sup>_′_</sup> ; **p** ), as well as how the number of people locating below the old notch changes as a result of the reform, _B_ = _G_ ( _τ_ ; **p** ) _− G_ ( _τ_ ; **p**<sup>_′_</sup> ).<sup>19</sup> In the context of our simple baseline model, _B_ equals the number of households bunching at the original notch and _J_ equals the number of households jumping down to bunch at the new notch. However, if households solve the more general household problem (5), the _interpretation_ of these terms may be changed. For instance, consider a labor supply model in which households can only work full-time, half-time, or not at all. In this case _B_ = _G_ ( _τ_ ; **p** ) _− G_ ( _τ_ ; **p**<sup>_′_</sup> ) simply captures the change in the number of households reporting at or below the original notch as a result of the reform, which does not correspond to a reduction in the bunching mass at the original notch as almost all households cannot precisely bunch. Similarly, _J_ = _G_ ( _τ_<sup>_′_</sup> ; **p**<sup>_′_</sup> ) _− G_ ( _τ_<sup>_′_</sup> ; **p** ) simply captures the change in the number of households reporting below the new notch as a result of the reform, which does not correspond to the number of households jumping down to bunch at the new notch as almost all households cannot precisely bunch. Nonetheless, for ease of exposition, we will continue to refer to _B_ as the number of bunching households and _J_ as the number of jumping households.

The core intuition for Proposition 3 is that we can again use revealed preference arguments to bound WTP for a reform from policy **p** to policy **p**<sup>_′_</sup> . And these revealed preference arguments require very little structure on household utility, household heterogeneity, the choice variables, or choice sets available to households.

> 17. We are slightly abusing notation here. Our upper bound for the MVPF, _MV PFU_ , is actually the upper bound on the MVPF from moving from policy **p**<sup>_′_</sup> to **p** . This is because our upper bound on the WTP is actually an upper bound on the negative WTP of moving from policy **p**<sup>_′_</sup> to **p** , or equivalently, it is an upper bound on the willingness-to-accept (WTA) to move from policy **p** to **p**<sup>_′_</sup> . We obviate this distinction in Proposition 1 by making the assumption that utility is quasi-linear in consumption, so that WTP=WTA.

> 18. Note that in Proposition 3 we have assumed _τ_<sup>_′_</sup> _> τ_ and that _b_<sup>_′_</sup> _G_ ( _τ_<sup>_′_</sup> ; **p**<sup>_′_</sup> ) _− bG_ ( _τ_ ; **p** ) _>_ 0. Assuming _τ_<sup>_′_</sup> _> τ_ is WLOG because one can also use Equation (9) to get bounds on the welfare gain from moving from **p**<sup>_′_</sup> to **p** . On the other hand, if _b_<sup>_′_</sup> _G_ ( _τ_<sup>_′_</sup> ; **p**<sup>_′_</sup> ) _− bG_ ( _τ_ ; **p** ) _<_ 0, both inequalities in Equation (9) are simply reversed.

> 19. Again, we also need to know the total cost of the reform; but the total cost can be constructed from _G_ ( _τ_<sup>_′_</sup> ; **p**<sup>_′_</sup> ) and _G_ ( _τ_ ; **p** ), which are also needed to construct _J_ and _B_ .

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Problem (5) can encompass a variety of important realisms: (1) households may respond by changing labor supply instead of misreporting their income (or respond on a variety of dimensions),<sup>20</sup> (2) households may face limited choice sets (e.g., restrictions on labor supply), (3) households may face reporting costs (e.g., hassle or time costs) and thereby face a decision of whether to report/update their income on the registry<sup>21</sup> , (4) households may have a wide range of heterogeneity in their utility functions (e.g., households may have varying preferences over the labor/leisure trade-off or varying preferences to locate at round numbers). We view this robustness as perhaps the most important aspect of our theory: we can construct bounds for the MVPF of changing a notch in a manner which is, in large part, model-free.

But of course there are _some_ implicit restrictions encoded in the assumed household problem (Problem (5)) used to prove Proposition 3. Perhaps most importantly, Proposition 3 requires that households correctly perceive the benefit schedule and the reform. The proof to Proposition 3 uses the fact that household reoptimization _improves_ utility; if misperceptions are extreme for many households this may not be the case. However, it is straight-forward to extend Proposition 3 when households misperceive the schedule if we are willing to assume that, on average, behavioral responses to the reform from **p** to **p**<sup>_′_</sup> improve welfare (i.e., perceptions are not so extreme that households, on average, harm themselves by responding to the reform; see Appendix A.5). For example, if some proportion of households are entirely unaware of the reform while the rest of the population is perfectly aware of the reform, our bounds hold as unaware households will not respond to the reform whereas those who are aware of the reform improve their utility via their behavioral response.<sup>22</sup> Moreover, Problem (5) is also a static problem, so that Proposition 3 does not allow for dynamic decision making or uncertainty. We augment Proposition 3 in Appendix A.6 to show that we can bound the discounted welfare impact of the policy over time relative to the discounted total budgetary cost in a general dynamic model allowing for income dynamics, savings, and stochastic shocks. In this case, the relevant bounds for the MVPF are constructed using the discounted sum of the expected number of jumping households over time and the discounted sum of the expected number of bunching households over time. Proposition 3 also requires that there are no externalities from household decisions so that decisions of one household do not directly impact the utility of any other household. Our bounds can be generalized to allow for externalities by augmenting the upper and lower bounds for the MVPF with an additional term measuring the WTP for these externalities relative to the total cost; however, measuring WTP for externalities is likely difficult in practice.

Additionally, Proposition 3 can be augmented to allow for more complex policy environments. Proposition 3 assumes that there is no underlying tax and transfer system beyond the benefit _b_ given to those with a ˆ reported income _y ≤ τ_ . But we can easily extend Proposition 3 to account for more complex underlying tax and transfer schedules; in this case, the total budgetary cost of the reform must include the impacts that behavioral responses have on other programs that impact the government’s budget (i.e., we need to calculate the fiscal externalities associated with the reform).<sup>23</sup> Proposition 3 also assumes that the transfer is given in

> 20. This is consistent with Feldstein (1999), who argues that the efficiency costs of taxation do not depend on whether behavioral responses occur on the labor supply margin or the misreporting margin.

> 21. To capture adjustment/updating costs, one could suppose _x_ = _y_ ˆ _t_ and _θ_ consists of current income _yt_ , aversion to misreˆ porting _μ_ , and prior reported income _yt−_ 1; households incur an adjustment cost _k_ if their reported income today differs from prior reported income.

> 22. In the extreme case where all households are unaware, both _B_ and _J_ are 0 so that our upper and lower bounds for the MVPF coincide at 1, which is definitionally the MVPF of non-distortionary cash transfers. 23. In particular, the total cost of the reform would equal _b_<sup>_′_</sup> _G_ ( _τ_<sup>_′_</sup> ; **p**<sup>_′_</sup> ) + _R_ ( **p**<sup>_′_</sup> ) _− bG_ ( _τ_ ; **p** ) _− R_ ( **p** ) where _R_ ( **p** ) denotes net

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cash; if the transfer is paid in-kind, one would require an estimate of the average WTP for $1 worth of the in-kind good to apply an analogue to Proposition 3.

Lastly, we discuss the advantages of bounding the welfare impacts (as opposed to exactly characterizing the welfare impacts) of a notch reform. First, because we cannot apply envelope conditions in our setting, exactly characterizing welfare impacts requires one to take a stance on which margins households are responding, the functional form of their utility function, the sorts of frictions they face, etc., whereas bounding welfare impacts requires very little structure on the household optimization problem. In fact, we prove in Appendix A.4 that the bounds in Proposition 3 are as tight as possible without making additional assumptions on primitives. Second, our bounds on the welfare impact of a notch change are expressed in terms of estimable reducedform objects, whereas exactly characterizing welfare impacts would require one to estimate a potentially large number of structural parameters.

We now turn to our empirical application: estimating the number of bunching and jumping households for the June 2014 Bolsa Fam ́ılia reform, and, in turn, calculating bounds for the welfare impact of this reform. We begin by describing the structure of the Bolsa Fam ́ılia program, our data, and the June 2014 reform.

# 3 The Bolsa Fam ́ılia Program

The Brazilian anti-poverty program Bolsa Fam ́ılia (BF) provides cash transfers to poor households based on their reported, monthly per-capita income. BF was implemented in October 2003 and is administered by the social development ministry (Minist ́erio do Desenvolvimento Social, or MDS). BF is one of the world’s largest cash transfer programs with around 14 million households receiving benefits in 2014 (Gazola Hellmann, 2015). Applicants report their information, including information on household income, expenditures, assets, socioeconomic characteristics, and demographic characteristics, to interviewers at Cadastro Unico<sup> ́</sup> agencies, which are program offices spread across Brazil’s 5,570 municipalities. Information is entered by interviewers into the Cadastro Unico<sup> ́</sup> registry. Beneficiaries of the BF program are required to update their information once every 2 years to maintain their benefits.

Eligibility for the BF program is based on reported household per-capita income. Household per-capita income is calculated in five steps. First, the applicant is asked to report labor income for the last month as well as average monthly labor income over the past year for each member in the household (the applicant must present a government-issued ID for herself and for each family member thus making it difficult to register fictitious family members). Second, the applicant is asked to report average monthly income received from five additional sources for each household member (see Appendix B.1, which shows the questionnaire used to calculate monthly income). Third, for each individual, the computer calculates the minimum between the average monthly labor income over the past year and last month’s labor income. Fourth, the computer sums this minimum monthly labor income along with income from the five additional sources to get a measure of government spending under policy **p** (exclusive of spending on BF), and ∆ _R_ = _R_ ( **p**<sup>_′_</sup> ) _− R_ ( **p** ) captures the fiscal externalities of the reform. In this case, the lower and upper bounds for the MVPF are given by:

> <sup><u>[</u></sup><sup>_G_</sup><sup><u>(</u></sup><sup>_τ ′_</sup><sup><u>;</u></sup><sup>**<u>p</u>**</sup><sup>_′_</sup><sup><u>)</u></sup><sup>_−G_</sup><sup><u>(</u></sup><sup>_τ ′_</sup><sup><u>;</u></sup><sup>**<u>p</u>**</sup><sup><u>)]</u></sup><sup>_−_∆</sup><sup>_R_</sup> _J_ ∆ _R MV PFL ≡_ 1 _−_<sup>_b′_</sup> _b_<sup>_′_</sup> _G_ ( _τ_<sup>_′_</sup> ; **p**<sup>_′_</sup> ) _− bG_ ( _τ_ ; **p** ) + ∆ _R_<sup>= 1</sup><sup>_−b′_</sup> Total Cost<sup>_−_</sup> Total Cost

> <sup>**<u>p</u>**</sup><sup><u>)</u></sup><sup>_−G_</sup><sup><u>(</u></sup><sup>_τ_</sup><sup><u>;</u></sup><sup>**<u>p</u>**</sup><sup>_′_</sup><sup><u>)] + ∆</u></sup><sup>_R_</sup> _B_ ∆ _R MV PFU ≡_ 1 +<sup>_b_</sup><sup><u>[</u></sup><sup>_G_</sup><sup><u>(</u></sup><sup>_τ_</sup><sup><u>;</u></sup> _b_<sup>_′_</sup> _G_ ( _τ_<sup>_′_</sup> ; **p**<sup>_′_</sup> ) _− bG_ ( _τ_ ; **p** ) _−_ ∆ _R_<sup>= 1 +</sup><sup>_b_</sup> Total Cost<sup>_−_</sup> Total Cost Thus, in addition to _B_ and _J_ , we need to observe ∆ _R_ to assess the welfare impact of the reform.

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total monthly income for each individual. Finally, the computer sums this individual total monthly income across all household members and divides it by the number of household members.

The government then transfers a monthly, unconditional benefit (referred to as the “basic benefit”) to all households reporting a per-capita income below the “extreme-poverty threshold” and transfers an additional benefit (referred to as the “variable benefit”) to households with children who have a reported per-capita income below the higher “poverty threshold” conditional on these households making health and education investments in their children.<sup>24</sup> Between July 2009 and June 2014, the extreme-poverty threshold was R$70 per-capita, per-month and the poverty threshold was R$140 per-capita, per-month.

Finally, the MDS has several enforcement mechanisms to prevent income misreporting. First, during the interview, the income questions come at the end of the questionnaire so that questions on expenditures and assets can help the interviewer asses the veracity of the reported income (Bastagli, 2008). Second, during the interview, the applicant is reminded of her responsibility to provide true statements under penalty of losing the right to be eligible for government programs (Gazola Hellmann, 2015). Third, the ministry conducts audits, which can be triggered by citizens’ complaints and cross-checks of registry data with other datasets such as administrative data on formal employment, deaths, or automobile purchases (Gazola Hellmann, 2015). However, despite these attempts, the large informal sector in the Brazilian economy leaves substantial scope for misreporting, which we conjecture is an important response margin to the reform.

# _3.1 Data Sources and Sample Description_

We have access to the Cadastro Unico<sup> ́</sup> household registry, which is used to determine the eligibility of households for BF as well as all other targeted federal social programs (Veras Soares, 2011). Many of these other programs have eligibility criteria above the BF thresholds which explains the large number of ineligible applicants in the registry.<sup>25</sup> These other programs do not change concurrently with the BF reform that we analyze and are discussed in more detail in Appendix B.2.

The final data set is constructed by appending eight extractions of the registry: one in December of each year from 2011 until 2015, one in April 2015, one in August 2015, and one in September 2016.<sup>26</sup> Each extraction contains the latest information for all households on the registry at the time of the extraction date. For instance, if a household updated its information in August of 2011 and September 2013, its information will appear as of August of 2011 in the 2011 and 2012 extractions and as of September 2013 in the 2013, 2014, 2015, and 2016 extractions. The reform to BF that we study occurred in June 2014. Summary statistics on household per-capita income and number of family members as of June 2014 are displayed in Table 2. Note, 24. Technically, eligible families do not automatically become BF beneficiaries. There is a quota (cap) on the number of beneficiaries per municipality. Prior to 2009, these quotas were based on the predicted number of households below the poverty threshold in each municipality. Post 2009, these quotas were based on the predicted number of households below the poverty threshold scaled by 1.18 (Gerard, Naritomi and Silva, 2021). If the number of eligible families exceeds the quota in a municipality, priority is assigned first to certain vulnerable populations (indigenous families, Quilombola families, families with children in child labor, families who collect recyclable materials, families with members free from situations similar to slave labor), second to families with lower per-capita income, and third to families with a larger number of children. Given our focus will be on households reporting below the extreme-poverty threshold post 2009, we believe that it is reasonable to assume that the vast majority of these households do in fact receive the basic benefit.

25. Moreover, the government aims to register all families with per-capita incomes below half the minimum wage (or total incomes below three times the minimum wage) (Veras Soares, 2011). The minimum wage was R$724 per-month in 2014; thus half the minimum wage was R$362, which is substantially higher than the highest BF threshold.

26. Every time the MDS analyzes the Cadastro Unico<sup> ́</sup> data, it creates one of these extractions. Therefore, the frequency of the extractions are a result of previous data analyses by the ministry. Appendix B.3 contains a figure depicting the timeline of the data extractions.

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Table 2 also presents separate statistics for single individual households (households with one adult and no children) as our main analysis will focus solely on these households (we discuss why below).

Table 2: Summary Statistics as of June, 2014

|Variables|Mean|Median|
|---|---|---|
|Per Capita Income (single individual households)|330.51<br>(324.30)|200.00|
|Per Capita Income (all households)|151.17<br>(184.97)|76.66|
|Number of Members Per Household|3.04<br>(1.46)|3.00|
|Observations (single individual households)|4,232,528||
|Observations (all households)|28,932,001||

_Note:_ This table shows summary statistics for households in the Cadastro Unico<sup> ́</sup> database as of June, 2014. Per-capita income denotes household, monthly, per-capita income and is measured in Brazilian reais. The PPP conversion from US dollars to Brazilian reais was 1.813 in 2014 (OECD, `https://data.oecd.org/conversion/purchasing-power-parities-ppp.htm` ).

# _3.2 The Transfer Schedule and the June 2014 Reform_

At the beginning of our data (December 2011), the extreme-poverty threshold was equal to R$70 percapita, per-month and the poverty threshold was equal to R$140 per-capita, per-month.<sup>27</sup> The basic benefit was equal to R$70 per-month, while the variable benefits were based on the number and ages of the children in the household (see Appendix B.4 for more information on the variable benefits). In June 2014, the government increased both the benefits and thresholds by 10%. Thus, the extreme-poverty threshold was raised from R$70 to R$77 per-capita, per-month, the poverty threshold was raised from R$140 to R$154 per-capita, per-month, the basic benefit was raised from R$70 to R$77 per-month, and the variable benefits were also increased by 10%. This reform was announced on national television by the president in April 2014.

Our main analysis will focus on single individual households. These households are not eligible for the variable benefits as they do not have children. Thus, prior to June 2014, these households received R$70 permonth if their reported income was less than or equal to R$70 per-month and 0 otherwise. After June 2014, these households received R$77 per-month if their reported income was less than or equal to R$77 per-month and 0 otherwise. Thus, the benefit schedule for these households has a single notch which increased both in level and location as a result of the June 2014 reform; see Figure 2.

27. In 2003, the extreme-poverty threshold and the poverty threshold were set to equal one-fourth and one-half of the monthly minimum wage of R$200, respectively. These thresholds have since been periodically adjusted for inflation; the time betwen adjustments is _ad hoc_ and not linked to the minimum wage. Prior to June 2014, the last readjustment was in July 2009 (Gazola Hellmann, 2015).

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Benefit, b <!-- Start of picture text --> 77<br>70 u<br>70 77<br>Reported income, ¥<br><!-- End of picture text -->
reform changed the policy from **p** = _{b, τ }_ = _{_ 70 _,_ 70 _}_ to **p**<sup>_′_</sup> = _{b_<sup>_′_</sup> _, τ_<sup>_′_</sup> _}_ = _{_ 77 _,_ 77 _}_ . Thus, we seek to calculate: where _t_<sup> ̄</sup> denotes the end of our four-year-window, i.e., _t_<sup> ̄</sup> =June 2016. We will then use the bounds on the MVPF to bound the welfare impact of the reform for June 2016.<sup>31</sup> Thus, we need to estimate the number of jumping and bunching households as of June 2016, which, in turn, requires us to estimate the ̄ ̄ number of households locating below the old and new notch under both **p** and **p**<sup>_′_</sup> at _t_<sup> ̄</sup> : _Gt_ (70; **p** ), _Gt_ (70; **p**<sup>_′_</sup> ), ̄ ̄ ̄ ̄ _Gt_ (77; **p** ), and _Gt_ (77; **p**<sup>_′_</sup> ). However, because this was a national reform, only _Gt_ (77; **p**<sup>_′_</sup> ) and _Gt_ (70; **p**<sup>_′_</sup> ) are observed directly because only policy **p**<sup>_′_</sup> was offered in period _t_<sup> ̄</sup> . Thus, our goal is to estimate the number of households reporting less than or equal to R$70 and R$77 in period _t_<sup> ̄</sup> had the reform not happened: _Gt_ ̄(77; **p** ) ̄ and _Gt_ (70; **p** ).

Ideally, we would estimate _Gt_ ̄(77; **p** ) and _Gt_ ̄(70; **p** ) using control groups from random experimental variation (e.g., from staggering the implementation of the reform randomly across geographies); however, as mentioned above, the BF reform was a national reform implemented everywhere starting June 2014. Consequently, our identification strategy will rely on using regions of the reported income distribution that _were not_ impacted by the reform to control for underlying time trends in the portions of the reported income distribution that _were_ impacted by the reform. This brings us to our two identification assumptions.

# _4.1 Identification Assumption 1_

Our identification strategy relies on first finding a region of the reported income distribution which was not impacted by the reform. In the context of the baseline model in Section 2.1, the number of single individual households reporting an income strictly below R$70 should be unchanged by the reform. The intuition for this is that anyone who has a true income below R$70 always reports truthfully both pre- and post-reform and anyone who has a true income above R$70 prefers to misreport at the threshold rather than misreport to an income level below the threshold (because misreporting costs are increasing in the distance between true and reported incomes). While in this baseline model bunching should occur precisely at R$70, in reality bunching is typically more diffuse due to small optimization errors and/or frictions (Kleven, 2016). Thus, our first identification assumption is that the number of people reporting incomes at or below R$63 is unaffected by the reform (i.e., we assume that R$63 is sufficiently far below R$70 such that there are no “bunchers” at or below R$63):

**Identification Assumption 1.** _The distribution of reported incomes below R$63 is unaffected by the reform: Gt_ ( _x_ ; **p** ) = _Gt_ ( _x_ ; **p**<sup>_′_</sup> ) _∀ x ≤_ 63 _, t._

To provide suggestive evidence that Assumption 1 is reasonable, Figure 3 plots the number of single individual households reporting in income bins of size 7 from R$0 to R$63 (with the numbers in each bin

> 31. Implicitly, we assume that agents are not making dynamic decisions (e.g., agents are myopic) so that we can apply Proposition 3 and calculate the welfare impact of the reform in a given time period. Note, there is another reform to the schedule in June 2016 so we cannot estimate the welfare impact of the reform beyond June 2016.

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<!-- Start of picture text --> wo a<br>2 Le<br>£8 De _eeeetecces te<br>& ae _ eee”<br>@ aa ae<br>oY Le » wa 4<br>= LE ee peeaeee-— ae<br>2012m2 2013m6 2014m6 2015m6 2016m8<br>Month<br>* (0,7] + (7,14]<br>° (14,21] - (21,28]<br>. (28,35] - (35,42]<br>* (42,49] + (49,56]<br>—-— (56,63]<br><!-- End of picture text -->
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indicates an average trend break of -0.038 across these bins, indicating that the number of people reporting incomes in bins _{R_ $(0 _,_ 7] _, R_ $(7 _,_ 14] _, ..., R_ $(56 _,_ 63] _}_ was, on average, approximately 3.8% lower in June, 2016 relative to polynomial trend. However, under Identification Assumption 1, any post-reform trend break for these bins must be due to underlying time variation unrelated to the reform. Loosely speaking, our second identification assumption is going to be that our two treatment bins, R$(63 _,_ 70] and R$(70 _,_ 77], would have seen the same deviation post-reform as the control bins had the reform not happened, i.e., these two bins also would have seen a 3.8% reduction in the number of people in June, 2016 (relative to their bin-specific polynomial time trends) had the reform not happened. However, as can be seen in Figure 5, the number of people reporting incomes in R$(63 _,_ 70] saw a reduction of around 13.6% (a 0.146 log-point decrease) while the number of people reporting incomes in R$(70 _,_ 77] saw an increase of 326.3% (a 1.45 log-point increase) as of June 2016. Formally, our second identification assumption is:

**Identification Assumption 2.** _In absence of the reform, the (log) number of people reporting in each bin evolves according to:_

Under Identification Assumption 2, the difference between the (log) number of households in any two 7-increment bins below R$77 is, _in absence of the reform_ , governed by a stable polynomial plus a random error term. Combining Assumptions 1 and 2, we can use our control bins (i.e., bins _≤_ R$63) to identify _h_ ( _t_ ) in the post-reform period.<sup>36</sup> In other words, we can use our control bins to identify the expected deviation from bin-specific polynomials in the post-reform period if the reform did not occur. Any deviation observed above and beyond _h_ ( _t_ ) in our two treatment bins is then attributed to the reform. This brings us to our main empirical specification: a generalized difference-in-difference specification where we allow for flexible pre-treatment dynamics between treatment and control bins: where _δt_ represents a set of month fixed-effects; _treatx_ takes value 1 if _x ∈{_ 70 _,_ 77 _}_ and 0 otherwise; and _K_ � _k_ =0<sup>_αk,xtk_capturespolynomialtimetrendsforeachbin(indexedby</sup><sup>_x_)whichpredatethereformandare</sup> assumed to persist into the post-reform period had the reform not occurred. Under our two identification assumptions, the causal impact of the reform on the (log) number of households locating in R$( _x −_ 7 _, x_ ] in month _t_ , denoted ∆log � _N_ ( _x−_ 7 _,x_ ] _,t_ �, is equal to _β_<sup>ˆ</sup> 1 _,x_ + _β_<sup>ˆ</sup> 2 _,xt_ for _x ∈{_ 70 _,_ 77 _}_ .

Before we present the results from Equation (15) in Section 5 (using various polynomial degrees _K_ ), let

> 36. We use the distribution below R$63 rather than the distribution above R$77 to control for underlying time trends because the distribution above R$77 is presumably impacted by the reform given that the jumping households would have located above R$77 in absence of the reform. However, reported incomes _sufficiently far_ above R$77 should not be impacted by the reform. The question is, how far is sufficiently far? Kleven and Waseem (2013) use an iterative procedure to determine how far above a notch is sufficiently far so that the distribution beyond this point is unaffected by the notch. Their procedure relies on equating the excess mass at and below the notch with the missing mass above the notch. However, such an exercise is not feasible in our setting due to extensive margin responses. In particular, while some of the “excess” households locating below R$77 would have located above R$77 in absence of the reform, some of them may have simply decided to not report an income and, thus, not be on the registry. Thus, we cannot equate the excess mass below R$77 with the missing mass above R$77. Consistent with our selection of control bins, Kleven (2016) notes that when extensive margin responses are strong, one should consider only using data below the notch to estimate the bunching mass.

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us discuss the statistical and economic interpretations of Identification Assumption 2. From a statistical perspective, Identification Assumption 2 is simply a generalization of the standard difference-in-difference assumption (this generalization is employed in, for example, Wolfers (2006) and is discussed more generally in Mora and Reggio (2013)).<sup>37</sup> Setting _K_ = 0 results in a standard difference-in-difference estimator in which the control groups and treatment groups are assumed to have “parallel trends” pre-reform that would have persisted in the post-reform period had the reform not occurred. The standard difference-in-difference strategy therefore assumes that the difference between the treatment and control groups follow a 0<sup>_th_</sup> order polynomial in absence of the reform (i.e., that they differ by a constant). Larger values of _K_ require progressively weaker parallel assumptions. For instance, setting _K_ = 1 requires the “parallel growths” assumption which asserts that the growth rates in the treatment and control groups over time are the same (i.e., that second and higher differences between treatment and control groups are constant over time).<sup>38</sup> Setting _K_ = 2 leads to the “parallel accelerations” assumption which asserts that the acceleration rates in the treatment and control groups over time are the same (i.e., third and higher differences between treatment and control groups are constant over time). Setting _K >_ 2 results in what Mora and Reggio (2013) refer to as the “parallel- _K_ ” assumption which asserts that the _K_ + 1 and higher differences between the treatment and control groups are constant over time.

But what is the economic meaning of Identification Assumption 2? Fundamentally, there are complex structural relationships between the number of people reporting in each income bin; these relationships are determined by how the true income distribution is evolving over time, how the true income distribution is mapped to the reported income distribution, as well as growth of the BF registry over time. By making Identification Assumption 2, we are essentially assuming that the differences over time between the number of people reporting in each income bin (which are determined by unknown structural relationships) are well approximated by polynomials which would have persisted in absence of the reform. Identification Assumption 2 is not fully testable in the same way that the standard differences-in-differences assumption (that parallel pre-trends persist post treatment) is not fully testable. However, as in the case of the standard “parallel trends” assumption, we can gauge whether Identification Assumption 2 seems sensible by looking at prereform data. Identification Assumption 2 implies that the difference between the log number of households in any two 7-increment bins below R$77 is governed by a stable polynomial in absence of the reform. Appendix C.4 shows how the differences log � _N_ (70 _,_ 77]� _−_ log � _N_ ( _x−_ 7 _,x_ ]� and log � _N_ (63 _,_ 70]� _−_ log � _N_ ( _x−_ 7 _,x_ ]� evolved in the pre-reform period for _x ∈{_ 7 _,_ 14 _, ...,_ 63 _}_ . These differences follow stable, low order polynomial relationships in the pre-period. While this of course does not imply that these relationships would have persisted into the post-reform period (just as parallel pre-trends do not imply that the trends would continue on a parallel path post treatment), it is at least suggestive that stable relationships exists between the various income bins.

However, because we have several control bins, we can _partially_ test the validity of our two identification assumptions. In particular, under Identification Assumption 1, our control bins should be unaffected by the reform. Thus, in the post-reform period, we can test whether the number of households locating in each of our control bins can be accurately predicted by our other control bins using Identification Assumption 2. Thus, at the end of Section 5, we run a number of placebo tests, suggesting that our two identification assumptions are reasonable.

> 37. Equation (2) in Wolfers (2006) uses an analogous generalized difference-in-difference accounting for differential quadratic pre-trends. Our Equation (15) is a combination of Equation (17) and Equation (20) from Mora and Reggio (2013). 38. A number of papers discuss the extended version of differences-in-differences under the “parallel growths” assumption (e.g., Mora and Reggio (2013), Rambachan and Roth (2020), and Bilinski and Hatfield (2019)).

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## _4.3 Could We Use a Bunching Estimator to Bound the MVPF?_

Our empirical strategy amounts to estimating the reduction in the mass of households bunching at the old notch and the increase in the mass of households bunching at the new notch as a result of the reform using a difference-in-difference strategy. But one may wonder whether we could have used standard bunching techniques (developed in Kleven and Waseem (2013) and Saez (2010)) to back out the changes in these masses. Of course, even using standard bunching techniques, one must account for time variation, i.e., one must estimate how many people would have bunched at the old notch and at the new notch in the post-reform period had the reform not occurred. As an example of how one might use standard bunching techniques while also controlling for time variation, one could first use these techniques to back out the counterfactual reported income distributions that would result if there were no notches in both the pre- and post-reform period (e.g., in June 2014 and June 2016). To do so, one would use the observed reported income distributions in the pre- and post-reform periods and make the following two assumptions (which are standard in the bunching literature): (a) the reported income distribution would be smooth in absence of the notch, and (b) the reported income distribution sufficiently far away from the notch is unaffected by the notch. One could then assume that the relationship that exists between the counterfactual and the observed reported income distributions in the pre-reform period would have stayed the same in the post-reform period in absence of the reform. This assumption combined with the estimated counterfactual reported income distribution in the post-reform period would then allow one to calculate the reported income distribution in the post-reform period had the reform not happened. A similar strategy is employed in Carril (2022). However, this strategy is unlikely to be feasible in our setting. As seen in Figure 17 in Appendix C.3, the reported income distribution in Brazil is _extremely_ non-smooth. For instance, in June 2014, in addition to substantial bunching at the notch of R$70, there is extreme bunching at numbers equal to 0 mod 50, less severe bunching at numbers equal to 0 mod 10, and substantial bunching at R$60. R$60 was a previous BF eligibility threshold (the notch of R$60 was implemented in 2006 while the notch of R$70 was implemented in 2009; see Gazola Hellmann (2015)). While bunching estimators have been augmented to deal with “round-number” bunching and other “reference-point” bunching (e.g., Kleven and Waseem (2013) and Best and Kleven (2017)), we believe that the pervasiveness and the variability of round-number and reference-point bunching in our setting will make it too difficult to precisely identify the counterfactual distributions around our notches (in particular, around the original notch of R$70 which is equal to 0 mod 10). Thus, our empirical strategy highlights an alternative way to estimate changes in bunching when smoothness assumptions cannot be used to estimate counterfactual distributions.

# 5 Results

In this Section, we present results from our generalized difference-in-difference specification, Equation (15), and, in turn, calculate bounds on the MVPF. Based on these bounds, we then discuss the welfare implications of the reform. Next, we show robustness of our results to a variety of factors: we show robustness to Identification Assumption 1 by allowing the number of households between R$(56 _,_ 63] to also be impacted by the reform; we show robustness to a more general version of Identification Assumption 2; and, we show robustness of our results to household composition. Finally, we conduct a placebo exercise which partially tests the validity of our two identification assumptions.

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not happened, while 22,000 would have located above the new notch had the reform had not happened (i.e., 22,000 households jump into the program as a result of the reform).<sup>40</sup> We repeat this exercise under the alternative assumptions that the differences in the (log) numbers in any two bins follow quadratic, quartic, or quintic polynomials over time, i.e., we re-estimate Equation (15) for _K_ = 2 _,_ 4 _,_ 5.<sup>41</sup> Figures of the counterfactual paths for our two treatment bins under these alternative assumptions are shown in Appendix C.2. Table 3 presents the estimated impact of the reform on the numbers locating in R$(63,70] and R$(70,77], ∆ _N_ (63 _,_ 70] _,t_ and ∆ _N_ (70 _,_ 77] _,t_ , along with the estimated number of bunching ̄ ̄ households _Bt_ , estimated number of jumping households _Jt_ , and lower and upper bounds on the MVPF in June 2016. All of these quantities are stable across different values of _K_ . Under our preferred specification ( _K_ = 3), we find a lower bound for the MVPF of the reform around 0.9 and an upper bound of around 1.12.

Table 3: Impacts of Reform and MVPF Bounds in June 2016 Estimated from Equation (15)

||(1)|(2)|(3)|(4)|(5)|(6)|
|---|---|---|---|---|---|---|
|Polynomial Degree, _K_|∆_N_(63_,_70]_,_ ̄_t_|∆_N_(70_,_77]_,_ ̄_t_|_B_ ̄_t_|_J_ ̄_t_|_MV PFL,_ ̄_t_|_MV PFU,_ ̄_t_|
|Quadratic, _K_ = 2|-26,279|51,759|26,279|25,480|0.88|1.11|
||(6_,_163)|(2_,_160)|(6_,_163)|(6_,_659)|(0_._03)|(0_._03)|
|Cubic, _K_ = 3|-27,452|49,247|27,452|21,794|0.90|1.12|
||( 4,357)|(234)|(4_,_357)|(4_,_592)|(0_._02)|(0_._02)|
|Quartic, _K_ = 4|-29,338|50,873|29,338|21,535|0.90|1.13|
||( 6,257)|(1_,_345)|(6_,_257)|(6_,_503)|(0_._03)|(0_._03)|
|Quintic, _K_ = 5|-29,240|50,559|29,240|21,318|0.90|1.13|
||( 5,912)|( 1,184)|( 5,912)|( 6,141)|( 0.03)|( 0.03)|

_Note:_ Columns (1) and (2) show the estimated impacts of the reform on the number of single individual households reporting incomes in bins R$(63,70] and R$(70,77] for June 2016: ∆ _N_ (63 _,_ 70] _,t_ ̄ and ∆ _N_ (70 _,_ 77] _,t_ ̄. Estimates are calculated using Equation (15) with various polynomial degrees _K ∈{_ 2 _,_ 3 _,_ 4 _,_ 5 _}_ . Columns (3) and (4) show the estimated number of bunching and jumping households for June 2016, _Bt_ ̄ and _Jt_ ̄, calculated using Equations (12) and (13). Columns (5) and (6) show the estimated upper and lower bounds for the MVPF for June 2016, calculated using Equations (10) and (11). Standard errors are presented in parentheses and are computed from the delta method from the clustered standard errors estimated in Equation (15).

# _5.2 Discussion_

Our lower bound on the MVPF of the June 2014 BF reform is approximately 0.90 whereas our upper bound on the MVPF is approximately 1.12. This implies that the WTP for the reform relative to the budgetary cost is between 0.90 and 1.12. Notably, these bounds are somewhat tightly centered around 1. This is because the number of mechanical households (households locating below 70 both with and without the reform) is much larger than the number of bunching or jumping households. In particular, for June 2016, we estimate there to be around 1.88 million mechanical households compared to 22,000 jumping households and 27,000 bunching households.

What can we say about the welfare implications of an MVPF between 0.90 and 1.12? We can be sure 40. One may then wonder whether we estimate a reduction of 22,000 households locating above R$77 as a result of the reform. To investigate this, we can include income bins above R$77 in Equation (15) as additional _treatment_ bins. Cumulatively, we estimate that income bins between R$77 and R$147 saw a decline of around 14,300 households when setting _K_ = 3 (with a standard error of around 6800). However, as mentioned in footnote 36, the set of jumping households consists of both households who would have located above R$77 in absence of the reform _and_ households who would not have reported an income to the registry at all in absence of the reform (i.e., new entrants). Because of these new entrants, it is not surprising that we estimate the number of jumping households as exceeding the reduction in households reporting above R$77.

41. Our results are also robust to estimating Equation (15) with more granular income bins, see Appendix C.5.

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that the reform was welfare improving as long as the government values giving R$0.90 to BF households in a non-distortionary manner more than spending R$1 on their next best alternative. On the other hand, the reform was welfare decreasing if the government values spending R$1 on their next best alternative more than giving R$1.12 to BF households in a non-distortionary manner.<sup>42</sup> But what is the government’s best alternative use of funds? In general, this is a difficult question to answer. Lindert et al. (2007) show that BF performs better (in terms of targeting performance) than other anti-poverty programs in both Brazil and other countries in Latin America; this suggests that there is not a better alternative anti-poverty program that the government could finance. Instead, for expositional simplicity we assume that the next best use of funds is a non-distortionary UBI. Under this assumption, we can perform a conservative back-of-the-envelope calculation to argue that the 2014 BF reform was almost certainly welfare improving. Suppose the government is utilitarian and that the true income distribution is log-normal with parameters taken from the World Bank’s PovcalNet database for Brazil in 2016.<sup>43</sup> Conservatively, we assume that the BF household per-capita income distribution matches the distribution for the bottom 50% of income earners in Brazil.<sup>44</sup> Moreover, we assume utility of consumption is CRRA: _u_ ( _c_ ) = _c_<sup>1</sup><sup>_−γ_</sup> _/_ (1 _− γ_ ). Based on these assumptions, the government prefers giving R$0.90 (in a non-distortionary manner) to BF households more than spending R$1 on a non-distortionary UBI as long as _γ >_ 0 _._ 14. While estimates for _γ_ vary widely, typically estimates fall between 1 and 10 (Outreville, 2014). Alternatively, if _γ_ = 1 (i.e., _u_ ( _c_ ) = log( _c_ )), giving R$0.90 (in a non-distortionary manner) to BF households yields equivalent welfare gains to spending R$1.50 on a non-distortionary UBI. Thus, if the next best alternative policy is a non-distortionary UBI and the government is utilitarian, the BF reform was almost certainly welfare improving. This finding contributes to the debate around targeted vs. universal transfers in developing settings (Hanna and Olken, 2018): we find that even in a setting with a highly pronounced notch and substantial scope for misreporting, the efficiency cost generated by behavioral responses is simply not large enough to outweigh the equity gain associated with increased benefit generosity targeted to poor households (relative to a universal transfer).

Finally, when calculating our bounds for the MVPF, we have ignored any potential fiscal externalities when determining the total cost of the reform (i.e., we have ignored the impact that behavioral responses have on other components of the government budget). There is evidence to suggest that some beneficiaries partially substitute formal sector employment for informal sector employment to become eligible for the BF benefit (as informal income is less easily verified making misreporting less costly; see De Brauw et al. (2015)). While it is easier to evade taxes in the informal sector, it is unlikely that this behavioral response will affect tax revenues as BF beneficiaries are almost certainly sufficiently poor so as to be exempt from income 42. Technically, the reform is welfare improving as long as the government values spending R$1 on their next best alternative less than splitting R$0.90 (in a non-distortionary manner) among the mechanical, threshold, bunching, and jumping households, where the split is determined by the lower bounds on each group’s WTP for the reform. Similarly, the reform is welfare decreasing if the government values spending R$1 on their next best alternative more than splitting R$1.12 (in a non-distortionary manner) among the mechanical, threshold, bunching, and jumping households, where the split is determined by the upper bounds on each group’s WTP for the reform.

43. In 2016, the mean per-capita income in Brazil was R$615.32 and the Gini coefficient was 0.533; these parameters fully pin down the income distribution if we assume log-normality.

44. Bastagli (2008) finds that of all transfers paid in 2004, 91% went to households in the bottom 50% of the income distribution. Alternatively, Lindert et al. (2007) suggests even better targeting performance, finding that 94% of all benefits go to the bottom 40%. Notably, transfers are not evenly distributed across the bottom 50% of households: the poorest households within this group receive more (e.g., Bastagli (2008) finds that the bottom 20% of the income distribution receive 50% of BF transfers, while Lindert et al. (2007) report that the bottom 20% receive 73% of BF transfers). Thus, we believe the assumption that the income distribution of BF households is the same as the income distribution for the bottom 50% of income earners in Brazil is highly conservative.

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taxation.<sup>45</sup> However, there is evidence showing that increased BF transfers lead to an increase in formal sector employment of non-beneficiaries, which leads to higher GDP and tax revenue (Gerard, Naritomi and Silva, 2021). If this positive fiscal externality exists for the June 2014 reform, this would lower our estimate for the total cost of the reform, thus raising our estimates for both the lower and upper bound of the MVPF (see footnote 23). Thus, incorporating this positive fiscal externality would only reinforce our finding that the 2014 BF reform was welfare improving relative to a non-distortionary UBI.

# _5.3 Robustness to Identification Assumption 1_

Identification Assumption 1 may not hold if optimization frictions are large. For example, consider households who, in response to the reform, jump below the threshold by changing their labor supply but face large labor market frictions. These households may not be able to perfectly jump and bunch at the new notch, but may instead jump to an income level below R$63. Alternatively, under the original policy, some households may wish to bunch at R$70, but are only able to locate at an income below R$63 due to labor market frictions; if these households are able to update their income to an income between R$(70,77], they may move to the new notch as a result of the reform. Hence, large labor market frictions may imply that the distribution below R$63 is impacted by the reform. To test for this possibility (or equivalently, to allow for larger frictions), we relax Identification Assumption 1 by instead assuming that the number of people reporting in bins _≤_ R$56 are unaffected by the reform, allowing for the possibility that the number reporting in bin R$(56 _,_ 63] is affected by the reform. We augment Equation (15) by setting _treatx_ = 1 if _x ∈{_ 63 _,_ 70 _,_ 77 _}_ and 0 otherwise, i.e., we include R$(56 _,_ 63] as a treatment bin. Figure 7 plots the actual and counterfactual paths for log � _N_ (56 _,_ 63] _,t_ � _,_ log � _N_ (63 _,_ 70] _,t_ �, and log � _N_ (70 _,_ 77] _,t_ �. It does not appear that the reform had a significant impact on the number reporting in R$(56 _,_ 63] and the impact of the reform on our two original treatment bins is robust to including R$(56,63] as a treatment bin. Using this relaxation of Identification Assumption 1, we find that the MVPF is bounded between 0.82 and 1.07 (see Table 7 in Appendix C.6).

# _5.4 Robustness to Identification Assumption 2_

Identification Assumption 2 essentially boils down to assuming that the differences over time between the (log) number of people reporting in each income bin (which are determined by unknown, complex structural relationships) are well approximated by polynomials which would have persisted in absence of the reform. Identification Assumption 2 therefore implies that if, for example, bin R$(35,42] experiences a 1% deviation from its bin-specific polynomial trend, bin R$(63,70] would also experience a 1% deviation from its bin-specific polynomial trend in absence of the reform. However, one may argue that, for example, a structural change in the economy which leads to a 1% deviation from the bin-specific polynomial time trend for bin R$(35,42] would lead to a 2% deviation for bin R$(63,70]. As such, we relax Identification Assumption 2 to instead assume that the log number reporting in each bin evolves according to: 45. For example, in 2015, individuals earning less than R$1903.98 per-month were exempt from income taxation.

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as benefits are paid out per-household as opposed to per-capita.<sup>47</sup> Hence, the reform may have increased incentives to misreport family composition as well as income.<sup>48</sup> From a theory perspective, Proposition 3 holds even if misreporting responses occur on the family composition margin. However, such a behavioral response may affect the validity of our identification strategy (for example, it may no longer be reasonable to assume that the distribution below R$63 is unaffected by the reform if these new “single individual” households enter at income levels well below the threshold). Thus, we re-do our main analysis restricting to single individual households whose composition does not vary over the sample period. Our point estimates for the lower bound for the MVPF still lie between 0.88 and 0.91, while our point estimates for the upper bound are now smaller lying between 1.01 and 1.05; see Appendix C.8.

Finally, our main analysis is restricted to single individual households due to the fact that the schedule for households with more than one individual features a notch at R$70 and a kink below R$70 (e.g., this kink is at R$35 for two adult households with no children; see Section 3). Consequently, the 2014 BF reform led to both a change in the notch _and_ a change in the kink for households with more than one individual. Thus, for these households, it is not necessarily reasonable to make Identification Assumption 1 as we might expect the reform to affect the number of people reporting in bins around the kink. We nonetheless proceed with estimating the bounds on the MVPF for two adult households without children, noting that our identification assumptions are imperfect in this setting. For these households we see the same pattern of behavioral responses to the reform and estimate lower bounds for the MVPF between 0.88 and 0.96 and upper bounds for the MVPF between 1.08 and 1.12; see Appendix C.9.<sup>49</sup>

# _5.6 Placebo Tests_

We can _partially_ test the validity of our two identification assumptions via placebo tests. Together, Identification Assumptions 1 and 2 imply that all of the income bins below R$63 should evolve approximately according to a common time trend plus a bin-specific polynomial throughout the entire analysis period. To test this, we re-estimate Equation (15) but only include bins below R$63 (i.e., _x ∈{_ 7 _,_ 14 _, ...,_ 63 _}_ ) and randomly assign some of these bins to be “treatment” bins (i.e., _treatx_ = 1). If both of our identification assumptions are correct, the “treatment effects” from these placebo regressions should be close to zero, i.e., the post-reform deviation of the “treated” bins relative to the post-reform deviation of the “control” bins should be close to 0. There are a total of 510 different ways to assign our nine bins below R$63 “treatment” status.<sup>50</sup> Figure 8 plots the results from all 510 such regressions, showing the estimated “treatment effects” in June 2016: _β_<sup>ˆ</sup> 1 _,x_ + _β_<sup>ˆ</sup> 2 _,xt_<sup> ̄</sup> for _x ∈{_ 7 _, ..,_ 63 _}_ , where _t_<sup> ̄</sup> represents June 2016. Each bin gets assigned _treatx_ = 1 255 47. E.g., a household with two adults and no children that has a combined per-capita income of R$60 is eligible for R$70 in transfers pre-reform and R$77 in transfers post-reform. However, if this household were to report that they were actually two single individual households with incomes of R$60, they would _each_ be eligible for R$70 in transfers pre-reform and R$77 in transfers post-reform.

48. However, the ability of households to misreport the number of members is limited as individuals must provide government issued IDs for all family members to be on the registry. Moreover, household composition is arguably more verifiable than income for many households given the large informal sector in Brazil. Thus, we suspect that households are more likely to misreport income than family composition.

49. In Appendix C.10, we show strong suggestive evidence of a behavioral response to the change in the basic benefit notch for households with children, but we do not attempt to bound the MVPF for these households. This is because households with children may also receive the “variable benefit”. Both the level and location of the notch associated with the variable benefit also changed with the June 2014 reform. Thus, the WTP of households with children needs to account for changes in the variable benefit schedule in addition to changes in the basic benefit schedule. This exercise is beyond the scope of the current paper.

50. There are �91� ways to pick one “treatment” bin, �92� ways to pick two “treatment” bins; thus, there are a total of<sup>�8</sup> _i_ =1�9 _i_ �= 510 possible regressions.

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6 Conclusion This paper proposes a theoretical framework and empirical strategy to gauge the welfare impacts of reforms that change notches in transfer schedules. We show that we can use two empirically observable objects to bound the MVPF of the reform: the number of households who jump down to the new notch and the number of households bunching at the old notch who move toward the new notch. These bounds on the MVPF can then be used to construct bounds for the welfare impact of changing the notch. We estimate bounds for the MVPF of a reform to the Bolsa Fam ́ılia program that changed the structure of the notch, finding a lower bound of 0.9 and an upper bound of 1.12. Back-of-the-envelope calculations suggest that this reform was likely welfare improving.

More broadly, we believe that this paper highlights a new manner in which reduced-form evidence on jumping and bunching can be used to inform policy. Given the ubiquity of notches, we hope that the methods developed in this paper will be useful for analyzing reforms in a variety other contexts such Medicaid, incomedependent tax credits, or firm tax schedules. Finally, the bounding techniques developed in this paper may be helpful for bounding welfare impacts of large reforms which do not necessarily feature notches.

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