Casting the Tax Net Wider: Experimental Evidence from Costa Rica

The majority of firms in developing countries are informal, and encouraging them to register with the tax authority has proven challenging and costly. This paper argues that incomplete tax filing among registered firms constitutes an important intermediate form of informality, which can be tackled with much higher cost-effectiveness. Using a nationwide randomized experiment in Costa Rica, The paper shows that credible enforcement emails tripled the income tax filing rate and doubled the payment rate among previously non-filing firms. The treatment effect was even higher when the email listed examples of third-party reports of a firm's transactions, with the return on an email reaching US$ 19. It also shows that the intervention had no negative spillovers on other tax compliance dimensions, the treatment effects persisted in the medium term, and treated firms became more likely to file information reports about their suppliers or clients, thereby increasing the tax authorities' information set for future tax enforcement.


Policy Research Working Paper 7850
This paper is a product of the Macroeconomics and Fiscal Management Global Practice Group. 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://econ.worldbank.org. The authors may be contacted at abrockmeyer@worldbank.org.
The majority of firms in developing countries are informal, and encouraging them to register with the tax authority has proven challenging and costly. This paper argues that incomplete tax filing among registered firms constitutes an important intermediate form of informality, which can be tackled with much higher cost-effectiveness. Using a nationwide randomized experiment in Costa Rica, The paper shows that credible enforcement emails tripled the income tax filing rate and doubled the payment rate among previously non-filing firms. The treatment effect was even higher when the email listed examples of third-party reports of a firm's transactions, with the return on an email reaching US$ 19. It also shows that the intervention had no negative spillovers on other tax compliance dimensions, the treatment effects persisted in the medium term, and treated firms became more likely to file information reports about their suppliers or clients, thereby increasing the tax authorities' information set for future tax enforcement.
1 Introduction of rms for which no third-party information was available, the emails either did not mention thirdparty information at all (treatment 1), or mentioned the general use of these information by the tax authority (treatment 2), without making a statement about the (non-)availability of information for the taxpayer in question. In the sample of rms for which third-party information was available, the emails either mentioned the existence of third-party information about the taxpayer in question (treatment 1), or provided specic examples of the taxpayer's third-party reported sales, such as the name of a client rm and the reported purchase amount (treatment 2). Unlike Carrillo, Pomeranz, and Singhal (2016), we use examples rather than the total amount of third-party reported sales in the message, as the amounts are small for many taxpayers, and it is possible that rms over-estimate the total amount of third-party reports, in which case providing examples rather than specic amounts might lead to larger compliance gains. The experiment design allows us to test whether the existence of third-party information increases rms' response to a baseline deterrence message and whether leveraging third-party information can further strengthen the message.
We analyze the impact of the intervention using rich administrative data on multiple taxes and ling obligations of rms, and nd three sets of results. First, the emails sent to non-lers tripled their rate of income tax ling and more than doubled the rate and amount of payment, relative to the control group that received no message. Among rms covered by third-party information, listing specic examples of third-party information about the rm had an additional positive eect on all outcomes, and signicantly increased the rate of ling by two percentage points (p.p.). The ling rate reached 34% among rms covered by third-party information and 19% among rms not covered by third-party information. While the proportional treatment eect is larger in the latter group, the absolute eect on payment is an order of magnitude larger in the former group. The return on the (strongest) email is US$ 19 for rms with third-party information and US$ 0.39 for rms without third-party information. 10 Second, we advance the understanding of compliance spillover eects by examining whether the treatment had an impact on a wide variety of compliance outcomes that were not specically targeted by the intervention. The possibility of negative spillovers on other compliance margins is indeed a key concern for compliance interventions. In our experiment, we nd no negative impact on compliance with sales tax ling or payment, and a signicant but small increase in the deregistration rate by 1-2 p.p., though this latter result applies only to rms with extremely small reported tax 10 Figures in US dollars are calculated using an exchange rate of 545 Costa Rican colones (CRC) per U.S. dollar. 4 liabilities. Instead, we nd that the intervention increased the rate of income tax ling and payment, both in the scal years prior to the interventionmeaning that treated taxpayers were more likely to catch up with previous outstanding obligationsand also in the year following the intervention.
The persistence of the treatment eect one year later without any further communication suggests that the intervention did not just act as a reminder or nudge, but led taxpayers to update their belief about enforcement. In addition, we nd that the emails, and particularly those mentioning specic examples of third-party information, induced a higher share of rms to le an informative declaration, reporting transactions with clients and suppliers, an eect that also persists in the year following the intervention. This means the intervention increased the tax authority's information set for future tax enforcement.
Third, in an eort to provide guidance for targeting future communication interventions, we analyze heterogeneity in the main treatment eect on tax ling and payment. We nd that the impact on ling is driven by smaller rms and the self-employed, and the impact on payment is driven by larger rms, particularly corporations. This can be explained by the presence of an exemption threshold in the tax schedule for the self-employed, but not for corporations. We also nd that rms with a better past compliance record respond more strongly to the treatment. Finally, we provide some evidence suggesting that the treatment mentioning specic examples of third-party information generates an improvement in taxpayers' reporting behavior conditional on ling, leading rms to declare higher sales without fully osetting this eect through a cost increase.
Given an overall cost-benet ratio of about 1:5, we conclude that the email intervention is a costeective and sustainable way to cast the tax net wider, by not only increasing present compliance but also past and future compliance among targeted taxpayers, as well as broadening the tax authority's information set for future tax enforcement. Targeting the intervention at rms covered by third-party information, particularly corporations, and those with a better past compliance record can further increase cost-eectiveness.
This paper contributes to three strands of literature. First, we contribute to the literature on taxation and development, as reviewed in Besley and Persson (2013), that analyzed how tax capacity grows along the development path and which interventions are best suited to accelerate this process. While most recent contributions in this literature have focused on misreporting on the intensive margin (Best et al. 2015;Pomeranz 2015;Naritomi 2015, Carrillo, Pomeranz, and Singhal 2016), our study highlights the importance of compliance gaps on the extensive margin, and the cost-eectiveness of simple interventions to reduce these compliance gaps. In this sense, our study is a complement to Brockmeyer and Hernandez (2016) who conduct a systematic anatomy of compliance in Costa Rica, uncovering substantial compliance gaps on the extensive margin. The role of third-party information in enhancing tax compliance has featured prominently in the literature (Kleven et al. 2011;Kleven, Kreiner, and Saez 2015). Third-party reporting has been shown to enhance tax compliance at the intensive margin for the value-added tax (Pomeranz 2015;Naritomi 2015), but was also found to generate evasion shifting to the cost margin, when applied to income taxation (Carrillo, Pomeranz, andSinghal 2016, Slemrod et al. 2015). Our study focuses on the role of third-party reporting in enhancing compliance on the extensive margin, showing that information is both a tool for strengthening deterrence interventions and a by-product of better ling compliance.
Second, this experiment adds to other communication experiments to increase tax compliance, as reviewed in Dwenger et al. (2016) and Hallsworth (2014). Our study uses a cost eective delivery method -emails -and maximizes message impact by combining dierent message elements that have proven successful in other contexts. As expected, the observed treatment eect of our emails is substantially larger than treatment eects in most other studies. Besides, our study is one of few in this literature to focus on rms, including corporations, as opposed to individual taxpayers, and the rst with Kettle et al. (2016) to focus on tax ling. 11 Indeed, most studies in this literature have focused on correct reporting of liabilities or on the payment of already assessed liabilities, such as property tax liabilities. Furthermore, we extend the literature by using rich administrative data to measure a variety of outcomes. Contrary to compliance crowd-out, we nd positive impacts on compliance in prior tax periods, ling of informative declarations, and a persistence of the main treatment eects in the medium term.
Finally, this paper contributes to the literature on rm formalization, as reviewed in Bruhn and McKenzie (2014) and De Andrade, Bruhn, and McKenzie (2014). This literature found that providing information, reducing registration costs or simplifying regulation is relatively ineective in encouraging rms to formalize. Only enforcement, e.g. in the form of inspection visits, or payment of about one month of prots were found to signicantly increase registration rates. We suggest that encouraging regular tax ling among rms that are tax-registered but do not le (regularly) is a more cost-eective way of casting the tax net wider. As non-lers are rms that have chosen to 11 Hallsworth (2014) refers to three other papers considering ling behavior, but all are focused on individual taxpayers. 6 register for taxes, their perceived benet from compliance (tax ling), likely exceeds that of fully informal rms that chose not to register. In addition, the tax authority already has the contact information and in some cases also third-party reports about the business activities of these rms, which can be leveraged to estimate outstanding tax liabilities and contact non-lers. In general, we extend this literature by considering an empirically important intermediate form of informality which has so far received little attention.
The rest of this paper is organized as follows. Section 2 describes the tax system and the mechanisms of third-party reporting in Costa Rica, and the data we use. Section 3 presents the experimental design. We discuss the results of the experiment in Section 4. Section 5 concludes.
2 Context and Data

Income and Sales Tax
Total tax revenues in Costa Rica represented 13.5% of GDP in 2014 (Oviedo et al. 2015). Sales tax revenues constitute the largest share (36%) of total revenues, followed by income tax revenues from corporations (16%) and income tax revenues from wage earners and self-employed individuals (10%) (CR Ministry of Finance 2015).

12
All rms in Costa Rica are subject to the income tax, and a subset of rms is subject to the sales tax. The income tax schedule depends on whether a rm is registered as a corporation or as an unincorporated rm, i.e. a self-employed individual. There are no size requirements for either rm type. Corporations face an average tax rate on prots of 10, 20 or 30%, depending on their revenue level. The self-employed face a marginal tax rate on prots between 0 and 25%, depending on their prot level. The self-employed thus have lower tax rates on average, and the self-employed below the exemption threshold can le an income tax declaration without incurring a liability. The vast majority of rms is required to le the income tax declaration by December 15 for the previous scal year (October 1 to September 30). A few large rms use the calendar year as scal year and le the annual declaration by March 15. Firms have to make three quarterly advance tax payments for the annual income tax if their previous year's liability or their average liability over the last 12 Costa Rica's aggregate statistics do not distinguish between wage earners and un-incorporated rms, which are listed together as personas físicas. Our analysis focuses on rms. 7 three years is non-zero, with the maximum of these two amounts determining the level of advance payments.
Firms selling manufactured goods and certain service businesses, such as hotels and restaurants, are also liable for the monthly sales tax. The sales tax is eectively a VAT, with a recrediting mechanism for taxed inputs, but has a relatively narrow base that excludes most services (see Brockmeyer and Hernandez (2016) for details). Approximately 20% of income tax-liable rms are liable for the sales tax.
Instead of paying the regular income tax (and, where applicable, the sales tax), retailers in certain sectors and below certain size thresholds (i.e., those with annual purchases below 150 base salaries, net assets below 350 base salaries, or with less than six employees) can opt into a simplied regime. Under the simplied regime, a tax is levied on inputs at sector-specic rates that vary from 3% to 9.8%. Firms in this regime declare on a quarterly basis, and can claim credit for withholding by state institutions for the income tax, but not for withholding by credit card institutions for the sales tax. During the period we study, approximately 30,000 rms led their taxes under the simplied regime, while 360,000 rms led their income taxes under the regular regime. Firms can opt into or out of the simplied regime by submitting a D140 modication form, or deregister completely by submitting a D141 deregistration form. Figure 1 shows the percentage of tax-registered rms that did not le a tax declaration in 2014 by rm and tax type. For the income tax, this share was 19% of corporations and 25% of the self-employed.
13 It is lower but still substantial for the sales tax19% for corporations and 14% for the self-employed. This proportion has been stable over the last ve years, and is based on a tax register that is updated on a regular basis. However, it is possible that the tax register contains inactive rms whose owners decided not to deregister, as deregistration requires a personal visit to the tax oce and the payment of any outstanding tax obligations. Even among rms covered by third-party information, i.e., shown to be economically active, 12% did not le their income tax for the 2014 tax year.
13 The corresponding gures in Brockmeyer and Hernandez (2016) are comparable, albeit lower, as they use an algorithm based on tax declarations and registration/deregistration records to construct snapshots of the tax register at dierent points in time, but do not directly observe the tax register. The gures in this paper are the authority's own estimates based on all available data. 8

Third-Party Information
To enforce taxes, the Costa Rican tax authority makes use of third-party information from dierent sources. The relevant informative declarations, submitted by public or private sector agents about the economic activities of tax-liable rms and individuals, are explained below. An informant submits one informative declaration for each customer or provider, specifying their tax identication number, the transaction amount, the tax withheld (if applicable), and the income or transaction type (in general categories). Taxpayers are not provided with the informative declarations at the time they le their tax declaration, and they are not notied about the existence of an informative record. Given the structure of reporting requirements, rms should be aware of the existence of third-party reports about them, but rms with unsophisticated accounting systems might not be able to accurately estimate the amount of third-party reports.
14 Firms have to report transactions with clients and suppliers (form D151) if the accumulated annual amount of transactions with a single transaction partner reaches CRC 2.5 million.
The payment of rent, commissions, professional service fees, or interests must be reported if the annual transaction amount with a single transaction partner reaches CRC 50,000. These transactions must be reported by both the seller and the purchaser. 15 As compliance with this reporting requirement is considered to be incomplete, a rm may not know whether it has been reported by a client or supplier.
State institutions report all purchases from private rms (form D150). They also withhold tax at a rate of 2%, which is remitted to the tax authority as an advance payment on the income tax. 16 State institutions are considered to be highly compliant with their reporting obligation, so that a rm selling to a state entity can be relatively certain that the transaction will be reported to the tax authority.
Credit or debit card companies report all card sales by aliated businesses (form D153).
14 In the case that a taxpayer inquires about the information held about her economic activities, the tax authority is legally obligated to provide the information.
15 Similar to the D151 informative declaration, form D158 must be led by the organizers of agricultural auctions, and the declaration covers all sales and purchases at the auction. As this declaration covers very few taxpayers, we do not include it in our analysis.
16 The D150 informative declaration is also led by a small number of rms purchasing certain specied services (e.g. transport, communications) from non-resident rms. Firms in this case withhold tax at a rate of 3% on the specied purchases. However, less than 1% of rms in the full sample of income tax returns are aected by this scheme, which we thus do not take into account in our analysis. 9 They also withhold tax at a rm-specic rate between 0% and 6%.
17 The withheld amount is remitted to the tax authority as advance payment on the sales tax. Card companies are also considered to be highly compliant with their reporting obligation, so that a rm can be relatively certain that its card-machine sales will be reported to the tax authority.
The ling deadline for third-party reports by rms and state institutions is the same as the ling deadline for the income tax, December 15. Credit and debit card reports are led monthly. The tax authority uses all informative declarations, combined with customs declarations on imports and exports, to automatically cross-check all income tax returns. Taxpayers with strong discrepancies between third-party information and the self-assessed tax declaration, and/or meeting other criteria 18 , are selected for partial audits or full audits.
Third-party reports, combined with the list of tax registered rms, are also used to identify nonlers, i.e. rms that have not complied with their ling obligations, for the income tax, the sales tax or third-party reports (reporting transactions with suppliers or clients). The tax authority uses dierent communication interventions, variably relying on emails, phone calls, or personal visits, to follow up with non-lers. However, given human resource constraints, the non-ler campaigns do not systematically cover all non-lers and all ling obligations each year.

Data
The data set used in this paper includes the anonymized income and sales tax returns for 2013-2015 for rms ling in Costa Rica, both corporations and self-employed. This amounts to about 360,000 income tax returns per year and 68,000 sales tax returns per month. The data allows us to measure compliance prior to the experiment (2013), estimate the eect of the experiment on ling for the scal year 2014, and estimate the medium term impact on ling in 2015. The data includes all line items from the tax declarations, and we match it with payment receipts, including advance payments and nal payments, to estimate payment compliance. Finally, we match the rms' declarations with third-party reports submitted by other rms, state institutions, and credit/debit card companies.
These data identify sellers and purchasers, transaction types, transaction amounts, and tax withheld where applicable. About 72% of rms who led an income tax return in 2014 were reported by at least one client or supplier, 9% were reported by a credit or debit card company, and 6% by a state 17 See Brockmeyer and Hernandez (2016) for details on this withholding scheme.
18 Such as pertaining to specic sectors or reporting a prot rate substantially dierent from the sector specic rate. 10 institution.

Experiment Design
Our study design relies on a randomized communication experiment implemented by the tax authority in Costa Rica. Table 1 summarizes the experiment design. The target population included 115,000 rms that were registered with the tax authority, but had not led their income tax declaration for 2014 by February 15, 2015, two months after the regular ling deadline. Of these non-lers, the experiment targeted 49,757 rms that had an email address on le.
19 The experiment was divided into two sub-experiments, targeting rms that were covered by at least one third-party report from a client or supplier (N = 12, 515), i.e. the rms that were reported to be economically active, and those that were not covered by any third-party report (N = 37, 242). To determine which rms were covered by third-party information, the authority considered all reports by other rms, by state institutions, and by credit/debit card companies. 20

Firms Covered by Third-Party Information
Firms covered by third-party information were randomly assigned to one of three groups: a control group and two treatment groups. The control group received no email message. Firms in the treatment group received an email from the tax authority, requesting it to le the income tax declaration for 2014, as shown in Figure A1 in the Appendix. The message content was similar to past communication campaigns. It emphasized that not ling taxes is a serious oense, and that oenders could be audited or subject to business closure, as stipulated in the law. Additionally, the message integrated ndings from behavioral design to strengthen the message impact, as studied by Hallsworth et al. (2014), BIT (2015), and Kettle et al. (2016). The message used shortened and simplied text (with legal details below the main body of the email), featured a clear call to action written in red capital lettersPlease le your income tax return in the next 10 days, provided 19 Given the costs of sending letters as well as their slow and incomplete delivery, the tax authority contacts rms by post only in the context of audits, when a written announcement of the audit is required. 20 A small number of rms in the study shared the same primary email address, either because they had a common owner or shared a common legal representative. For this reason, rms were grouped into clusters based on their primary email address and randomization took place at the cluster level. Throughout our analysis, we use standard errors that are robust to within-cluster correlation, and the results are robust to limiting the sample to clusters with only one rm (98% of clusters). The full experiment sample, including the SMS experiment described in the Appendix, contains 80,605 rms and 77,300 clusters. The mean number of rms per cluster is 1.04 and the median is 1. a direct link the the tax form, and was personalized with the name of the addressee featuring in the address eld. The message also presented the social norm8 out of 10 [tax-registered] Costa Ricans have led their 2014 income tax returnand introduced the possibility of public shaming through the publication of names. The social norm and the deterrence content of the message are all fact-based and credible, given the usual enforcement activities the tax authority conducts through audits, rm closures, and the online publication of the list of late-lers (for the sales tax) and late-payers (for various taxes).

21
As the tax authority routinely uses third-party information in its enforcement activities and mentions this to taxpayers, the baseline treatment message (treatment 1) also stated that We have third-party information, conrming that you or your client performed activities in 2014 which require you to pay taxes. 22 Treatment 2 further strengthened this statement by providing rms with specic examples of third-party information held by the tax authority about their activities: Treatment 2 (T2): We have third-party information conrming that you or your client performed activities in 2014 which require you to pay taxes. From third-party reports (D150, D151 and D153), we know about your operations, for example: • Sales of at least XXX reported by COMPANY, • Sales from credit/debit cards of at least ZZZ reported by BANK, • Sales or contracts with state entities of at least WWW.
For each type of third-party information held by the tax authority (reports from other rms, state institutions, and credit/debit card companies), it listed the transaction amount and purchaser of the highest reported transaction. Providing evidence of third-party reported transactions and transaction partners clearly demonstrates the tax authority's possession of third-party reports and thus makes the message highly credible. In addition, providing examples rather than the total amount of third-party reported transactions, as in Carrillo, Pomeranz, and Singhal (2016), allows us to apply this treatment to small or marginally formal rms with very small third-party reports.
21 As the message style and content used in past communication campaigns with non-lers varied from year to year, relied on a diverse set of communication methods (emails, SMS, phone calls, invitations for personal interview), and messages were not systematically sent to all late lers, we consider that a treatment eect compared to the control group cannot simply be due to sending a dierent message.
Finally, the design of the treatment allows us to test whether rms over-or under-estimate the amount of information that the tax authority holds about them.

Firms Not Covered by Third-Party Information
As in the rst sub-experiment, rms not covered by third-party information were also assigned randomly to either a control group, which received no email, or one of two treatment groups. The treated groups received an email that was nearly identical to the email in the rst sub-experiment, as shown in Figure A2 in the Appendix. The only dierence is the paragraph on third-party information, which was either omitted entirely (treatment 1), or replaced by a weaker but true statement (treatment 2): Treatment 2 (T2): The tax authority uses information from third-party returns (D150, D151 and D153) to identify economic activity and sources of income. This treatment thus does not claim that the tax authority has third-party information about the taxpayer in question, but it may encourage compliance among rms who are uncertain about whether they have been reported by a supplier or client.
As the message content here diers slightly from sub-experiment 1, comparing treatment eects across sub-experiments confounds the dierence in treatment and the dierence in the target population, which may both generate dierent treatment eects. The most comparable treatments are the weaker message for rms covered by third-party information (T1) and the stronger message for rms not covered by third-party information (T2). We will return to this comparison in our analysis of how treatment eects dier for rms covered and not covered by third-party information.

Experiment Timing
The experiment took place between March and April 2015, as shown in 1. The list of non-lers was extracted on February 15, 2015, two-and-a-half weeks before any emails were sent to rms covered by third-party information and seven weeks before any emails were sent to rms not covered by thirdparty information. The emails were sent on specic dates. As emails were not sent automatically but manually by individual tax ocers in the regional tax authority, the interventions were sequenced to accommodate the available human resources. Given the existing communication systems and data management procedures, it was not possible to update the list of non-lers at the start of each experiment. Some rms in the experiment sample had thus already led by the time the emails were sent. This allows us to demonstrate parallel trends in the treatment and control groups between the extraction of the list and the start date of the experiment. Moreover, the fact that emails are delivered instantly, as opposed to letters which vary in their delivery time, allows us to test whether treatment eects emerge sharply at the start of the experiment.

Balance of Randomization
To assess the internal validity of the experimental design, we examine the balance of treatment and control groups in terms of characteristics and compliance outcomes at baseline. Table 2 presents balance in terms of rm characteristics that are relevant to compliance behavior, and of which we include a subset as controls in our estimation. The characteristics include the rm type (corporation or self-employed), whether the rm has a legal representative, a secondary email address on le 23 , whether it is located in the capital city of San José, and the total transaction amount reported by third-parties. The latter is measured by indicators capturing whether the total amount of thirdparty reported sales for a given rm, as per the sum of reports by client companies, state institutions, and credit/debit card companies, is above CRC 2.5 million or above CRC 6 million. These cutos correspond to the priority group designations used by the tax authority in prior communication campaigns targeting non-compliant rms, when rms with larger third-party reports were more likely to be contacted.
In addition, as some regional tax oces deviated from the experiment design and contacted rms prior to the start of the experiment date through phone calls and emails (dierent from the experimental emails presented in the previous sections), we also consider whether the occurrence of such early communication is balanced across treatment groups. Finally, as we expect past tax compliance to be a predictor of future compliance, we also consider past compliance as measured by a series of dummy variables that capture whether the rm made any quarterly advance tax payments for 2014, and whether it led income tax, had a positive net liability, made a payment, 23 When treated rms had two email addresses on le, the tax authority sent the same email to the two addresses.
For experiment 1, all (and only) rms with a legal representative have a second email address on le; for experiment 2, we test whether the proportion of rms with two email addresses is balanced across control and treatment groups, and we control for second email addresses when we estimate treatment eects. 14 or submitted a third-party informative declaration (D151) about a client or supplier in 2013. Table 2 covers experiment 1 in columns 1-4 and experiment 2 in columns 5-8. Column 1 (5) displays the average for the control group, columns 2 and 3 (5 and 7) show the dierence between the control group and treatment groups 1 and 2, respectively, and column 4 (8) reports p-values from a test of the hypothesis that the two treatment groups are jointly equal to the control group.
All p-values exceed the 10% signicance cuto and for 40 out of 42 coecients, we fail to reject at the 10% level of signicance the hypothesis that the treatment group mean equals the control group mean. We thus conclude that the control and treatment groups in both experiments are well balanced.
In experiment 1, only 15% of rms are corporations, 61% use a legal representative and 35% and 18% respectively have medium or high amounts of third-party information. The experiment 2 sample features a 26% share of corporations, and a 66% share of rms using a legal representative.
The fact that self-employed below the exemption threshold do not have to pay income tax, and may be unaware that they are nonetheless required to le a declaration, could explain the high share of self-employed compared to corporations in both experiments. Only 6% of rms in experiment 1 and 5% of rms in experiment 2 have a second email address on le. In both experiments, about 50% of rms are located in the capital city. As for past compliance, only 2% of rms in experiment 1 made advance payments for the income tax for 2014, 33% led income tax in 2013, and 5% made a payment in 2013. Past compliance rates are even lower among rms in experiment 2, as would be expected given that these rms are not covered by any third-party information. The rms who were contacted early mostly pertain to experiment 1, representing 12% of the sample, but are perfectly balanced across control and treatment groups. Table 3 examines the balance of outcomes of interestincome tax compliance and other compliance outcomesmeasured on the day prior to the start of the rst email experiment (March 3, 2015). The fact that all declarations and payment receipts carry a time-stamp and indicate the corresponding scal period allows us to precisely capture compliance at dierent points in time.
The structure of this table is identical to table 2. We nd that about 5% of rms in experiment 1 and 1% of rms in experiment 2 led their income tax declaration after the extraction of the non-ler list and before the start of the experiment. The share of rms reporting a positive net liability and making a payment is below 2% for experiment 1, and close to zero for experiment 2.
Despite not ling their own tax declaration, 16% of rms in experiment 1 and 1% in experiment 15 2 presented a third-party declaration about a client or supplier. Compliance with the sales tax is also non-negligible, with an average number of sales tax declarations over the last twelve months of .6 in experiment 1 and .24 in experiment 2, despite the fact that only about 15% of these rms are liable for the sales tax. As would be expected given the short window between extraction of the non-lers list and the experiment start date, hardly any rms deregistered, deregistered from the sales tax or switched to the simplied tax regime in this period.
We can reject the hypothesis that the treatment group mean equals the control group mean in 38 out of 40 means tests in Table 3, and the p-values of the test jointly comparing the treatment groups to the control group exceeds the 10% signicance cuto in all cases. For the two variables for which we detect a statistically signicant dierence (positive net liability and deregistration, both in experiment 2), the means are extremely close to zero, so that the result is driven by a handful of rms. We thus conclude that the control and treatment groups are well balanced in terms of the relevant rm characteristics and outcomes measured prior to the start of the experiment. This validates a causal interpretation of the treatment eects, and allows for straightforward estimations.

Results
This section presents the results of our empirical analysis. First, we present the estimation strategy.
Second, we present the results on income tax compliance, other compliance outcomes such as sales tax compliance and information reporting, and examine persistence of the eects in the medium term. Third, we discuss the heterogeneity of our results and potential mechanisms. Finally, we conclude with a cost-benet analysis.

Estimation
To estimate treatment eects on binary outcomes, such as income tax ling or making a payment, we use the probit specication: where T 1 i and T 2 i indicate treatment 1 and 2, respectively, for rm i; X i is a vector of covariates; and Φ is the cumulative distribution function of the standard normal distribution. The parameters α, β 1 , and β 2 , and the parameter vector γ are estimated using maximum likelihood. Our probit estimates are very similar to ordinary least squares (OLS) estimates.
To estimate treatment eects on continuous outcomes, such as the payment amount, we use two specications. We rst use OLS to estimate the log-linear model where y i is payment for rm i, ε i is an error term, and T 1 i , T 2 i , and X i are dened as before. Second, we use iterated, reweighted least-squares (maximum quasi-likelihood) to estimate the Poisson pseudo-maximum likelihood (PPML) model: where g(·) is the natural log function, y i ∼ Poisson, and the other variables are dened as before.
PPML has been shown to outperform OLS if the outcome variable has many zeros (Santos Silva and Tenreyro 2006). Nonetheless, our PPML estimates of the eect of treatment on payment are very similar to OLS estimates.
In all specications, we compute (Huber-White) standard errors that are robust to within-cluster correlation, as randomization was conducted by clusters of the primary email address. 24 For the probit and PPML specications, we report average partial eects of discrete changes from zero to one for binary independent variables, such as the treatment indicators, and compute the clustered standard errors using the delta method. In addition to testing the hypotheses that β 1 and β 2 are signicantly dierent from zero, we report the p-value from a (Wald) test of the hypothesis that β 1 and β 2 are equal.
We condition on a set of control variables, which include rm type (corporation), whether the rm has a legal representative, rm location, amount reported by third-parties, and the rm's previous compliance record (i.e. income tax ling and payment in the previous year). Each of these controls is dened as in the balance tests in Section 3.4 and measured prior to the start of the experiment.
24 The results are also robust to conducting the estimation on the sample of one-rm clusters only.

Income Tax Compliance
We start by analyzing the impact of the emails on income tax compliance non-parametrically. Figure   2 shows the rate of income tax ling and payment over time by treatment status, with the start of the experiment indicated by a vertical line. The left (right) column refers to rms with (without) third-party information. While pre-intervention trends in the treatment and control groups were nearly identical for all outcomes, a positive treatment eect on ling and payment emerged sharply at the start of the experiment. This eect stabilized by about ve weeks after the experiment start date, and did not decrease thereafter.
25 This conrms that the emails generated additional tax payments rather than just bringing forward payments that rms would have made anyways.
After 15 weeks of the intervention, the ling rate for information-covered rms reached 32.5% for those sent the baseline email, and 34.2% for those sent the email with examples of third-party information, relative to 11.5% for the control group. 26 The dierence between the two treatment eects is statistically signicant at the 10% level. The payment rate was 4.7% for those sent the baseline email, 5.3% for those sent the email with examples of third-party information, and 1.7% for the control group, though the dierence between the two treatment groups is not signicant.
For rms not covered by third-party information, the shape of the ling and payment response relative to the control group is similar, with the exception of any signicant dierence between the two treatments. Emphasizing the use of third-party information, in addition to highlighting deterrence measures, thus did not enhance compliance among rms not covered by an information trail, which suggests that these rms did not expect the tax authority to possess any third-party reports about them. After 15 weeks of the intervention, the proportion of treated rms ling an income tax declaration reached 19%, relative to 3.9% for the control group. The rate of payment among rms not covered by third-party information was below 1%, as most rms declare a net liability of zero, but the payment rate was still signicantly higher for the treatment group.
To consider a larger number of outcomes and control for covariates, we report probit, OLS, and PPML estimates in Tables 4 and 5 for the two sub-experiments. Table 4 presents estimates of the treatment eect at 15 weeks for rms covered by third-party information. The rst three columns report extensive-margin responses on income tax ling, reporting a positive net liability, and making 25 This is true also when considering a longer post-intervention period (results available upon request). 26 The fact that over 60% of the treatment group do not le in response to the (strong) enforcement message might partially be attributable to the fact that not all taxpayers received and opened the email. It is unfortunately not possible to identify the taxpayers who did not receive or open the email. a payment. We estimate that the baseline email increased the probability of ling by 21.3 p.p., which is consistent with Figure 2. The eect of the information email, at 23.2 p.p., is signicantly greater than the baseline email. The two emails also increased the probability that a rm reported a positive net liability (by about 5 p.p.) and made a positive payment (by about 3.4 p.p.). Note that the payment rate is lower than the share of rms reporting a positive liability, as some rms make quarterly advance payments or are subject to withholding at amounts that fully cover their liability, and others under-pay or pay with delay. The fourth and fth columns show that the emails also increased the average payment amount, although this is driven by a greater number payers, not larger payments conditional on making a payment.
27 Using PPML, we estimate that the baseline email increased income tax payments by CRC 8,168 (US$ 15) per taxpayer, on average, while the information email increased payments by CRC 10,192 (US$ 19). 28 The information email had a larger impact on all outcomes than the baseline email, but the dierence is statistically signicant at conventional levels only for payment, where we observe the highest average and presumably the least noise among the dummy variable indicators. Table 5 shows the analogous results for rms not covered by third-party information. Recall that, for these rms, the baseline treatment omitted any mention of third-party information, and the information treatment mentioned the general use of third-party information by the tax authority, without making specic reference to the email recipient (see Section 3). The emails increased the probability of income tax ling by 15 p.p.; they also increased the probability of reporting a positive net liability and of making a payment, but the magnitude of the eect is small0.6 p.p.compared with the eect on ling. The eect on the payment amount is statistically signicant but not economically large. The treatment increased payment by CRC 215 on average (US$ 0.39).
In sum, we nd that the emails signicantly improved income tax compliance by non-lers.
For rms covered by third-party information, the eects of emails that listed specic examples of information known to the tax authority were generally higher. All treatment eects estimated here equal or exceed those from other communication experiments (Castro and Scartascini 2015;Del Carpio 2014;Fellner, Sausgruber, and Traxler 2013;Kettle et al. 2016), which suggests that combining dierent messages contents that have proved to be impactful individually (deterrence, 27 Note that we consider payments made by the taxpayer with her annual declaration, and ignore the quarterly advance payments during the year. If a taxpayer is a non-ler and also has outstanding advance payments, those would have to be made with the annual declaration, and are thus considered in our estimation.
28 We winsorize payment amounts at the top 0.1% of the unconditional payment distribution to reduce the inuence of outliers.
use of third-party information, behavioral design) can generate a larger impact overall.

Other Compliance Outcomes
As the experiment had a strong impact on the targeted compliance outcomes, notably income tax ling and payment, it is appropriate to consider also spillovers on other compliance outcomes.
Indeed, taxpayers might perceive the intervention as a general increase in enforcement, and improve compliance also with other tax ling and payment obligations. Alternatively, they might perceive the intervention as pertaining to income tax compliance only, and increase compliance with the targeted tax but compensate for lost income by reducing compliance with another obligation towards the government. To shed light at this, we use rich administrative data on rm's ling of informative declarations, sales tax declarations, sales tax payment, deregistration, and switches to the simplied regime 29 , all of these representing compliance outcomes which were not directly targeted by the intervention. We also consider income tax compliance in 2013, which may be positively or negatively aected by the intervention (targeting non-lers for 2014), as a non-negligible share of rms le (or pay) their taxes with substantial delay (see Brockmeyer and Hernandez (2016) for details), and 80% of non-lers for 2014 were also non-lers in 2013. This is to our knowledge the rst study to examine the impact of enforcement on such a large variety of compliance measures. Table 6 shows the treatment impact on the above-mentioned outcomes, for experiment 1 in Panel A and experiment 2 in Panel B. Columns 1-3 in Panel A show that treated rms were marginally more likely to le an information report (D151) about their supplier, and signicantly more likely to le an information report about their client. 30 With a 4.8 p.p. increase over a control group average of 12.8%, the eect is twice as large for the information treatment as for the baseline treatment, and the two coecients are statistically distinguishable at the 5% condence level. The observed impact can be explained by the fact that, for rms ling an income tax declaration, ling an informative declaration generates only a small hustle cost, but no monetary cost, and prevents a possible ne for non-compliance with the reporting obligation. Consistent with this, 53% of non-lers that led a third-party report have also led their own income tax declaration. As the emails with additional third-party information made the existence of third-party reports salient and provided information 29 Firms can opt into simplied income or sales tax regimes if they meet certain criteria, such as expenditure or employment thresholds. To do this, they must submit a modication form to the tax authority. 30 We do not consider other information reports, such as the D150 and D153 reports, as those cannot be led by rms.
about the nature of these reports, it is not surprising that this treatment had a signicantly larger impact on reporting compliance than the baseline treatment. About 25% of the newly generated information reports concern transactions that were not previously known to the authority while 75% conrm transactions that had already been reported by the other transaction partner (the client in most cases). The impact on information reporting of clients is also present and signicant, though smaller in magnitude, among rms not covered by third-party information. For both samples, we conrm in the bottom panels of Figure 2 that the pre-intervention trends in treatment and control groups were similar, and the eect emerged sharply at the time the intervention started. A targeted (income tax) enforcement intervention thus led to a signicant expansion of the tax authority's information set for future tax enforcement, of the income tax and other taxes.
Columns 4-6 show that the intervention had no signicant impact on sales tax compliance, which is the most important tax paid by rms. However, given the small share of rms (especially among unincorporated rms) that are liable for the sales tax, it is dicult to detect any signicant change in compliance with the sample size at hand.
Columns 7-9 show that the emails increased rms' likelihood of deregistering with the tax authority. This is consistent with the fact that deregistration generates a hustle cost (visiting the tax oce 31 ), and there are eectively no nes for remaining registered but economically inactive, so that rms are unlikely to voluntarily deregister when ceasing activities. For rms with third-party information, treatment increased the deregistration rate from 0.9% to about 2%, and coverage by particularly large amounts of third-party information was reassuringly negatively correlated with deregistration. For rms not covered by third-party information, treatment increased the deregistration rate from 1.2% to about 3%. Firms not covered by third-party information were also marginally more likely to deregister only from the sales tax (rather than from all tax obligations) or switch to the simplied tax regime which is available to rms below certain size thresholds in specic sectors (see Section 2), but this concerns less than 0.5% of the sample. The smaller eect on information-covered rms is consistent with these rms' reported economic activity in the scal year in question (although they could have seized activities during the year).
When considering the rms that deregistered and those who did not, pooling the two experiments, it appears that the deregistrants were rms that strive to be compliant on paper, without 31 The possibility for online deregistration was abolished as rms exploited it to register with the aim of obtaining a book of ocial receipts, only to deregister immediately afterwards, as reported by the tax authority.
transferring any revenue to the tax authority. Among deregistrants, 61% led an income tax declaration for 2014 and 52% did so for 2013, versus 21% and 26%, respectively, for rms that remained in the tax register. Yet the mean reported liability was orders of magnitude lower for deregistrants compared with rms remaining in the tax registerCRC 826,620 versus CRC 5,100 in 2014, and CRC 656,409 versus CRC 40,101 in 2013. While some deregistrants continued their business activities informally (8.2% or 103 rms were third-party reported as suppliers in 2015), they would have been unlikely to pay more taxes in the current enforcement environment. It thus appears that the deregistrations reduced the number of taxpayers to be managed by the administration, but did not signicantly aect tax collection.
Finally, columns 10-11 show that the emails improved compliance for the previous tax year, by signicantly increasing the probability of (late) ling and payment for the previous tax year, 2013. This is true even though the emails specically mentioned the requirement to le the 2014 income tax return. Emails to information-covered rms increased rm's likelihood of ling an income tax declaration by 2-3 p.p., compared to the control group's average of 35.0%. The impact on rms no covered by third-party information was even largerabout 5 p.p. compared to the control group's average of 18.9%. In both samples, treated rms were slightly more likely to make a payment for the income tax in 2013, but the increase was economically small (below 0.5%).
In sum, our analysis of a diverse set of compliance outcomes that could potentially be impacted by the enforcement intervention detects positive treatment eects on compliance with third-party reporting and past income tax obligations, and a small increase in deregistration rates, mostly reecting the exit of rms with disproportionally low reported liabilities.

Persistence of Eects
Having shown that the treatment had an economically large impact on contemporaneous income tax compliance and other compliance outcomes, we now examine whether these eects persisted over time without a follow-up communication. 32 Table 7 shows the impact on compliance outcomes and third-party reports in 2015, one year after the treatment. For compliance outcomes (columns 1-3 and 7-9), we pool the two treatments for simplicity, as the coecients do not dier signicantly by treatment. For rms covered by third-party information, the email messages increased the income 32 The tax authority conducts other communication campaigns for the ling of sales tax and informative declarations, and it is possible that rms in our experiment were contacted through one of these campaigns, but the targeting would have been orthogonal to our treatment group assignment.
22 tax ling rate one year later by 6.5 p.p., over a control group average of 35.1%. The eect was even larger7.3 p.p. or 46%for rms not covered by third-party information, which received a presumably weaker email message in the treatment year. The emails also had a statistically signicant but economically small eect on payment rates one year later: 1.0 p.p. for rms with third-party information and 0.2 p.p. for rms without information. Finally, treated rms were more likely to le informative declarations in 2015, mostly to report a client. For information-covered rms, the emails generated a 2.3 p.p. increase in the third-party reporting rate, thus further expanding the tax authority's enforcement capacity.
Conversely, we do not detect any eect of the emails on rms' propensity to be the subject of third-party reports in a later year. Columns 4-5 in Table 7 display the eect of the two treatments on rms' likelihood of being reported by state institutions (D150), private sector clients or suppliers (D151), or card processing companies (D153) in 2015. Treated rms were no more or less likely to be the subject of these reports, even if they received the stronger information email, which provided them with examples of third-party information held by the tax authority. The result holds also when pooling the two treatments. Thus, the treatment thus does not seem to have distorted production networks by encouraging rms to reduce trade with state agencies or credit/debit card machine usage, or to change trading practices with other rms in an eort to avoid being covered by third-party reports.

33
Overall, these ndings suggest that one-time deterrence messages can have a signicant and positive impact on compliance in the medium term, including compliance with information reporting requirements. The strong medium-term eects in our experiment suggest that the email messages lead rms to update their beliefs regarding the tax authority's enforcement capacity, i.e. the capacity to identify and follow up on non-lers, and that the update was persistent over time, hence conrming the messages' credibility. 34 The emails thus did not just act as a reminder or nudge, nor as a temporary, yet ultimately empty, enforcement threat.
The positive treatment eect in the medium term also sheds some light on the size of potential real eects. By reducing (compliant) rms' after-tax protability, the treatment might have lowered 33 We also examine potential compliance spillovers of treatment on rms' trading partners, as identied by the D151 information reports from clients and suppliers, but do not nd any spillover eects.
34 It is possible that the treatment and subsequent consultations with tax ocers allowed rms to gain new information about the tax ling procedure, which would have reduced the cost of future tax ling. However, we consider this mechanism to be less important than the deterrence mechanism, as tax ling in Costa Rica is very simple, all the necessary information is available online, and rms in our sample are tax registered and have thus been in contact with the tax authority at some point, often through ling a previous income tax declaration. 23 investment and rm growth. However, the persistent treatment eect on compliance shows that the (positive) eect on income reporting is larger than the (potentially negative) eect on true income.

Heterogeneity
Although the emails can be sent at a marginal cost of zero, communications campaigns such as the one analyzed here still generate non-negligible costs to the tax authority (more on cost-eectiveness below) as emails have to be personalized manually or an algorithm needs to be constructed for this task, and the communications generate information and advice requests from targeted taxpayers to tax ocials. Ocials report that responding to these inquiries constitutes the most important cost of communication campaigns. Given human resource constraints, it is thus important to understand which taxpayers are most likely to respond to the treatment and target the intervention accordingly.
This section considers heterogeneity in treatment eects by coverage of third-party information, and by other rm characteristics, distinguishing the two main outcomes of income tax ling and payment.

By Third-Party Information
It is ex ante ambiguous whether coverage by third-party information or having larger amounts of third-party information would be associated with larger treatment eects. The information could interact with the intervention to strengthen its eect. Alternatively, rms that are covered by third-party information may be more likely to comply even without a treatment, and thus less likely to respond to the intervention. We start by considering heterogeneous treatment eects by information coverage, and then examine heterogeneity by the amount of information within the sample of information-covered rms.
To compare treatment eects across the two sub-experiments for rms with and without thirdparty information, we focus on the most comparable treatments. These are the baseline email for rms covered by third-party information, which emphasized the presence of third-party information about the rm in question without providing specic examples, and the second email for rms that are not covered, which mentioned the general use of third-party information by the authority. The latter message was thus weaker, but delivered the strongest message on third-party information that the authority can credibly send to rms in this sample. While Figure 2 and Tables 4 and 5 35 It is also conceivable that the real eect is positive, for instance if better tax compliance allows rms to trade with more formalized and more productive rms (though this requires assuming that non-lers were not prot maximizing).
show that the percentage point increase in the rate of income tax ling is greater for rms covered by third-party information (21 p.p.) than for rms not covered (15 p.p.), the proportional eect is greater for rms not covered by third-party information. Their treatment group ling rate is 380% greater than the control group, compared with 180% for information-covered rms. The same qualitative dierence between the percentage point increase and the proportional eect holds when considering treatment impact on the rate of payment, the payment amount, and the rate of deregistration. Only the response in terms of information reporting is proportionally larger for information-covered rms. The large proportional eects among rms not covered by a paper trail are somewhat surprising, but can be explained by the low baseline (and control group) compliance rates. 36 Regardless, policymakers striving to increase revenue should target information-covered rms rst, as their absolute payment response is an order of magnitude larger than the response among non-covered rms.
Zooming in on rms covered by third-party information, Table 8 shows that treatment eect heterogeneity with respect to the extent of information coverage is also complex. The ling rate responds less strongly to the treatment for rms with larger amounts of third-party reported sales (columns 1-3), but these rms' payment rate responds more strongly, at least to the information treatment (5-7). The number of dierent third-party reports is associated with a larger treatment eect for both outcomes (columns 4 and 8).
To ascertain that the heterogeneity by third-party reported sales is not driven by a particular cuto choice, we also report the compliance outcomes by deciles of third-party information in Figure   3. The results are similar when using deciles of the maximum of self-reported sales in year t − 1 (or the most recent year available) and third-party reported sales in t. The exercise is thus equivalent to examining treatment eects by rm size as measured in sales. 37 We nd that the treatment eect on ling is driven by seemingly smaller rms, with larger rms being signicantly more likely to declare even when in the control group, whereas the treatment eect on payment is driven by 36 The fact that baseline compliance is higher among information-covered rms but the proportional treatment eects are larger among rms not covered by third-party information suggests that enforcement and third-party information are substitutes when it comes to tax compliance at the extensive margin. This contrasts with the nding by Almunia and Lopez-Rodriguez (2015) that information trails and monitoring eort are complements, although they focus on rm bunching below revenue thresholdsan intensive-margin response. 37 We can also estimate rm size for rms without third-party information, taking reported sales from the most recent available income tax declaration, but this measure is available only for a subset of rms and is more noisy, as many rms have not led for several consecutive years. This, combined with the smaller absolute treatment eects in the sample of rms without third-party information makes it dicult to examine treatment heterogeneity among these rms. larger rms. This is consistent with the fact smaller rms, especially the self-employed, may declare without making a payment (due to being below the exemption threshold or deducting suciently high advance payments or tax withheld), and large rms are more likely to incur a positive tax liability. The intervention thus enhanced compliance along the rm-size distribution, but derived its revenue eect from larger rms. 38

By Other Firm Characteristics
Other rm characteristics along which the treatment eect may vary include rm type, as corporations and the self-employed are taxed under dierent tax schedules, location in the capital city, and past compliance record. Table 9 considers heterogeneity along these lines for rms with third-party information in Panel A and for rms without such information in Panel B. Unsurprisingly, given the lack of an exemption in their tax schedule, the ling rate of corporations compared to the selfemployed responds less strongly but their payment rate responds more strongly to the treatment (columns 1 and 6). There is no heterogeneity in treatment eect along this line on the likelihood of ling by rms without third-party information (Panel A, column 1). Firm location in the capital city is associated with a marginally stronger treatment eect in only one out of the four estimations (columns 2 and 7). Past compliance in the form of ling and payment of the income tax in 2013, and ling of sales tax, strongly predicts a larger treatment eect, as would be expected. This is the case for both compliance outcomes and both sub-samples (with the exception of sales tax compliance which is negatively correlated with the treatment eect on ling among information-covered rms).
When targeting their intervention, it is thus advisable for the tax authority to take into account a rm's degree of third-party information coverage, its rm type, and its past compliance record.

Mechanisms
Before concluding our study, it is appropriate to examine the mechanisms of the large treatment eects on tax payment for rms covered by third-party information. Treatment more than doubled the rate of payment and approximately doubled the amount of payment, with larger eects for the information treatment. These large eects contrast with other studies using third-party information to enhance compliance on the intensive margin. These studies nd that rms respond to an increase 38 With the caveat of low precision, we nd that the eect of the treatment on submitting an informative declaration does not dier by rm size (the likelihood of complying on this margin increases with rms size for both the treatment and control group), and the treatment eect on deregistration is concentrated among smaller rms. 26 in third-party reported sales by increasing both their sales and costs, thus minimizing any increase in reported prots and taxes paid (Carrillo, Pomeranz, andSinghal, 2016 andSlemrod et al. 2015).
The challenge in our study is that treatment both increased the ling rate and potentially altered reported liabilities conditional on ling.
We start by comparing third-party reported sales, self-reported sales, and self-reported costs nonparametrically, as in Carrillo, Pomeranz, and Singhal (2016). Figure 4 shows that self-reported sales increase less than one-for-one with third-party reported sales (Panel A), although self-reported sales are on average about 30% higher than third-party reported sales. It thus does not seem to be the case that rms under-estimate third-party reports and match reported sales to an amount lower than true third-party reports. This result supports the use of examples rather than amounts of third-party information in the information treatment. However, the average rm matches declared sales very closely with declared costs (Panel B). Controlling for covariates, Table 10 shows the impact of the two treatments on declared sales, costs, and prots, measuring these variables with an indicator for positive amounts, an indicator for amounts larger than third-party reports, or in logs (in absolute amounts for prots as these can be negative). The results are tentative, but suggest that the information treatment generated a signicantly larger increase in reported sales than the baseline treatment (columns 1-3), but only a marginally larger increase in reported costs (columns 4-6).
Firms receiving the information treatment thus increased reported sales by more than other treated rms, and did not fully oset this through cost increases. As a result, the likelihood of reporting a positive prot was signicantly higher among rms receiving the information treatment than among rms receiving the baseline treatment (column 7). While this evidence remains suggestive, it is consistent with the possibility that the information treatment generated an improvement in rm reporting behavior conditional on income tax ling.

Cost-Benet Analysis
We conclude with a cost-benet analysis, considering the cost of the intervention and the increase in tax revenue it generates. The primary cost to the tax authority is the human resource cost of sending the personalized emails and responding to taxpayer inquiries. The authority reports that the sending of the emails was executed in seven and a half days by 32 tax ocers, paid at about 39 Results are similar when conditioning on ling, with the obvious caveat that the comparison across treatments is then no longer experimental.

27
CRC 36,700 a day. 40 We assume that each ocers spent at most an additional ve days answering taxpayes' inquiries. This generates a total cost of CRC 14.7 million (US$ 27,000). To draw the most conservative conclusion possible, we take this cost into account, although other studies implicitly assume that the opportunity cost of time for the tax ocers is zero.

41
The direct benets are measured by the increase in tax payment from treated rms. Among rms covered by third-party information, the baseline email increased rms' income tax payments by CRC 8,168 (US$ 15), on average, 15 weeks after the start of the experiment, while an email that lists specic examples of information known to the tax authority increased payment by CRC 10,192 (US$ 19). The eect on payment at 15 weeks was smaller for rms not covered by third-party information, for whom the email increases payment by CRC 215 (US$ 0.39). In total, we estimate that the emails increased income tax revenue by CRC 82.2 million, or US$ 151,000. Of this amount, CRC 76.9 million came from emails sent to information-covered rms. Sending the strongest email, which listed specic examples of third-party information, to all information-covered rms, would have generated an additional CRC 50.7 million, or US$ 93,000 in revenue. We do not include in our calculation the impact on income tax payment for prior or future years, as we can detect a statistically signicant eect only on the propensity to make a payment for these periods, but do nd a statistically signicant point estimate for the payment amount increase.
Although the additional revenue generated by the experiment constitutes less than .1% of total income tax revenue, the intervention was highly cost-eective, with a cost-benet ratio of about 1:5 42 , and serves the broader purpose of sustaining voluntary compliance by detecting and following up on non-compliers. As we have shown, the intervention had positive indirect eects in terms of enhancing compliance with information reporting requirements, which facilitate future tax enforcement, and in terms of better medium term compliance for treated rms that update their beliefs about tax enforcement. These eects could potentially generate compliance spillovers on non-treated rms.
Beyond revenue considerations, the intervention improves horizontal equity of taxation by enhancing compliance among relatively small rms, and could thus improve tax morale and the per-40 Fixed cost already incurred include the cost of maintaining the taxpayer and third-party reporting database. 41 We further assume that the administrative costs of ling for taxpayers are small, which is appropriate given the simplicity of the tax code and the online ling system. ception of fairness of the tax system. In addition, the new information generated through rms' self reports and third-party reports give the government a broader view of the economy and hence a better basis for policy design.

Conclusion
This paper has argued that non-ling among tax registered rms constitutes an important and under-researched compliance gap in low income countries, that can be addressed cost-eectively.
In Costa Rica, approximately 25% of tax registered rms do not le their income tax declaration in a given year, and this share is similar in other countries in the Latin America region. We evaluate a nation-wide communication campaign in which the tax authority in Costa Rica requested non-ling rms by email to le their income tax declaration. The emails featured strong but credible deterrence messages, integrated behavioral insights and leveraged third-party reports about taxpayers' business activities. We nd that the emails tripled the ling rate and doubled the payment rate among previous non-lerstreatment eects that are substantially larger than those found in much of the existing literature, and that further increase when emails specically mention examples of third-party reported sales. The return on an email was US$ 19 for rms covered by third-party information, but only US$ .39 for rms not covered by third-party information.
We extend the literature on communication interventions to reduce compliance gaps by considering a large variety of outcomes, all measured through rm-level administrative tax records.
We show that the emails generated no negative spillovers on sales tax compliance. They slightly increased the deregistration rate, but they also increased the likelihood of ling third-party reports about clients or suppliers, and income tax ling in the year prior to and following the year of the intervention. This nding of a persistent treatment eect, which applies to income tax ling and payment and the ling of third-party reports, suggests that the intervention permanently raised rms' perceived enforcement probability and hence their compliance level.
Although the intervention increased total tax revenue by less than a fraction of a percent, the intervention was highly cost-eective and can thus be seen as a simple and sustainable way to widen the tax net. It may also generate positive compliance spillovers in the future, through the increased availability of third-party reports on rms' business activities. Whether the tax authority should allocate human resources to this intervention, or to audits, desk audits or follow-up on late-payers 29 depends of course on the elasticity of revenue to these dierent enforcement activities (Keen and Slemrod 2016).  Emails to taxpayers with third-party information (N = 12, 515)

March 410
No message control group T1: Baseline email T2: Information email (mentions amount of largest third-party information report) Emails to taxpayers without third-party information (N = 37, 242)

April 723
No message control group T1: Baseline email T2: Information email (emphasizes tax authority's use of third-party information) Note: The table shows the balance of randomization in terms of rm characteristics, as measured before the experiment start. The rows correspond to the dierent variables. Columns 1-4 (5-8) correspond to the sample of rms with (without) third-party information, i.e. experiment 1 (2). Column 1 (5) displays the mean for the control group, columns 2 and 3 (5 and 7) show the mean dierence between the control group and treatment groups 1 and 2 respectively, and column 4 (8) reports p-values from a test of the hypothesis that the two treatment groups are jointly equal to the control group. Robust standard errors clustered by email address are in parentheses. TPI stands for third-party information (third-party reported sales), meaning the sum of sales reported by clients (D151), state institutions (D150) and credit/debit card companies (D153). The cutos of 2.5 million and 6 million CRC correspond to the priority group designations used by the tax authority. Signicance levels are noted as per convention: * p<.10, ** p<.05, *** p<.01. Note: The table shows the balance of randomization in terms of outcomes, as measured before the experiment start. The rows correspond to the dierent variables for scal year 2014. The number of months that a taxpayer led and paid sales tax, and the sales tax payment are calculated over July 2013 until June 2014. Columns 1-4 (5-8) correspond to the sample of rms with (without) third-party information, i.e. experiment 1 (2). Column 1 (5) displays the mean for the control group, columns 2 and 3 (5 and 7) show the mean dierence between the control group and treatment groups 1 and 2 respectively, and column 4 (8) reports p-values from a test of the hypothesis that the two treatment groups are jointly equal to the control group. Robust standard errors clustered by email address are in parentheses. Signicance levels are noted as per convention: * p<.10, ** p<.05, *** p<.01.  Note: These gures show the percentage of rms ling income tax (row 1), paying income tax (row 2) and ling a third-party informative declaration (D151) about a client or supplier (row 3), all for scal year 2014. Column A corresponds to rms with third-party information and column B corresponds to rms without third-party information. The horizontal line in each gure indicates the experiment start date. The black solid line corresponds to the control group and the blue/red dashed/dotted lines correspond to the baseline treatment and information treatment respectively for the two dierent subsamples, as explained in experiment design Table 1. The numbers indicate the mean for each outcome and treatment group at 15 weeks after the start of the experiment. Stars indicate a signicant dierence compared to the control group and come from regressions that include controls (as in Table 4, Table 5, and Table 6). Signicance levels are noted as per convention: * p<.10, ** p<.05, *** p<.01. Daggers indicate signicant dierences between the two treatments. Note: This table displays estimates of probit, OLS and PPML estimations as explained in Section 4.1, using the control variables noted in the table rows. The columns display the outcome variables: dummies for whether the rm led income tax for 2014, reported a positive net liability and made a payment (considering only nal payments made with the declaration and not advance payments that may have been made earlier), and the (log) payment amount. All outcomes are measured 15 weeks after the start of the experiment. Robust standard errors clustered by email address are in parentheses. Average partial eects are reported for probit and PPML. Payment amounts are winsorized at the top 0.1% to reduce the inuence of outliers. TPI stands for third-party information (third-party reported sales), meaning the sum of sales reported by clients (D151), state institutions (D150) and credit/debit card companies (D153). The cutos of 2.5 million and 6 million CRC correspond to the priority group designations used by the tax authority. Signicance levels are noted as per convention: * p<.10, ** p<.05, *** p<.01. Daggers indicate signicant dierences between the two treatments.  Note: This table displays estimates of probit, OLS and PPML estimations as explained in Section 4.1. Panel A corresponds to rms with third-party information, using the same controls as in Table 4, and Panel B corresponds to rms without third-party information, using the same controls as in Table 5. The columns display the outcome variables, which refer to compliance for scal year 2014 unless otherwise noted. All outcomes are measured 15 weeks after the start of the experiment. Robust standard errors clustered by email address are in parentheses. Average partial eects are reported for probit and PPML. Sales tax payment amounts are winsorized at the top 0.1% to reduce the inuence of outliers. TPI stands for third-party information (third-party reported sales), meaning the sum of sales reported by clients (D151), state institutions (D150) and credit/debit card companies (D153). The cutos of 2.5 million and 6 million CRC correspond to the priority group designations used by the tax authority. Signicance levels are noted as per convention: * p<.10, ** p<.05, *** p<.01. Daggers indicate signicant dierences between the two treatments. Note: This table displays estimates of probit estimations, with dummy outcome variables as denoted in the column titles, measured in June 2016. Panel A corresponds to rms with third-party information, using the same controls as in Table 4, and Panel B corresponds to rms without third-party information, using the same controls as in Table 5. The treatment groups are pooled into one treatment dummy. The reported coecients are average partial eects, and robust standard errors clustered by email address are in parentheses. TPI stands for third-party information (third-party reported sales), meaning the sum of sales reported by clients (D151), state institutions (D150) and credit/debit card companies (D153). The cutos of 2.5 million and 6 million CRC correspond to the priority group designations used by the tax authority. Signicance levels are noted as per convention: * p<.10, ** p<.05, *** p<.01. Daggers indicate signicant dierences between the two treatments. Note: This table displays estimates of OLS estimations, with dummy outcome variables (measured 15 weeks after the experiment start) as indicated in the panel titles, and interactions between the treatment indicators and dierent control variables, as indicated by the column titles. The rows display the coecents on the two treatments, the control, and the interactions between each treatment and the control. All regressions are for the sample of rms with third-party information only, and use the same controls as in Table 4. Robust standard errors clustered by email address are in parentheses. TPI stands for third-party information (third-party reported sales), meaning the sum of sales reported by clients (D151), state institutions (D150) and credit/debit card companies (D153). The cutos of 2.5 million and 6 million CRC correspond to the priority group designations used by the tax authority. Signicance levels are noted as per convention: * p<.10, ** p<.05, *** p<.01.
42 Note: This table displays estimates of OLS estimations, with dummy outcome variables (measured 15 weeks after the experiment start) as indicated in the panel titles, and interactions between the treatment indicators and dierent control variables, as indicated by the column titles. Panel A corresponds to rms with third-party information, using the same controls as in Table 4, and Panel B corresponds to rms without third-party information, using the same controls as in Table 5. The rows display the coecents on the treatment dummy (pooling the two treatment groups), the control, and the interactions between the treatment and the control. Robust standard errors clustered by email address are in parentheses.
Signicance levels are noted as per convention: * p<.10, ** p<.05, *** p<.01. Note: This gure shows the share of non-lers that led an income tax declaration (Panel A) and the share that made an income tax payment (Panel B) for 2014 at 15 weeks after the start of the experiment, for rms with third-party information (experiment 1). The shares are displayed by ventiles of third-party reported sales for Panel A and by deciles for Panel B. The blue solid line is for the pooled treatment group and the black solid line is for the control group, with dashed lines representing the 95% condence intervals. For the 4th and 5th decile in the control group, not one observation made any payment, so the average payment rate is zero, and so is the standard deviation. Estimates are similar when calculated by bins of the maximum of self-reported sales in year t − 1 (or the most recent year available) and third-party reported sales in t.   Note: This table shows estimates from probit and OLS estimations, with dummy outcome variables as indicated by the statements in the column headings. Prots are winsorized at the rst and 99th percentile to reduce the inuence of outliers. All regressions are for the sample of rms with third-party information and include the same controls as in Table 4. Average partial eects are reported for probit estimations. Robust standard errors clustered by email address are in parentheses. TPI stands for third-party information (third-party reported sales), meaning the sum of sales reported by clients (D151), state institutions (D150) and credit/debit card companies (D153). The cutos of 2.5 million and 6 million CRC correspond to the priority group designations used by the tax authority. Signicance levels are noted as per convention: * p<.10, ** p<.05, *** p<.01. Daggers indicate signicant dierences between the two treatments.

SMS Experiment
In addition to the email experiment presented in this paper, the tax authority implemented a parallel experiment using SMS reminders. Like the email experiment, the SMS experiment targeted rms that registered for income taxes but did not le. Only rms that had a cell phone number but no email address on le were included in the SMS experiment (N = 30, 844). Firms in the email experiments did not receive SMS messages. The SMS messages were sent between March 1626, 2015around the same time as the email messages. Among the SMS-eligible rms, 16% were covered by third-party information, which we control for in our analysis.
One third of SMS-eligible rms were assigned to a control group, which received no message. that have not updated their records recently), the message content, and the delivery mechanism (email versus SMS), which has been shown to matter for compliance (Ortega and Scartascini 2015). Table A1 in this Appendix displays the balance of randomization for the SMS experiment. Table   A2 shows the balance of outcomes measured prior to the start of the experiments. These estimates are generated by regressing each row variable on a constant and two treatment indicators. Like the email experiment, the SMS experiment exhibits balance. increase the rate of income tax ling. However, the absolute and relative increase in the ling rate is smaller than the increase from an email. The SMS that threatens public shaming as a consequence of inaction increases the probability of ling more than the SMS that mentions the use of third-party information, and this dierence is signicant. Neither message results in an economically large or statistically signicant increase in average tax payment, and the overall payment rate for this group (tax-registered rms that did not have an email address on le) is below 1%. Table A4 shows other eects of the SMS messages, which also increased prior-year ling and income tax deregistration, although the eects (which are less than 1 p.p.) are again smaller than the corresponding eects from the email experiment. The threat of public shaming increased deregistration signicantly relative to the SMS that mentioned third-party information. Note: The table shows the balance of randomization in terms of rm characteristics, as measured before the experiment start. The rows correspond to the dierent variables. Column 1 displays the mean for the control group, columns 2 and 3 show the mean dierence between the control group and treatment groups 1 and 2 respectively, and column 4 reports p-values from a test of the hypothesis that the two treatment groups are jointly equal to the control group. Robust standard errors clustered by phone number are in parentheses. TPI stands for third-party information (third-party reported sales), meaning the sum of sales reported by clients (D151), state institutions (D150) and credit/debit card companies (D153). The cutos of 2.5 million and 6 million CRC correspond to the priority group designations used by the tax authority. Signicance levels are noted as per convention: * p<.10, ** p<.05, *** p<.01. Note: The table shows the balance of randomization in terms of outcomes, as measured before the experiment start. The rows correspond to the dierent variables for scal year 2014. The number of months that a taxpayer led and paid sales tax, and the sales tax payment are calculated over July 2013 until June 2014. Column 1 displays the mean for the control group, columns 2 and 3 show the mean dierence between the control group and treatment groups 1 and 2 respectively, and column 4 reports p-values from a test of the hypothesis that the two treatment groups are jointly equal to the control group. Robust standard errors clustered by phone number are in parentheses. Signicance levels are noted as per convention: * p<.10, ** p<.05, *** p<.01.
52 Note: This table displays estimates of probit, OLS and PPML estimations as explained in Section 4.1, using the control variables noted in the table rows. The columns display the outcome variables: dummies for whether the rm led income tax for 2014, reported a positive net liability and made a payment (considering only nal payments made with the declaration and not advance payments that may have been made earlier), and the (log) payment amount. All outcomes are measured 15 weeks after the start of the experiment. Robust standard errors clustered by phone number are in parentheses. Average partial eects are reported for probit and PPML. Payment amounts are winsorized at the top 0.1% to reduce the inuence of outliers. TPI stands for third-party information (third-party reported sales), meaning the sum of sales reported by clients (D151), state institutions (D150) and credit/debit card companies (D153). The cutos of 2.5 million and 6 million CRC correspond to the priority group designations used by the tax authority. Signicance levels are noted as per convention: * p<.10, ** p<.05, *** p<.01. Daggers indicate signicant dierences between the two treatments.
53 Note: This table displays estimates of probit, OLS and PPML estimations using the same controls as in Table A3. The columns display the outcome variables, which refer to compliance for scal year 2014 unless otherwise noted. All outcomes are measured 15 weeks after the start of the experiment. Robust standard errors clustered by phone number are in parentheses. Average partial eects are reported for probit and PPML. TPI stands for third-party information (third-party reported sales), meaning the sum of sales reported by clients (D151), state institutions (D150) and credit/debit card companies (D153). The cutos of 2.5 million and 6 million CRC correspond to the priority group designations used by the tax authority. Signicance levels are noted as per convention: * p<.10, ** p<.05, *** p<.01. Daggers indicate signicant dierences between the two treatments.