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MISCONDUCT AND REPUTATION UNDER
IMPERFECT INFORMATION
Francis Annan˙
University of California, Berkeley
MAY 2023
Abstract
Misconduct – market actions that are unethical and indicative of fraud – is a significant
yet poorly understood issue that underlies many economic transactions. We design a
field experiment to study the impact of two-sided anti-misconduct information programs,
which we deploy on the local markets for mobile money (Human ATMs) in Ghana. The
programs lead to large reduction in misconduct (-21pp=-72%) and as a result, broader
improvements in overall market activity, consumer welfare, and firm revenue. We show
the treatment effect is due to a combination of more accurate consumer beliefs about
misconduct and increased vendor reputation concerns.
Keywords: forensics and information (D83), vertical markets and reputation (L14,Z13),
household finance (D14, O12), consumer protection (D18), firm behavior and growth (L26,
L13)
˙UC Berkeley. e-mail: fannan@berkeley.edu. For helpful discussions and suggestions, we thank Iwan
Barankay, Arun Chandrasekhar, Pascaline Dupas, Chiara Farronato, Mariassunta Giannetti (discussant),
Xavier Gine, Paul Goldsmith-Pinkham, Marco Gonzalez-Navarro, Brett Green, Glenn Harrison, Sean Hig-
gins, Dean Karlan, Supreet Kaur, Erzo F.P. Luttmer, Isaac Mbiti, Jeffrey Perloff, Matt Shum, Sandip
Sukhtankar, Tavneet Suri (discussant), Catherine Tucker, Christopher Snyder, Christopher Udry, and sev-
eral seminar participants at Household Finance Seminar, University of Virginia Economics, University
of Pennsylvania-Wharton, Georgia State University, Michigan State University, Columbia University, UC
Berkeley, Cornell University, Dartmouth College, PEDL 2020 Conference on Firms in Low-Income Coun-
tries, CSAE Oxford 2021, BREAD 2021 Conference on Behavioral Economics and Development, NBER 2021
Economics of Digitization Meeting, BREAD 2021 Conference on the Economics of Africa, and NBER 2021
Summer Institute. We thank the NBER Development Economics Program Fall 2020 meeting participants
for their comments on an earlier draft. We are grateful to three anonymous referees and the editor for their
insightful comments. Field support from Samuel Adotevi and Kwamena Arkafra (Ghana Statistical Service)
is acknowledged. We are grateful to the World Bank for funding. The World Bank had no involvement
in any substantive aspect of the research project. Institutional Review Board (IRB) approvals for research
data collection were obtained from Georgia State University. The project was registered in the AEA RCT
Registry, ID-0003812.
I Introduction
Casual empiricism suggests that firm misconduct—failure to comply with rules/ laws/standards—is
prevalent and costly. As FORTUNE Magazine claims, “[Businesses] lie, they cheat, they
steal, and they’ve been [mostly] getting away with it too long.” (FORTUNE 2002). This
assertion is at the heart of several regulatory apparatuses designed to prevent and pun-
ish firm misconduct, with leading, recent examples in markets for digital financial services
(DFS). In 2018, the Global System for Mobile Communications (GSMA) launched a global
certification program meant to bring safer, more transparent, and resilient financial services
to millions of mobile money users around the world (GSMA 2018). Similar initiatives have
emerged at national levels to increase government oversight of financial services provision
and governance, including Ghana’s DFS Policy of 2020 and Kenya’s Payment Systems Act
of 2011. These initiatives were particularly targeted at DFS for the poor, as firms in the
marketplace recently came under serious scrutiny for issues pertaining to their conduct and
to consumer protection (Garz et al. 2021).
Despite its evident importance, there are major gaps in research on firm conduct. In
particular, the key ingredients for advancing basic and applied knowledge—mechanisms, cost
of misconduct, and, especially, negative externalities from misconduct—are often unidentified
(Zitzewitz 2012; Zinman and Zitzewitz 2016). This paper addresses these gaps in two ways.
First, we collect original data on misconduct prevalence and severity, market participant
beliefs, and firm and consumer outcomes. Second, we run a market-level field experiment,
testing scalable approaches to enriching information sets and lowering enforcement costs.
We conduct our large-scale experiment in the retail market for mobile money (M-Money).
This important financial market innovation has the potential to improve welfare and reduce
poverty (Suri and Jack 2016; BMGF 2021). Tariffs on M-Money transactions are set ex-
ante by the providers that contract with market vendors or sellers, who are not allowed to
alter these rates. Nonetheless, these markets exhibit substantial vendor misconduct (vendors
1
overcharge on over 22% of transactions), imperfect information about official tariffs (poor
consumer knowledge relative to vendors), consumer mistrust (62% of customers distrust
transacting at vendor points), and misperceived beliefs (upwardly-biased consumer beliefs)
about misconduct. These features, which we show at baseline, make M-Money a relevant
setting to study misconduct and reputation under imperfect information. Indeed, this form
of seller misconduct or overcharging in payment markets exists in many other countries like
Kenya, Uganda, and Nigeria (Blackmon, Mazer, and Warren 2021).
We construct a unique census of 130 independent, spatially-distinct local markets (local-
ities or villages) across 9 districts for M-Money between February–March 2019, as detailed
data about vendor and customer interactions are unavailable. The large number of distinct
markets allows for randomization at the market level, as well as identification of both dif-
ferentiated markets (with minimal cross-market spillovers) and spillovers therein. Markets
designate pairs of vendors and their nearby customers. We perform our experiment by ran-
domly assigning these markets to one of three anti-misconduct information programs: one
about price transparency (PT), the second about monitoring and reporting (MR), and the
third about both (PT+MR, their interaction). In the PT treatment, consumers receive rel-
evant information and training about official transaction charges. In the MR treatment,
consumers receive a toll-free number to report suspected misconduct to providers or au-
thorities. The joint treatment combines the PT and MR treatments. In all cases, vendors
are informed that customers have received such information, and the same information sets
are then given to the vendors, making our interventions two-sided. Thus, the interventions
empower consumers with technologies to enforce market vendors’ trustworthiness by relying
on social sanctions and/or punishment. For each locality, we apply the intervention to one
random vendor and nearby customers. We track additional non-treated vendors to examine
spillover effects.
We implement an audit study to measure vendor misconduct: trained auditors visit vendor
points to make actual transactions. The transaction charges are then compared to the official
2
tariffs to measure misconduct (Egan, Matvos, and Seru 2019; Annan 2020). Misconduct in
markets remains a poorly understood issue due to the empirical difficulties in measuring
it objectively. Here, we develop a procedure to cleanly measure misconduct connected to
increased transaction costs and shrouded prices. Our dataset is unique due to its size (130
random vendors and 990 customers), the expansive set of outcomes from both sides of the
market, the administrative audit measures of misconduct, market census and surveys, and
the 2 x 2 random information variation at market level. We have five set of results.
First, the intervention reduces vendor misconduct and improves consumers’ beliefs about
vendor’s honesty dramatically. Overall, the incidence of vendor misconduct decreases by -21
percentage points (pp) = -72%, while the severity of misconduct decreases by -GHS0.60 (-
$0.14) = -78%. With a control mean of GHS0.70, the latter means the intervention leads the
total fee (official charge + misconduct) to fall from about 1.70% to about 1.10%, implying a
40% reduction of typical M-Money transaction fees. Consumers’ perception of honest vendor
behavior increases (+7.0 pp = +30% overall), and, importantly, such beliefs are positively
correlated (+27 pp = +51%) with the objective audit measure of misconduct, implying
more accurate and updated consumer beliefs due to the information sets. The combined
information intervention has the greatest reduction in market vendors’ misconduct. However,
the PT-alone and MR-alone programs also have meaningful impacts on misconduct.
Second, customers meaningfully increase their use of M-Money (+10% to +45%) and their
likelihood of saving on M-Money (+7.5 pp =+12.1%) at vendor points. Third, vendors’
sales revenue increases. Overall, the information programs significantly increase vendors’
total sales (+52%). This result is consistent with the estimated consumer impact. Thus,
reducing vendor misconduct can enhance the efficiency of local markets by increasing market
activity. For context, a 45% increase in consumer demand (or 52% increase in vendors’ sales)
in response to a 40% total fee (official charge + misconduct) reduction is reasonable; it is
an elasticity of about 1.1 (or 1.3) and falls within the range of market effects from relevant
M-Money tax and subsidy policy experiments.
3
Fourth, we find significant spillover effects. Non-treated vendors located in treated local-
ities reduce their misconduct by -21 pp overall, suggesting our information programs have
market-wide behavioral impact. We estimate a 55% increase of vendors’ non-M-Money busi-
ness services revenue. Fifth, consumers in treated markets are -6.8 pp (7.6%) less likely to
experience shocks they could not financially remedy. The combined program shows larger
impacts across the various outcomes than the alternative individual information programs,
suggesting that the two individual information sets complement one another. We do not find
evidence of an impact on overall poverty levels, the number of customers, or business exits.
Why does everyone benefit from our market-level interventions? One possible explana-
tion is that vendors face a prisoner’s dilemma problem. Vendors (including other market
participants) would be collectively better offif vendors did not cheat, but there are private
benefits to deviating from a low-misconduct equilibrium, resulting in a privately profitable
high-misconduct equilibrium. In this market with significant information frictions, it might
be difficult to establish a reputation for low rates, which result in a better collective outcome.
Thus, transparency and monitoring systems that enforce a low-misconduct equilibrium could
be welfare improving. We develop a simple framework to evaluate reputation, where vendors
expect that they are more likely to be perceived by customers as irresponsible if they commit
misconduct in our experiment (Macchiavello and Morjaria 2015).
We make three main contributions to the existing literature. First, we contribute to the
literature on information and business growth in developing countries. Previous studies have
emphasized several barriers to business growth, including managerial constraints (Bloom et
al. 2013), limited network and interfirm relations (Cai and Szeidl 2017), lack of capital (De
Mel, McKenzie, and Woodruff2008), lack of market access (Atkin, Khandelwal, and Osman
2017), and asymmetric information (Jensen and Miller 2018; Bai 2019). Here, we emphasize
miscalibrated consumer beliefs about seller misconduct and vertical market structure as
potential barriers. Our market operates on a vertical structure: service providers at the
upstream set up commission-motivated vendors at the downstream who are not allowed to
4
alter rates, leading to a “version” of the well-known single versus double marginalization
problem (Tirole 1988, Chapter 4; Janssen and Shelegia 2015). The treatment pushed the
double marginalization high price (high misconduct) to a single marginalization lower price
(low to no misconduct). Thus, we show that all players on the vertical structure—providers,
vendors, and customers—can be made better offunder the single marginalization result,
which is novel and interesting.
Second, we add to the literature on forensic economics (see e.g., Olken and Pande 2012;
Zitzewitz 2012 for detailed reviews). Misconduct underlies many economic and financial
transactions (Egan, Matvos, and Seru [2019, 2022]; Annan 2020), yet the sources of such
concealed behavior are not well-understood. We emphasize how imperfect information might
exacerbate misconduct, showing in our experiment that providing symmetric information
to transacting parties raises vendor concerns for reputation. Little is known about how
reputational losses discipline business misconduct (Karpoff2012 provides a review indicating
ambiguous effects). We emphasize how local sanctions via reputation-building can promote
rural financial institutions and development in low-income settings (see Munshi 2014 for a
review).
Third, we contribute to the literature on information disclosure, household finance, and
financial technology adoption. There is much existing research on the consumer effects of
FinTech (Jack and Suri 2014; Suri and Jack 2016), but there is almost no work on supply-
side behavior (Higgins 2020). We emphasize seller misconduct as a key barrier to both sides
of the market, and show that reducing it via information disclosure has broader impacts
on consumers and businesses. We show that disclosure – transparency and monitoring –
is beneficial to retail businesses and improves sales revenue (Brown, Hossain and Morgan
2010). Moreover, we document misconduct in payment markets, which is an open—and
high-priority— area of research, particularly in developing countries,1where consumers lack
1Hasanain et al. (2023) discloses information about artificial insemination services of livestock provision to farmers in Punjab,
Pakistan, through an information clearinghouse. Unlike Hasanain et al. (2023), we (i) deploy market-level interventions and
set up a design that allows us to measure within-market spillovers; (i) have direct measures of consumers’ subjective beliefs
and objective measures of vendor misconduct, which allows us to define and evaluate belief updates, bias vs price effects, and
5
experience with FinTech (Garz et al. 2021), and higher transaction fees can act as a barrier
to the adoption of payment services (Higgins 2020), as well as reduce risk sharing across
households (Jack and Suri 2014). Our study is the first, to our knowledge, to provide
quantitative estimates of both seller misconduct in digital financial markets and the value
of anti-misconduct information programs, particularly in environments where M-Money has
the potential to reduce poverty and meaningfully improve the welfare of consumers.
From a policy perspective, our results highlight how the provision of low-cost, two-sided
information might influence vendor conduct and consumer trust, and how this might even-
tually facilitate efficient market behavior, particularly in vulnerable market environments.
This is important for setting relevant consumer protection policies. Evaluating how unin-
formed local market buyers are, and providing information about price transparency and
monitoring to both sides of the market, could potentially be used to build trust and increase
the benefits of emerging markets for digital finance.
We proceed as follows: In Section II, we describe the research setting, and in particular,
vendor misconduct within M-Money. Section III contains the description of our experimental
design and data. Section IV presents our main results. In Section V, we discuss the implica-
tions of our results, and describe the framework we use to derive our preferred interpretation
of the results. We conclude the paper with Section VI.
II Research Setting
A. Mobile Money
M-Money provides financial services that are delivered on digital mobile networks to con-
sumers. The market for M-Money comprises (i) service providers, (ii) vendors, and (iii) cus-
tomers. In Ghana, there are four providers: MTN M-Money, Vodafone VodaCash, AirtelTigo
Money, and GCB Ltd.’s G-Money. MTN has about 90% share of the market. Providers are
joint partnerships between mobile network operators (MNOs) and commercial banks. Mar-
reputation; and (iii) are able to measure broader impacts on both prices, quantities, and welfare.
6
ket vendors (or sellers) are small business retail distribution points and correspond to outlets,
shops, premises, or local banking channels. They conduct M-Money transactions on behalf
of the providers.
Vendors register new accounts (also called “wallets”) for customers and act as cash-in (de-
posits, transfers) and cash-out (withdrawals) transaction points for customers (i.e., Human
ATMs). 2Vendors can freely enter and exit the market. To establish the retail business of
M-Money, vendors must have the required documentation and meet certain structural and
monetary requirements. Vendors should have a permanent space from which to operate and
a minimum startup capital of GHS4000 ($US781.25)3, which we observe in practice can be
relaxed, depending on the environment. All vendors must undergo official business train-
ing about the tariffs, commissions, and other services. They generally earn transactional
commissions on sales revenue as their profit. In comparison, customers receive little to no
information about M-Money’s transaction tariffs and services when they sign up. The tariffs
on transactions at vendor points are set ex-ante by providers, so market vendors are not
allowed to marginalize. Thus, the M-Money setup has a vertical market structure: service
providers at the upstream set up vendors at the downstream, who work for them and earn
commissions on sales.
The introduction, and significant penetration, of digital mobile telecommunications has
provided a cheap infrastructure to make M-Money services accessible even to poor and
low-income societies. In these environments, formal financial institutions are shallow and
largely absent (see Banerjee and Duflo [2006; 2011] for authoritative surveys), making M-
Money a competitive financial option. Evidence suggests that M-Money has the potential
to reduce poverty and improve the welfare of consumers in Sub-Saharan Africa and Asia
through several channels (Jack and Suri 2014; Suri and Jack 2016; BMGF 2021). M-Money
2There is demand for vendors because users (i) are poorly informed about how to operate M-Money platform’s menu for
self-serve transactions, or (ii) have to make deposits and open new accounts, or (iii) want to avoid digital taxes and digital loan
defaults, which only apply to self-serve transactions in our setting, or/ and (iv) otherwise direct merchant payments are limited
as merchants mostly accept only cash for goods and services. As in our setting, about one-third of consumers in Tanzania,
Uganda, and Bangladesh cannot do their own M-Money transactions and tend to rely on vendors (TCI: Transaction Cost Index
2023).
3MTN Mobile Money 2021: https://mtn.com.gh/momo/agent/
7
is an important market, but could be constrained by market misconduct that shrouds prices
and increases transaction costs. Providers at the upstream have limited oversight into the
behavior of downstream vendors, and consumers in low-income environments are poorly
informed.
Similar to other banking and financial services, the business of M-Money likely faces fraud
and misconduct, which could take different forms. Indeed, vendor misconduct is widespread.
Recent surveys from Innovations for Poverty Action (IPA) compare market misconduct (over-
charging of services) in Uganda, Nigeria, and Kenya (Blackmon, Mazer, and Warren 2021):
33%, 42%, and 3% of consumers respectively reported vendor overcharging. For our exper-
imental sample, this will correspond to 22% of transactions being overcharged or subject
to unofficial fees. In policy circles, regulators from Bank of Ghana, for example, have ex-
pressed concerns about such potential market misconduct. MNOs and their commercial
partners have been asked to build more risk- and fraud-resilient financial infrastructures.4
Our present study is designed to understand misconduct at retail vendor points (see Figure
D.1 in Appendix D), as well as the effect of social sanctions and/or punishment, and to eval-
uate their potential market-wide impacts. We do this in a rural context where the business
of M-Money could have larger positive impacts, if well designed.
B. Descriptive Motivating Facts
We document several facts about our setting, and, in particular information, frictions and
vendor misconduct, drawn from a pre-experiment market census in Eastern Ghana. Detailed
vendor ◊customer data on M-Money is unavailable, so, between February and March 2019,
we carry out a census of the market for M-Money, spanning nine districts. Districts are
made up of sub-administrative units called “localities” or villages. The select localities have
a mean and median population of 3900 and 2300 people respectively as of 2018. We use
a master gazetteer of localities kept by the Ghana Statistical Service. Our census exercise
4“We also want you [Mobile Network Operators] to make your service affordable, we also want you [Mobile Network Oper-
ators] to put in place systems to minimize or eliminate fraud if possible and we also want you [Mobile Network Operators] to
give wonderful customer service to your customers as they come to your premises to transact business. We want your system
to have what it takes, to give very good audit trail of transactions.” –Bank of Ghana’s payments oversight office head Clarence
Blay, speaking at a stakeholder conference titled Expanding Cashless Payments Through Mobile Wallet Transactions, 2015.
8
successfully documents the universe of all vendor points and surrounding households (within
a five-house radius around a given vendor) across 130 localities (Figure B.1 displays the
spatial distribution). This yields a total of 333 vendors and 1,921 customers or households.
We focus on nearby households in order to maximize our chances of studying households
that might make transactions with select vendors, while also minimizing costs. We define a
local market as the pair: vendor ◊the set of all nearby customers.
We gather information about basic demographics, poverty and assets, and detailed mar-
ket records on M-Money and non-M-Money services, including general to specific knowledge
of vendors and consumers about M-Money transactions. We also obtain additional house-
hold information from customers on personal finance, shocks, and investments. Detailed
summaries are available in Annan (2020) and upon request. Table B.8 shows summary
statistics for the market. Female vendorship is 39%, meaning that these local markets are
disproportionately made up of male vendors. Of potential customers, 62% are females, and
customers are more likely than vendors to be self-employed, married, and older. The over-
whelming majority (90% [SD=0.29]) of customers, as well as their networks of close family
and friends, have registered for a M-Money account, indicating that it is likely a popular
financial technology.
We turn next to specific features of the market. With an average experience of two years
doing M-Money business, a vast majority (75% [SD=0.43]) of vendors operate as a bundled
store, bundling M-Money with other services.5The average daily sales per vendor for M-
Money is about GHS2,260 (US$442). With an official sales commission of 1%, the average
vendor will earn a daily profit of around GHS23. The majority of households use M-Money
services rather than other alternative commercial financial services: 95% of customers are
M-Money users, 80% are past formal bank users, while just 9% are post office users. This
can be explained by the convenient access and arguably lower charges of M-Money, and by
the relative inaccessibility and distance of other services. We use the census to document
5We id e ntifie d b u n dled se r v i ces inc l u d ing gro ce r i e s and pro v isio n s , l o c a l m edic i n e , mult i - T V insta l l a tion, r e g i s trat i o n o f S IM
cards, phones and accessories, airtime recharge cards, mini-credit transfers, acting as agents for land and house sales, electronics
and accessories, photocopying and typesetting, educational/online results checking, and prepaid electric credit, among others.
Baseline sales revenue from these non-M-Money services represents about 7% of the sales revenue from M-Money (Table B.8).
9
three facts that suggest information frictions matter.
Fact 1: There is high vendor misconduct, but customers misperceive misconduct.
Figure B.10 compares true versus subjective beliefs of misconduct. Our audit transactions
provide an objective (true) misconduct incidence of 22% [SD=0.41, n=663] at vendor points,
which is high. We ask customers, at baseline, whether they believe they have experienced
overcharges at vendor points (the incidence of misconduct), yielding an overall subjective
incidence of 59% [SD=0.49, n=1921]. This suggests that consumers misperceive vendor mis-
conduct (upwardly-biased consumer beliefs).
Fact 2: High asymmetric information about official prices between vendors and customers.
In a series of tests, both vendors and customers are asked to indicate the official charges for
two randomly chosen transactions of sizes GHS200 (small to medium) and GHS1200 (large).
This provides us an estimate of their knowledge about the official charges. We are careful
to inform vendors at the beginning that we are not there to perform any actual transac-
tions, but rather to assess their overall knowledge of the market. Knowledge tests are taken
towards the end of the surveys for both sets of subjects. Results are displayed in Figure
B.7, showing strong evidence of asymmetric information: vendors have superior knowledge
of official prices relative to customers. This creates opportunities for vendor misconduct.
Overall, consumers are correct 42% (median) of the time, while vendors are correct 80%
(median) of the time (an incentivized measure increases vendor accuracy to 95%, without
any change to consumer accuracy). These results are expected, because, unlike customers,
vendors receive formal training before they start their businesses.
Fact 3: Customers mistrust vendors, but vendors value good reputation.
We solicit information about customers’ level of trust in vendors when carrying out their
transactions. Figure B.9 reports the results, suggesting limited level of trust. About 62%
10
[SD=0.48, n=1275] of customers indicate distrust in transacting at vendor points, while the
rest (38% [SD=0.48, n=779]) indicate trust. We ask a random sample of vendors about
the importance of demonstrating good market reputation (or image and responsibility) to
potential customers through their market transactions. As shown in Figure B.8, the vast
majority of vendors (81% [SD=0.391]) consider good market reputation or image as impor-
tant, suggesting there is likely a positive return to vendors for good market reputation, if
they are viewed by customers as responsible, though this may be constrained by the limited
consumer trust. Vendors have poor reputation in the market, perhaps because customers
are unable to infer vendors’ behavior.
Together, our markets reflect a setting where (i) misconduct is high; (ii) consumers are
uninformed; (iii) vendors value their reputation in the market, but good reputation is diffi-
cult to establish, because consumers, not knowing official prices, cannot determine whether
vendors are being honest; and (iv) consumers underperceive the level of vendors’ honesty
(upwardly-biased beliefs about vendor misconduct). The results demonstrate that informa-
tion matters and there is room to build trust and reputational capital in the market.
But why the high misconduct at baseline? We advance 9 separate hypotheses to shed
light on why the pre-experiment market equilibrium may have so much misconduct. We
implement follow-up surveys to gather various views from both managers of the service
provider and vendors in control markets. Managers and vendors were invited to rank 9
hypotheses in order of the most plausible reason for “why vendor misconduct is prevalent
in low-income areas”. Figure B.11 shows the results, separately, for managers (n=29) and
vendors (n=58). The top 4 ranked hypotheses are (i) poorly-informed consumers about
prices and redress channels, (ii) too low vendor commissions create short-run misconduct
incentives, (iii) limited provider campaigns in rural areas, and (iv) misguided vendor beliefs
about profit-maximizing prices6. We do not aim to separate the relative importance of
the various ranked hypotheses, but the rankings are clear, robust, and preserved even with
6In section V, we explore (i) what explains the possibly misguided vendor beliefs and non-profit-maximizing prices and (ii)
why the provider’s information campaigns in rural areas are limited yet beneficial to the provider.
11
alternative scoring mechanisms. As shown, the issue of poorly-informed consumers, which in
itself can exacerbate effects from the other possible hypotheses, is very crucial, and further
demonstrates that information frictions matter. Details about the follow-up surveys with
managers and vendors are contained in Appendix D.
III Experiment: Design
Intervention and Timetable. We evaluate the impacts on both customers and vendors of
different information sets that reduce market misconduct. Our markets feature a version of
the prisoner’s dilemma problem: vendors (including other parties in the market) would be
collectively better offif vendors did not cheat, but there are private benefits to deviating
from a low-misconduct equilibrium, and they therefore end up in a privately profitable high-
misconduct equilibrium. In such a market setting, with significant information frictions, it
might be difficult to establish reputation and achieve the better collective outcome. Trans-
parency and monitoring systems that enforce a low-misconduct equilibrium could be welfare
improving, which we discuss below.
All local markets (vendor ◊customers) receive a physical research visit, and markets
assigned to treatment receive additional anti-misconduct information programs. For all
markets, we show subjects the market roster of vendors, ask them to indicate where their
last financial transactions were conducted, and provide them our research team’s contact
information for further assistance. Markets assigned to treatment additionally receive one
of the following:
•Treatment program I: Price Transparency (PT) – Addresses the question of, “what to
ask vendors while at vendor points.” It informs consumers about the official tariffs
for common local transactions, and thus improves consumer sophistication at detecting
misconduct.
12
•Treatment program II: Monitoring and Reporting (MR) – Addresses the question of,
“how to report seller misconduct.” It provides customers with a toll-free number to
report suspected misconduct to authorities, and thus raises the potential cost of mis-
conduct to vendors if caught. Punishment for vendor misconduct ranges from losing
business license, to provider warnings, and to customers not transacting at vendor
points.
•Treatment program III: Combined PT+MR – A joint program that tests the interaction
of programs I and II. See Exhibits in Appendix D for the specific information sets.
•Control program: no additional information.
We visit the assigned local markets three consecutive times over a two-month period (once
every 2-3 weeks) to first deliver and then repeat the information programs to subjects. We
conclude visits by asking subjects to summarize the information they received, and giving
them hard copies of the treatment program. We ensure that vendors are equally aware of
the interventions by communicating the same information to them, right after seeding the
information with nearby households, yielding a two-sided information design. Together, our
treatment programs aim to reduce potential information frictions and increase the social
cost of vendor misconduct. Our design mitigates against Hawthorn effects, since all markets
receive regular visits.
To roughly gauge the likely significance of the information programs, the recipients are
ex-ante asked to rate the usefulness of the information we provide for their financial decision-
making (customers) and for their businesses (vendors). We use a five-point scale: 1 (Not
useful), 2 (Quite useful), 3 (Useful), 4 (Very useful), 5 (Extremely useful). Overall, the
median value = 3 (mean=3.38, [SD=0.82]), suggesting that subjects view our information
interventions as useful, and thus likely to be ex-post effective.7Programs I (PT) and II
7In practice, our research team received around 75 different phone calls from the experimental subjects (specifically the
customers) to discuss their M-Money two to three months after the provision of the information programs. This is a costly
action (because consumers had to pay to call/ talk), represents about 9.3% of the treatment sample, and suggests that subjects
are willing to pay for our information programs, perhaps because they find the information credible. In addition, this suggests
13
(MR) are popular consumer protection policy instruments in practice (Garz et al. 2021). By
benchmarking the two programs against each other and against Program III (PT+MR), we
can evaluate their relative effectiveness in reducing market misconduct committed against
consumers, and assess whether Program I is compatible with Program II, or whether it only
becomes effective when combined with an alternative that increases the direct cost of mis-
conduct to firms. Table 1shows the timetable of all field activities.
Data Collected. We gather information from multiple sources and rounds of data collection
(Table 1): (i) combined listing and baseline market census (discussed earlier); (ii) baseline
audit study (approach discussed below); (iii) transaction networks data; (iv) 22-weeks follow-
up (phone) market survey, 33-weeks administrative audit study, and market-level transaction
data from the largest service provider, which we call an endline. The official tariffs did not
change between baseline and endline.
Administrative Audit Data. To objectively measure true misconduct, in the absence of ex-
isting credible data, we implement an audit study procedure where auditors (experimental
customers) are given cash to make actual M-Money transactions at vendor points. The
transactions (12 in total) span multiple, common transaction types: cash-in, cash-out, and
account opening.8As mentioned, tariffs on transactions are ex-ante set by the providers.
To mimic the local market context, and properly capture misconduct, we recruit and use
local residents, who are trained to follow a consistent approach to interacting with vendors,
including using uniform language, provided in a short and transparent transaction script
(Appendix D contains details).
We randomly assign the local shoppers / auditors to a unique set of vendors and multiple
transactions (the 12 different transaction types) are performed at random at each vendor
that subjects’ rating of the usefulness of the information provided is less likely affected by potential experimenter demand
(pleasing) effects (de Quidt, Haushofer, and Roth 2018).
8Importantly, these include transactions are regular in this marketplace and inherently mimic the nonlinear fee structure.
The typical fee/ tariffstructure set by providers is piecewise linear: GHS0.50 for all transaction values ÆGHS50, 1% of the
value f or tran sa ction va lues betwee n GH S50 a nd G HS1,0 00, and G HS 10 fo r al l trans ac tio n val ues Ø1,000. Similarly, the cost of
a new SIM card is GHS2.0, and registering for a new M-Money wallet is free, but requires an initial minimum account deposit
of GHS5.0. Appendix D and Table B.9 contain details.
14
point, as long as such services are available. There are instances where auditors are unable
to make certain transactions for a variety of reasons, including unavailability of network and
vendor’s insufficient liquidity (e-credit or cash). With transaction-type fixed effects, as we do
later in the empirical analysis of misconduct, such service interruptions have limited impact
on our results. About four successful trips were made per auditor per day to their assigned
vendors.
A potential concern with the audit measurement approach is that vendors cheat strangers
(like the auditors) but not local repeat customers whom they know. This is not a major
concern here, for several reasons. First, it might be more risky to cheat strangers, because
they might be more informed, which is especially true in this market context with much im-
perfect information. This reduces the possibility that vendors systematically cheat strangers.
Second, in our market environment, we estimate that a very large share of market transac-
tions are conducted with customers who are not a family member or close relation of the
vendor. Customers from our study area were shown the locality-level roster of all vendors
and asked to indicate where they last transacted and how they are related to that vendor:
8.0% of transactions were between participants who are blood-related, 22.0% were between
participants who are friends, and 70.0% were between unrelated participants. Third, we vary
the type of transactions, and auditors conduct multiple or repeat transactions at a vendor
point to mimic repeat customers. Auditors were, however, reassigned to different vendors
between the baseline and endline to prevent vendors from identifying them at endline. We
are confident that our audit-based measurement provides an unbiased estimate of the degree
of misconduct.
We implement several quality controls for the transactional exercises. First, we set up
a computer-adaptive data collection platform (called data HQ), which allows us to track
and verify the data in real time and space. Right after every visit, auditors complete a brief
questionnaire about the transaction using their tablets, out of sight of the vendors (see Table
D.1), and synchronize the data to our data HQ for immediate access and verification. The
15
GPS coordinates of all transactions are traceable. Second, we piloted the proposed audit
approach in February 2017 (as noted in the Market Census section), which yielded patterns
of misconduct similar to the main experiment. Third, we include transaction types that
are either easy or difficult for the seller to overcharge, finding consistent evidence of higher
misconduct for the easy to overcharge transactions, as discussed below. Together, these
quality controls strengthen our approach by measuring the true incidence of misconduct
(unlike other survey-based measures of misconduct; DeLiema et al. 2018), while avoiding
deception and its later effect on the market (unlike other standard audit studies; Kessler,
Low, and Sullivan 2019).
We define misconduct to entail transactions that are over-charged when compared to the
provider-approved tariffrates (as in Egan, Matvos, and Seru 2019; Annan 2020). Table B.9
and Figure B.6 show baseline results across the various transactions. We estimate that 22%
of transactions are overcharged (which reflects the incidence of misconduct), which results in
GHS3.3 (= 82% of the official tariffs) overpaid to the vendor (which reflects the severity of
misconduct). There is heterogeneity in misconduct levels across the different types of trans-
actions. Misconduct is concentrated in over-the-counter (OTC) transactions, which involve
little to no automation or active verification from the customer, and are thus more vulner-
able to vendor misconduct. Non-OTC transactions (e.g., opening a new account) are also
overcharged, but at a much lower rate. This is reassuring, and alleviates several potential
concerns, including that auditors might be over- or under- measuring misconduct.
Market Survey Data. We measure several repeated outcomes at different stages of the study.
For vendors, we measure sales revenue by soliciting transaction records for their M-Money
business and non-M-Money services (if the vendor operates a bundled store).
With customers, we restrict attention to four relevant outcomes: (i) adoption and usage
of money services: we ask whether households use money services, and if so, the transac-
tion amount involved per week; (ii) savings on M-Money: we ask whether households saved
on their money wallets within the month; (iii) specific shock experiences (such as health,
16
revenue, and household expenditures) and risk mitigation: we ask whether customers ex-
perienced unexpected shocks that they could not financially remedy, providing an objective
proxy for insurance (Dupas and Robinson 2013; Breza and Chandrasekhar 2019); and (iv)
poverty. Since our study focuses on M-Money in low-income and poor environments, we field
questions that allow us to directly examine poverty. We adapt a recently developed measure
of poverty, called the “Simple Poverty Scorecard”, that is rigorous, inexpensive, simple, and
transparent (for details, see Schreiner 2015).9
With these combined measurements, we gather data from both sides of the market, which
allows us to cross-validate the accuracy of the records. For example, one will expect increases
in household money transactions to (positively) correlate with increases in nearby vendor
sales revenue, all else equal. See Appendix D for definitions of relevant select variables.
Treatment Assignment. We use a 2◊2 factorial design, randomizing the 130 randomly se-
lected markets (as defined below) into four experimental anti-misconduct programs: PT-
alone (31 markets ©31 select vendors ◊272 nearby customers); MR-alone (32 markets ©
32 select vendors ◊257 nearby customers); combined program (35 markets ©35 select ven-
dors ◊276 nearby customers); and control program (32 markets ©32 select vendors ◊185
nearby customers). We stratify based on districts, and all misfits are resolved and randomly
assigned. Figure B.2 displays the spatial distribution of the market-level treatment assign-
ments. We identify distinct markets, which limits potential cross-market spillovers: (i) As
displayed, most localities are spatially distinct and (ii) Consumers report not switching to
use different vendors other than the nearby, local vendors.
Balance and Validity of Design. We discuss two different levels of balance. First, we focus
our study on randomly-selected markets drawn from a listing of the baseline market census.
Each of the 130 localities has one or more vendor(s) (range=1-12, average=3.3), each with
9We es t i m a te an overa l l p o ver t y rate of 1 0 . 0 %, which i s l ow b u t very cl o s e t o the offic i a l p ove r ty sta t i s tics of G h a n a that
report the rate in 2017 as 12.6% for the Eastern Region, where our study is based (GLSS 7 Report, p.19). The slight difference
(underestimate) in poverty rates may be linked to one of the following reasons: (i) our poverty measure (Shreiner 2015), which
is a shortcut, underestimates poverty, or (ii) our 5-house radius around a given vendor rule for household surveying captures
relatively richer households, or (iii) simply, time trends, since GLSS 7’s estimate was in 2017, while our estimate reflects 2019.
In addition to poverty, we examine impacts on shock mitigation by households, which are alternative poverty-relevant outcomes.
17
surrounding customers or households (range=5-47, average=20.8). To maximize statistical
power, we randomly select one vendor and their nearby customers per locality for our study.
We call this combination (selected vendor ◊nearby households) a randomly-selected market.
Sample representativeness requires that being a randomly-selected market is independent of
any relevant market-level statistics. To test that these samples are comparable to the market
population, we run the regression
ymv =–+—Smv +‘mv
on the baseline census data, where Smv =1if market pair mfrom the pairs in village vis
randomly selected in the pre-intervention period. We consider a number of different relevant
outcomes, and show that neither side of the market demonstrates any observable differences
across the two groups. Tables B.1 and B.2 report the results, where we find no difference
across those markets selected and those not selected.
Second, we base our treatment analysis on a comparison of randomly-selected local mar-
kets (m=vnow) that received the information treatments with those that did not receive
the treatments. Successful randomization of treatments, and, thus, identification, requires
that the assignments to treatments (i.e., PT-alone, MR-alone, and combined information
sets) are independent of any relevant household or market-level statistics. Similarly, to test
that these markets are comparable, we run the regression
yiv =–+—Iv+‘iv
on the baseline data, where Iv=1if local market vin district dreceives an information treat-
ment, 0 otherwise. We consider the various treatments separately and together (i.e., pooled)
for a number of different outcomes, and show that neither side of the market demonstrates
any observable differences across the two groups. Tables B.3 and B.4 report the results, pro-
viding strong evidence in favor of balance, with no difference across subjects i(households
or vendors) in assigned (treated) and non-assigned (control) markets.
18
Attrition. Table B.5 displays the breakdown of response rates and attrition between baseline
and endline. To maximize response rates at endline, trained field officers conduct multiple
phone calls (see Figure B.5) at different times of the day, varying either weekdays or week-
ends, combined with manual contact tracing for subjects with inactive phone numbers. For
the survey-based measurements (customers and vendors), we record an overall attrition rate
of 18%, which is low, given that the business of M-Money is subject to a high degree of
migration and operator turnovers. Attrition is non-differential across arms (Tables B.6 and
B.7 show tests for statistical significance by treatment arm). For our endline audit measure-
ments, 129 out of the 130 randomly selected vendors were reached, implying an attrition
rate of just 0.8%.10 We evaluate and show robustness of the main results to attrition.
IV Experiment: Results
We present and discuss the treatment effects. Since all our treatments are about informa-
tion provision, we report both the pooled (any treatment) and separate treatment effect(s)
of the information sets. We estimate treatment effects using the model
yivd =—Ivd +÷d+—0ybase,ivd +XÕ
ivd›+‘ivd
which links various endline outcome(s)11 yivd of subject (customer or vendor) iin locality
(village) vin district dto the random treatment variable(s) Ivd, district-level (stratification
unit) dummies ÷d, baseline outcomes ybase,ivd and additional vector of controls Xivd.We
include baseline outcomes primarily to increase precision and to control for potential con-
founds (if any). For the pooled effects, Ivd is a 0-1 indicator for whether a locality received
10The interventions did not lead to significant vendor exits from the local market (demonstrating limited adverse selection
effects). Rather, they reduced vendor misconduct, which is consistent with moral hazard effects (similar to Klein, Lambertz,
and Stahl 2016).
11We h ave o n e c ont i nuou s o u t come ( c o n s umer s ’ weekl y u s a ge of ser v i c es; Fig u r e B.4) with zero values. To account for this,
we report results using an inverse hyperbolic sine transformation asinh.
19
any of the information programs, and thus —captures the (pooled) treatment effect. For
the separate effects, Ivd is a 0-1 indicator for whether a locality received a specific infor-
mation program. We denote by —1,—2, and ”the separate treatment effects for PT-alone,
MR-alone, and combined information sets, respectively (i.e., —=(—1,—
2,”)Õ). We report
cluster-robust standard errors for outcomes with more than one observation per locality and
heteroskedasticity-robust standard errors when there is one observation per locality.
For robustness checks, which we relegate to Appendix C, several alternative models and
inference procedures are allowed. First, we report alternative standard errors, including the
wild bootstrap cluster-tand randomization inference. Second, to address the potential is-
sue of multiple testing, we adjust p-values for multiple testing across families of outcomes,
following the procedure presented in Romano and Wolf (2005). Third, to evaluate potential
attrition bias, we report Lee (2009) attrition bounds, Imbens and Manski (2004) confidence
sets, and Behaghel et al. (2015) attrition bounds. Fourth, in alternative models, we choose
Xivd using post-double-selection LASSO (Belloni et al. 2014).
Treatment Effects on Seller Misconduct and Consumers’ Beliefs (1)
Seller Misconduct: We ask whether the information programs reduce misconduct. Table 2
reports the pooled and separate treatment effects, and shows that the intervention meaning-
fully reduced vendor misconduct (measured using actual audit transactions). We estimate
a pooled effect of -21 pp (-72% of control mean) for misconduct incidence and -GHS0.60 for
misconduct amount (-78% of control mean). The effects are economically much larger for the
combined and MR-alone programs, however, the differences across the programs are barely
distinguishable statistically. These results strongly confirm that the information programs
are indeed anti-misconduct, yielding economically very large, and statistically significant
decreases in both incidence (occurrence) and intensity (shift in the distribution) of seller
misconduct.
Consumers’ Subjective Beliefs: We evaluate whether the information sets affected con-
sumers’ beliefs about vendor misconduct. Following Bursztyn, González, and Yanagizawa-
20
Drott (2020), we elicit perceptions about seller misconduct (or honest behavior, otherwise)
by asking customers at endline agree or disagree with the statement: “In my view, M-Money
vendors generally overcharge customer transactions at vendor points.” To incentivize the be-
liefs elicitation, we also ask consumers: “What’s your estimate of the % of others (all vendors
and customers in this locality) that will Agree (Disagree, otherwise) with this statement?”
In each local market, the respondent with the closest guess receives 10GHS (see Appendix
D). For a third measure, we also ask whether customers believe they have experienced over-
charges at vendor points, as in the baseline. The three subjective belief measures, which
reflect consumer belief in vendors’ trustworthiness, are significantly positively correlated
(p-value = 0.000).
We ask if consumers’ views about honest vendor behavior at endline shifted in the direction
of the information treatments. Table 3reports the treatment effects (Figure 1provides
graphical illustration). There is strong evidence that the intervention meaningfully increases
consumers’ perceptions of honest vendor behavior. We estimate a pooled effect of +7.0
pp (+30% of control mean; p-value = 0.095). The perceived effects appear to be much
larger for the combined program (+13 pp = +30% of control mean; p-value = 0.022). The
change in perceptions reflect the reality that treated consumers now have the technologies to
enforce vendors’ trustworthy behavior using the channels activated – social sanctions and/or
punishment. The results robustly replicate across all three measures of beliefs.
We evaluate the accuracy of consumers’ views, and whether they updated their beliefs
as a result of the information sets. We estimate a regression of perception of misconduct
(subjective) against the interactions of the treatment variables and the audit measure of
misconduct (objective) to examine how the intervention causes consumer perceptions to
more closely correlate with the audit measure of misconduct. Tables 4shows the results. We
estimate a pooled effect of +27 pp (+51% of control mean) increase in customers’ ability to
correctly guess misconduct behavior. The combined information program had economically
larger effects. These results (i) provide evidence of updated consumer beliefs i.e., increased
21
ability of customers to accurately evaluate vendor behavior, and (ii) show increased consumer
sophistication. Treated customers are significantly better calibrated (+51%) about vendor
behavior relative to the control group.
These results strongly confirm that the information programs do not only reduce seller
misconduct / prices, but also meaningfully correct consumer misperceptions and improve
knowledge about misconduct. We next evaluate the broader impacts on consumers and
businesses.
Treatment Effects on Consumers’ Use of M-Money and Savings (2)
Graphical Evidence: We provide graphical illustration of the treatment effects on con-
sumers’ use of M-Money. Figure 2plots the empirical cumulative distributions of the asinh
of total transaction amounts per week at endline by treatment status. There is strong visual
evidence of positive effects of the information programs on consumers’ transactions. This im-
plies increased usage of M-Money financial services as a result of the information programs.
The effects do not seem to be driven by specific parts of the distribution.
M-Money Usage and Savings: Table 5reports the estimated effects on usage of services
(or demand) and savings, respectively. There is increased transaction amount per week, with
a treatment effect of about +45.8%. The probability of using the financial services increased
(7.3 pp =+10.0% of control mean). The impacts are much larger for the combined program
(+54.0% increased usage), compared to the individual information sets. The results are
similar for savings likelihood on M-Money. There is evidence of an increased savings rate
by 7.5 pp (=+12.1% of control mean). Customers are significantly more likely to save on
M-Money, with much larger impacts for the combined program (13.1pp = +21.0% of control
mean compared to the individual information sets). A Wald test rejects the null that the
savings effect from the combined program is equal to effects from either the PT-alone (p-
value=0.048) or MR-alone information set (p-value=0.066).
We combine all the usage and savings outcomes (via principal component analysis (PCA)),
finding that the effects are consistently larger for the combined program (Tables C.5 and
22
C.6). This is followed by the MR-alone information set. These results indicate that the
MR-alone and PT-alone programs are informationally complementary, and that PT-alone (a
popular consumer protection instrument) may not be sufficient unless combined with ran-
dom information assignment about MR.
Treatment Effects on Business Revenues (3)
Did market vendors experience an increase in sales revenue for M-Money? If the consumer
records, and hence the estimated treatment effects, are accurate, then one might expect
direct increases in M-Money business transactions (all else being equal). Table 6reports the
estimated impacts. We find evidence for a large positive impact on revenues for M-Money
(+GHS437 = +54.9% of control mean).12 Defining business exits (or deaths) as vendors that
were unreachable and/or had inactive registered phone numbers during our endline phone
surveys, we do not find evidence for an impact on exits from the local market 13 There is
limited significant difference in treatment effects across the different information programs.
Our evidence of significant impact on revenues/ intensive margin is consistent with Brown,
Hossain, and Morgan (2010), who examined retail sellers on Yahoo and eBay, specifically in
a market setting with low transaction tariffs.
Spillover Effects (4)
In principle, all the treatment effects on the non-price and non-beliefs outcomes are
spillovers. However, the experimental design implies two specific spillover effects, which
we emphasize below.
Misconduct for Untreated Businesses: We find significant spillover effects (Table 7):
untreated vendors located in treated localities or markets reduce their misconduct (-21 pp
12To further explore the market-level effects, we solicit administrative data from the largest service provider about market
transactions that originate from localities in our study area during the endline period. A limitation of this provider’s dataset is
that it does not cover all our experimental localities and hence does not provide much variation across the separate market-level
treatment arms. However, pooling all the treatments, we find an overall increase in transaction activities in the treated markets
relative to the control markets, which is qualitatively consistent with our treatment effects on consumer and vendor outcomes
(results omitted and available upon request).
13This is consistent with the very low attrition rate (0.8%) of the audit transactional exercises that require physical visits
to the vendor. Recall that we make repeated endline calls (see Figure B.5), varying the days and time of day. In our market
environment, defining business exists as unreachable vendors seems relevant, because active vendor phone numbers are required
for the business of M-Money to be in operation. However, it is possible that businesses could simply be switching their registered
numbers, which seems unlikely: one can replace the vendor phone number at no cost if lost; obtaining a completely new vendor
number is costly and entails more paperwork.
23
pooled effect). This broader impact on vendor misconduct is consistent with misconduct
being contagious with externality effects, which is typical of vertical markets (Tirole 1988,
Chapter 4). Good vendor reputation might be difficult to build pre-experiment due to ex-
ternality effects of misconduct, when combined with imperfect information between vendors
and consumers.
Revenues for Non M-Money Services: Table 8reports the estimated impacts on stores
that also offer non-M-Money services. Meaningful positive treatment effects are reported
for non-M-Money business services (+55.4% of control mean). Total business sales, which
adds the sales revenues from both M-Money and non-M-Money services, increase (+52.4%
of control mean). The large positive impacts on non-M-Money transactions for bundled
stores suggests positive spillover effects of the information programs on overall local market
activities.14
Decreased vendor misconduct and increased demand for financial services are beneficial
to consumers; increased sales revenue from M-Money’s line of business is beneficial to service
providers; but is the average vendor better or worse off? From the audit transaction data,
we estimate an average effective price of about GHS1.70 per GHS100 transaction value
for control vendors, versus GHS1.10 per GHS100 transaction volume for treated vendors.
With a treatment effect of +GHS450 increase in M-Money services, the treatment increases
M-Money sales revenue from about GHS800 to GHS1250. Vendors earn sales commission
as profits, so the treatment changed their average profits from 1.70
100 ◊800=GHS13.60 to
1.10
100 ◊1250=GHS13.75. This implies that vendors are unaffected, which is consistent with
the estimated elasticity of around 1.0. If we account for the additional improvements in
vendors’ non-M-Money services (the positive externalities from bundling), then the average
vendor is better off.
14We d o n o t hav e indi v i d u al-l e vel dat a t o s e parat e l y l o o k at spil l ove r s o n u nt r e a ted con s u m ers (in a d d i tion to s a l e s on ve n d o rs
in treated localities). Aggregate market-level data from the largest service provider, however, show increased transaction
activities overall in the treated markets relative to the control markets. This implies a potentially positive spillover effect on
usage of services for untreated consumers/ vendors, which is also consistent with the negative spillover effects on misconduct
for untreated vendors who served untreated customers at baseline.
24
This market operates with a vertical structure: service providers at the upstream set up
vendors at the downstream who work for them and earn commissions on sales, which leads
to a version of the well-known single-versus-double marginalization problem with vendor
misconduct (Tirole 1988, Chapter 4; Janssen and Shelegia 2015). Providers have limited
visibility into the behavior of their vendors. Because service providers fix prices of transac-
tions at vendor points (price forcing to charge marginal cost), vendors cannot reduce their
sales in an attempt to marginalize. Through misconduct, vendors impose illegal mark-ups on
transactions, which results in lower sales revenue than is optimal from the viewpoint of the
provider. The treatment pushed the double-marginalization high price (high misconduct) to
a single-marginalization lower price (low to no misconduct). In this case, lowered misconduct
results in benefits not only to providers and vendors, but also to consumers. In our setting,
there are vendors who earn profits not only from the M-Money business, but also from sell-
ing other products. When the treatment leads to less misconduct, customers conduct larger
money transactions and also purchase other non-M-Money items at the vendors premises.
Thus, we show that the vendor can also be better offunder the single marginalization result,
which is a novel and interesting result.15
Treatment Effects on Shocks Mitigation (5)
Mitigation of Shocks: Revenue, Health, and Expenditure: Did customers (or house-
holds) increase their transactional services and savings likelihood in meaningful enough levels
that they are better able to mitigate unexpected shocks? Tables 9and 10 show the estimated
effects on customers’ experiences of unmitigated shocks and poverty. We report on general
shocks (any experience), and, individually, on shocks related to household revenue, health,
and household expenditures.
There is reduced instance(s) of general unexpected shocks that consumers could not fi-
nancially remedy or pay for (i.e., when resource limits bind) (-6.8 pp =-7.6% of control
mean, p-value=0.044). This effect is mainly driven by household expenditures, which has
15We t h a nk Mat t S hum for p oi n ting t h i s o u t. We n o t e , h owe ver , t h a t we do no t h ave a d i r e ct cou n terfa c t u al wher e b o t h
the upstream provider and the regulator allow double marginalization. We have an approximation that uses the fact that, by
committing misconduct, the downstream vendors impose illegal markups (in addition to the markup the upstream provider
has imposed). There are two indirect counterfactuals: (i) control vendors committing misconduct and (ii) treatment vendors
committing misconduct in the pre-experiment phase.
25
the largest significant reduction of 10.4 pp (p-value=0.080). However, bot revenue and health
sources are equally meaningful based on their effect sizes (7.2 pp and 6.1 pp, respectively).
For shock mitigation, the PT-alone and combined information programs show significantly
negative larger impacts. Effects from the MR-alone program are relatively small and in-
significant. These estimates provide a large and objective proxy for financial resilience and
insurance value of reducing seller misconduct to consumer welfare. We do not find evidence
for an impact on overall poverty levels.
V Discussions and Interpreting the Results
A Discussions
The broader improvements in consumer and business outcomes are interesting; however,
these raise three immediate questions and/ or implications.
Implication 1: Why do vendors overcharge — i.e. set higher prices — that do not neces-
sarily maximize profits but decrease total welfare? To explore this question, in a follow-up
exercise at endline, we solicit the beliefs of vendors in control markets (n=58) about prices
and then ask the vendors to predict the intervention’s likely effect on prices and quantities
(treatment effects) [à la DellaVigna and Pope 2018]. The exercise suggests that vendors
commit (unprofitable) misconduct because they perceive that a higher price is better than a
lower price. In our context, such perception is reasonable, because while vendors can predict
very well prices, which they set, they cannot predict well the effect on quantities following
a price change (i.e., they cannot predict well the price elasticity), leading them to put less
weight on quantity effects. In short, retailers seem to overcharge because of their inability
to predict well the price elasticity of demand. Details are contained in Appendix C.
Implication 2: Why did the provider not implement interventions similar to our proposed
two-sided information programs, despite the promise of improving provider revenues? To
explore this question, managers – working for the provider (n=29) – were invited to pre-
dict effects of the information interventions on prices and quantities (treatment effects) [à
la DellaVigna and Pope 2018]. Details are contained in Appendix C. Most managers were
26
systematically incorrect in their forecasts — predicting zero absolute effects for the interven-
tions. We find suggestive evidence that managers (i) were unaware that such interventions
and their specific informational contents will work and (ii) perceive the cost of information
campaigns in rural areas to be more expensive.
Implication 3: Benchmarking the Magnitude of Treatment Effects—The program impacts
on quantities are very large. For context, the typical transaction is about GHS100 (based on
the audit transactions of GHS50, GHS160 and GHS1100, which were chosen to be typical of
the market setting, Table B.9). The official fee will be 1% of this transaction value, which
implies a fee value of GHS1.0. The experiment leads the total fee (official fee + misconduct)
to fall from about 1.70% to about 1.10% (Table 2), about a 40% reduction of the trans-
action fee. The 45% increase in consumer demand (or 52% increase in vendor’s total sales
revenue) in response to a 40% fee reduction is reasonable; it is an elasticity of about 1.1
(or 1.3). Our estimated impacts are very reasonable, and fall within the range of market ef-
fects from relevant M-Money tax and subsidy policy experiments (see details in Appendix C).
B. Heterogeneity
We examine heterogeneity along five dimensions: (i) vendor competition (market conditions),
(ii) seller’s gender (market conditions), (iii) pre-experiment consumer illiteracy (compliers
of the information programs), (iv) bundled stores, and (v) beliefs update effect on consumer
outcomes (compliers of the information programs). The results and details are contained in
Appendix C. The reduction in misconduct is concentrated in localities with more compe-
tition and a high fraction of uninformed customers, as well as within vendors who bundle
services, but the effects are similar across gender. In addition, the downstream effects on
quantities are concentrated in localities where consumers significantly updated their beliefs
about vendor misconduct.
C. Interpreting the Results – A Descriptive Model of Reputation
We seek to understand what happens when we give relevant seller misconduct information to
both (potentially uninformed) consumers and (potentially dishonest and informed) vendors
27
in a local finance. One could tell several stories about how the information intervention
might act to affect misconduct and, thus, market outcomes. Our underlying hypothesis,
however, is that vendors in our experiment expect they are more likely to be perceived by
potential customers as irresponsible if they commit misconduct. Following Macchiavello and
Morjaria (2015), we define a vendor’s reputation as consumer perceptions about the vendor’s
tendency to commit misconduct (vendor’s dis/honesty). In Appendix A, we present a model
that formalizes these arguments.
To organize ideas from the model for our reputation interpretation, it is useful to define
some terms while mapping the model to our experiment. Market vendors decide whether
to commit misconduct (s=0) or not (s=1). Customers imperfectly observe the vendor’s
action s. Denote by ˆficonsumers’ imperfect belief about the probability that a vendor is
honest. Consumers (uninformed vs informed) learn about the transactional action through
public signals ‡, giving rise to a moral hazard problem (Board and Meyer-ter-Vehn 2013).
Based on their inference about a vendor’s action given the available signal, a customer either
assigns a reputational payoff(E[ˆs=1|‡]) to the vendor (via either PT or MR information
programs) or reports the vendor’s dishonest behavior as a direct punishment (via MR infor-
mation program). If customers perceive (via ˆfi) that the vendor is honest, then the vendor
receives higher revenue (i.e., through repeated or large transactions and not being reported).
Our central goal is to compare market-level information sets about misconduct: one
“without” information and another “with” information assignment about anti-misconduct.
For the information assignment, we vary the information sets: one with technology to detect
and reward misconduct behavior (reputation effects, where ‡=s), another with technology
to directly report and punish misconduct behavior (reputation and punishment effects), and
one with both. We model assignment of the anti-misconduct market information as either a
shift in the distribution of ˆfior E[ˆs=1|‡], which measures reputational concerns for sellers.
We document three pieces of evidence based on the model to show that reputation is at
play: (i) changes in consumer beliefs about misconduct, ˆfi, which we measure as the impact
28
of the information treatment on ˆfi(Table 3); (ii) updates in consumer beliefs, E[ˆs=1|‡],
which we measure as the impact of the information treatment on the correlation between ˆfi
and the audit measure of misconduct (Table 4); and (iii) the treatment effects on quanti-
ties are concentrated in markets where consumers significantly updated their beliefs about
vendor behavior (compliers of the information programs) (Table C.15). The two-sided infor-
mation programs attenuate consumer misbeliefs about misconduct and raise vendor concern
for reputation.
D. Alternative Interpretations
The information programs substantially improved consumers’ ability to infer misconduct
accurately, and to report it, while also increasing vendor reputation concerns. As a result,
prices/ misconduct decreased and quantities / consumer demand, including firm revenues
and shock-mitigation increased. However, the information interventions might also turn on
at least five other interesting alternative interpretations of the results: (i) Hawthorne effects,
(ii) selection effects, (iii) marketing effects, (iv) price and/or (v) bargaining effects. In Ap-
pendix C, we find limited support for alternative explanations. We further estimate that
about 55% of our information treatment effect is attributable to bias effect from consumers
misperceiving seller misconduct, versus 45% for price effect from price increases as a result
of seller misconduct.
E. The Value of Anti-Misconduct Information
To put our treatment effects into context, we consider the cost-effectiveness of providing
anti-misconduct information to local markets. We use a very conservative approach that
focuses on a usage of money services-only measure for customers and a sales revenue-only
measure for vendors, ignoring the broader positive impacts. We estimate a very large value
for the anti-misconduct information sets: (i) a cost-effectiveness ratio of 1:5 for consumers,
implying a per subject cost of US$4.0 for about +US$19.3 increase in usage of services; and
(ii) for vendors, a ratio of 1:21 improvement in revenue. These rough estimates compare
favorably with other financial information programs (Frisancho 2018; Kaiser et al. 2020).
29
Details are in Appendix C.
VI Conclusion
Misconduct in markets with imperfect information matters for efficiency. The provision
of information sets that deter and reduce retail vendor misconduct has broader market
impacts. Customers meaningfully increase their demand for transactional services and their
savings behavior at vendor points, which enables them to better mitigate unexpected shocks.
Businesses experience meaningful increases in their sales revenue, with limited impact on
vendor profits/ commissions, suggesting improved market efficiency.
Reputation does matter for misconduct. In rural financial environments, where markets
are subject to a high degree of imperfect information, the use of reputation as a discipline
device against market misconduct is limited. When customers do not know official and
mandated prices, they cannot observe whether they are being cheated, making it difficult
for vendors to establish a good reputation—which may increase vendor misconduct. How-
ever, reputation becomes an effective tool and disciplinary if there is a high probability that
customers will infer misconduct (Shapiro 1982, Burkhardt 2018), and if vendors can easily
demonstrate the quality of their market services. Such reputation-driven conduct is illumi-
nated drawing on features of our empirical setting and the provision of relevant market-level
information that improves subjects’ ability to report misconduct and make accurate infer-
ences about it.
Our field experiment is carefully designed to (i) reduce market vendor misconduct/ prices
through cost-effective information programs; (ii) quantify the programs’ impact on impor-
tant economic outcomes/ quantities on both sides of the market; and (iii) show that these
effects are driven by a combination of more accurate consumer beliefs about misconduct
and increased vendor concern for reputation. Our results emphasize the significance of local
sanctions to support the growth of rural financial institutions (Karpoff2012; Munshi 2014),
and provide a proof-of-concept of a potentially significant source of local financial market
30
friction, where market activities are underprovided (Jensen and Miller 2018; Bai 2019) due
to seller misconduct, which diminishes overall market efficiency.
Commerce requires reputation and/ or consumer trust, but reputation in markets might be
difficult to build, and thus low, due to imperfect information. In developing countries, where
consumers are either uninformed about FinTech or lack experience with it, and many market
digitization initiatives are underway, consumers suffer significant market misconduct, which
can lead to consumer mistrust in payment markets, act as a barrier to market activities, and
reduce households’ welfare. Our study is the first, to our knowledge, to provide quantitative
estimates on vendor misconduct and the value of anti-misconduct information programs in
payment markets, emphasizing the effect of social sanctions and punishment.
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34
Main Results for Text
Table 1: STUDY TIMELINE
DATE ACTIVITY
Part 1 February 2017 Pilot: Misconduct – Incidence, severity, and correlates (Annan 2017)
Part 2 Feb 15-Mar 20, 2019 Baseline: Market census
Aug 1- Select sample (Experiment)
Aug 15, 2019 Intervention: Information sets assignment
Sep 01-Oct 15, 2019 Audit study I (Baseline)
Part 3 Oct 15- Intervention: Information sets deployment
Dec 15, 2019
Part 4 May 15-May 30, 2020 Endline: Phone surveys + manual tracing supplement
Aug 15-Sep 01, 2020 Audit study II (Endline)
>Sep 15, 2020 Administrative data: Market transaction records from service provider
Table 2: PRICES: EFFECT OF INFORMATION SETS ON VENDOR MISCONDUCT
Misconduct indicator Misconduct amount (GHS)
(1) (2) (3) (4)
Any treatment (—)-0.211 -0.551
(0.086) (0.255)
[-0.382, -0.039] [-1.059, -0.042]
Transparency alone (—1) -0.184 -0.439
(0.094) (0.276)
[-0.372, -0.003] [-0.988, 0.110]
Monitoring alone (—2) -0.217 -0.574
(0.093) (0.275)
[-0.403, -0.030] [-1.122, -0.027]
Combined (”) -0.212 -0.554
(0.089) (0.279)
[-0.390, -0.033] [-1.110, -0.001]
Observations 335 335 335 335
Mean of dep var in control 0.294 0.294 0.778 0.778
p-value (test: —1=”)0.670 0.553
p-value (test: —2=”)0.921 0.923
p-value (test: —1=—2)0.563 0.411
p-value (test: —1+—2=”)0.108 0.204
Note: Observations are at the select vendor x transaction type x transaction date level. Dependent variables are
audit-based measures. Includes (i) randomization strata (district) x transaction type x transaction date dummies, (ii)
baseline outcomes and (iii) controls (age, marital status, ethnic group status, employment status, business experience,
and bundled store status). Cluster-robust standard errors at the vendor level are reported in parenthesis. 95%
confidence intervals are reported in brackets.
35
Table 3: CONSUMERS’ BELIEFS ABOUT VENDOR HONESTY INCREASES
Belief about vendor honesty indicator
(1) (2)
Any treatment (—)0.070
(0.040)
[-0.011, 0.145]
Transparency alone (—1) 0.107
(0.057)
[0.007, 0.221]
Monitoring alone (—2) -0.045
(0.057)
[-0.158, 0.068]
Combined (”) 0.126
(0.054)
[0.018, 0.233]
Observations 810 810
Mean of dep var in control 0.314 0.314
p-value (test: —1=”)0.747
p-value (test: —2=”)0.005
p-value (test: —1=—2)0.022
p-value (test: —1+—2=”)0.432
Note: Observations are at the customer level. Dependent variable is a survey-based measure. Includes (i) random-
ization strata (district) dummies, (ii) baseline outcomes and (iii) controls (gender, age, marital status, ethnic group
status, employment status, education, and income). Belief denotes customers’ perception that they are not being
overcharged at vendor points (or customers’ perception that they have not experienced seller misconduct) at endline.
Cluster-robust standard errors at the market (locality) level are reported in parenthesis. 95% confidence intervals are
reported in brackets.
36
Figure 1: CONSUMERS’ BELIEFS ABOUT VENDOR HONESTY IMPACTS BY TREATMENT
0
.2
.4
.6
.8
1
Cumulative Probability
0 .2 .4 .6 .8 1
Share that perceive vendors are honest
Control Any treatment
0
.2
.4
.6
.8
1
Cumulative Probability
0 .2 .4 .6 .8 1
Share that perceive vendors are honest
Control Transparency alone (PT)
0
.2
.4
.6
.8
1
Cumulative Probability
0 .2 .4 .6 .8 1
Share that perceive vendors are honest
Control Monitoring alone (MR)
0
.2
.4
.6
.8
1
Cumulative Probability
0 .2 .4 .6 .8 1
Share that perceive vendors are honest
Control Combined (PT + MR)
Note: Figure plots distributions (CDFs) of customer beliefs about honest vendor behavior at endline for the different experimental subsamples. Observations
are at the customer level. Belief denotes customers’ perception that they are not being overcharged at vendor points (or perception that they have not
experienced seller misconduct). In each local market, we compute the share of experimental customers who indicate they believe they are not experiencing
misconduct (indicating belief in honest vendor behavior) at endline. From a Kolmogorov–Smirnov test for the equality of distributions, p-value = 0.000
for all cases.
37
Table 4: BELIEF UPDATE: EFFECT OF INFORMATION SETS ON CORRECT INFERENCE ABOUT VENDOR
MISCONDUCT
Belief about vendor misconduct indicator
(1) (2)
Any treatment (—)-0.282
(0.082)
[-0.445, -0.119]
xObjective misconduct 0.273
(0.106)
[0.062, 0.483]
Transparency alone (—1) -0.365
(0.087)
[-0.537, -0.192]
xObjective misconduct (b1) 0.349
(0.122)
[0.107, 0.592]
Monitoring alone (—2) -0.152
(0.093)
[-0.338, 0.033]
xObjective misconduct (b2) 0.235
(0.121)
[-0.004, 0.475]
Combined (”) -0.354
(0.078)
[-0.510, -0.199]
xObjective misconduct (d) 0.284
(0.109)
[0.067, 0.501]
Objective misconduct -0.199 -0.216
(0.087) (0.082)
[-0.373, -0.0255] [-0.380, -0.053]
Observations 810 810
Mean of dep var in control 0.685 0.685
p-value (test: b1=d)0.586
p-value (test: b2=d)0.683
p-value (test: b1=b2