Ban Targeted Advertising? An Empirical Investigation of the Consequences for App Development

Published Online:https://doi.org/10.1287/mnsc.2023.4726

Abstract

On many multisided app platforms, the supply-side monetizes their work with targeted advertising. The targeting of ads has raised concerns over user privacy and has led to calls for platform firms and regulators to bar this practice. Important for this debate is to understand the consequences that a ban on targeted advertising would have for app development. To inform, we exploit that Google, in 2019, banned targeted advertising in Android children’s games. This setting represents an ideal real-world laboratory and permits a quasi-experimental research design. Our overall finding is that the ban on targeted advertising caused substantial app abandonment. The ban reduced the release of feature updates, particularly for games of young, undiversified, and advertisement-dependent firms. Only games of exceptionally high quality and demand showed an increase in development. Corroborating this picture, affected games were more likely to be delisted. Developers shifted their efforts toward their unaffected games and released fewer new games on average. Further tests substantiate that targeted advertising represented a crucial form of monetization for affected games and that the ban obliterated ad revenues used for app development. Our findings have several implications. To avoid a loss in app innovation, platform firms should consider implementing measures to reduce the burden on developers, especially by creating alternative monetization opportunities. Consumers and policymakers should be aware that targeted advertising plays a crucial role for app development and can use our estimates for designing policies. Thus, consumers’ demand for privacy can conflict with platform firms’ goal to foster app innovation.

This paper was accepted by Hemant Bhargava, information systems.

Supplemental Material: The data files and online appendices are available at https://doi.org/10.1287/mnsc.2023.4726.

1. Introduction

On many multisided mobile app platforms—such as Android or iOS—the supply-side monetizes their work with advertisement (hereafter ads); this is a practice that has raised questions over user privacy (Parker and Van Alstyne 2005, Sun and Zhu 2013, Acquisti et al. 2016, Kummer and Schulte 2019, Bhargava 2021).

A widespread but highly debated form of advertising is targeted advertising, which refers to tailoring ads to users based on their demographic, behavioral, and location data (AdRoll 2021). Critics have labeled targeted advertising as “surveillance advertising.” Targeted advertising would be privacy invasive and gives developers an incentive to collect extensive data about users and share it with advertising third parties, often without users being fully aware of it (Wall Street Journal 2021, Business Insider 2022). Conversely, developers argue that banning targeted advertising would deprive them of ad revenues and, in turn, of their ability and incentive to develop apps. Moreover, targeted ads would represent the only feasible monetization model that allows compensating for users’ low willingness to pay for digital products (Chellappa and Shivendu 2010, Bleier and Eisenbeiss 2015, Casadesus-Masanell and Hervas-Drane 2015, Johnson et al. 2020). In 2021, for instance, Meta chief executive officer (CEO) Zuckerberg stated that mobile app platforms’ restrictions of targeting would curtail the financial resources of developers needed to provide innovative work (De Langhe and Puntoni 2021). More recently, however, public pressure has been mounting on legislators to regulate or even ban ad targeting. For example, in 2022, U.S. President Biden told Congress: “It is time to strengthen privacy protections, ban targeted advertising to children […]” (Wired 2022). Moreover, the planned Digital Services Act of the European Union could ban ad targeting based on religious beliefs, sexual orientation, and racial origin (Fortune 2022).

In light of this debate, it is important to understand the impact that a ban on targeted advertising would have for app development. Platform owners depend on developers continuously innovating their apps, enhancing them with richer functionality, and contributing new ones (Miric and Jeppesen 2020, Janssen et al. 2021). An in-depth investigation of the extent to which a ban on targeted advertising affects app development and transparency on which kinds of apps are more and less affected is needed. Such an investigation is also needed for policy-makers to decide about the optimal level of intervention.

Thus far, however, there has been little research on this question. Research on platform management has investigated the impact of various decisions (Boudreau 2012, Huang et al. 2018, Parker and Van Alstyne 2018), but only a few studies have focused on decisions related to advertising or user privacy (Kummer and Schulte 2019, Bhargava 2021, Mayya and Viswanathan 2021). The effects of banning targeted advertising on app development have, to the best of our knowledge, received scant attention. The broader literature on the economics of privacy has investigated the immediate economic effects of regulations that enhance user privacy yet lacks detailed empirical evidence of how a ban on targeted advertising impacts app firms’ product development (Goldfarb and Tucker 2012, Acquisti et al. 2016).

We seek to contribute to the debate by investigating the app development impact of Google’s 2019 ban on targeted advertising in the market for children’s mobile games on the Android platform. In May 2019, Google banned targeted advertising for all apps in the Google Play Store directed at children (Google 2019a, TechCrunch 2019). This setting is attractive for three reasons. First, this setting embodies an ideal real-world laboratory. Google’s ban can be investigated in a quasi-experimental setup that alleviates many of the biases that would normally distort inference. The ban was, at least in part, caused by forces exogenous to the Android ecosystem; it surprised app developers and took effect within a short period of time (Google 2019a). Moreover, confounding events are relatively unlikely and time series data are available on the app-month level, which promises a unique view. Second, this setting allows investigating the effects on app development. It permits a unique view into how a ban on ad targeting impacts the development of apps, and how declines in ad revenues impact products and consumers. Finally, the market for children’s mobile games is interesting in its own right. It is estimated that two thirds of children in the United States regularly engage with mobile apps, many of which are games (Pew Research Center 2020). Children’s games are particularly monetized through advertising as children have little money in their pockets (The Atlantic 2018). At the same time, children are considered a vulnerable audience that is susceptible to ads, which therefore deserves special privacy protection (Berey and Pollay 1968, Goldberg 1990).

Our empirical strategy is a quasi-experiment, in particular, a difference-in-differences (DiD) framework (Angrist and Pischke 2009). We compare games affected by the ban to those not affected by it, before and after the announcement. To determine affected games, we exploit that Google only banned ad targeting in games directed at children (i.e., users under the age of 13). To distinguish children’s games from others, we inspect games’ so-called content rating. The purpose of content ratings is to inform parents whether a game is suitable for their child, based on an age categorization. In the Google Play Store, the content rating categories are Everyone (0+), Everyone (10+), Teen (13+), Mature (17+), and Adults Only (18+). Arguably, only games with content ratings Everyone (0+) and Everyone (10+) are directed to children and therefore were forced to end targeting ads (treatment), whereas those with higher content ratings were unaffected. To enhance comparability, we assign games to the treatment group that are just forced to comply (content rating 10+) and games just not forced to comply (content rating 13+) to the control group. To additionally reduce heterogeneity between the groups, we perform coarsened exact matching (CEM). We obtain monthly panel data on treatment and control games and their developers.

We make the following findings. First, on average, the ban on targeted advertising curbed developers’ releases of feature updates. Affected games were −16.7% less likely to receive a feature update compared with similar but unaffected games and compared with before the ban. This estimate suggests a loss of 1,685 feature updates not being released by the end of the observation period. This result accounts for game, category, and time fixed effects and remains robust to alternative quasi-experimental analyses (e.g., synthetic control group, iOS games as control group) and time windows. In line, the analyses suggest that developers also cut the release of bug fixes and of any kind of update.

Second, the ban on targeted advertising has consistently negative effects except for games of exceptionally high quality and demand (i.e., defined as those above the 90th percentile), for which we observe positive effects. This observation suggests that highly rated and demanded games benefitted from the ban perhaps due to better monetization potential or weakened competition. This result is adjusted for differences in monetization, game category, and further factors that could distort this interpretation. Considering heterogeneity along developers, we find that games of undiversified (−35.4%), young (−33.3%), and advertisement-dependent (−22.9%) developers were adversely affected.

Third, we find evidence that the decline in feature updates is induced by a drop in advertising revenues and a lack of alternative monetization opportunities. In particular, we observe that games in ad-dependent segments experience a much stronger slump: Games that had collected more personal data, that brokered data to a greater number of ad networks, and that display more ads per user showed larger declines in feature updates.

Finally, we leverage our data to investigate further app development decisions of developers. In terms of portfolio effects, affected developers relocated their development efforts. Although developers are releasing fewer feature updates for their affected games, they are releasing more feature updates for their unaffected games. This suggests that developers are shifting their efforts from the markets deprived of ad targeting to those where targeting remained permitted. Moreover, we observe that the ban increased the likelihood of a game being delisted from the Google Play Store by 10.9%. We estimate that 3,270 children’s games were delisted following the ban until the end of the observation period. In addition, we observe that the ban curbed developers’ release of new games (−36.3%). We estimate an annual loss of 65,712 games that would have been contributed to the Google Play Store if the ban would not have been implemented.

We conclude that the ban had predominantly negative implications for app development. Our findings highlight the crucial role that ad targeting plays in the market for mobile games for children and suggests that mobile platform firms face a tradeoff between user privacy and app development. Our findings inform platform firms’ decision making on ad targeting policies and contribute to the growing work on platform governance (Parker and Van Alstyne 2018, Bhargava 2021). Moreover, our results offer empirical evidence from one particular setting to inform the broader debate on the relationship of privacy and innovation (Chellappa and Shivendu 2010, Lambrecht et al. 2014, Casadesus-Masanell and Hervas-Drane 2015, Bhargava 2021).

We proceed as follows. In Section 2, we review related work, and in Section 3, we introduce the setting. Section 4 outlines the theoretical background. We describe the research design and data set construction in Section 5. In Section 6, we present the results, and in Section 7, we report robustness checks. We discuss the findings and conclusions in Section 8.

2. Related Work

This paper relates to a stream of the literature on multisided platforms (Tiwana et al. 2010, Wareham et al. 2014, Parker and Van Alstyne 2018, Bhargava 2021), especially to work focused on third-party app development. We conceptualize an app platform firstly as a system of interdependent software components that jointly, but not independently, induce end-user demand, and second as a two-sided market, with users on one side and app developers on the other (Parker and Van Alstyne 2005). For owners of such platforms, it is critical to encourage continuous app improvement and development. Only if apps are regularly updated and only if new ones are developed can the platform satisfy the changing needs of the demand side. For instance, Miric and Jeppesen (2020) outline the necessity of platforms encouraging continuous product improvement and the detrimental consequences of buggy and less polished apps. Moreover, as argued in Janssen et al. (2021), platform firms need to attract a sufficiently large number of apps to promote the emergence of “hit” products.

Prior work investigated various interventions and design decisions for promoting app development, including competition (Boudreau 2012, Huang et al. 2013, Foerderer et al. 2018, Zhu and Liu 2018), intellectual property rights (Ceccagnoli et al. 2012), seeding (Huang et al. 2018), and interfirm exchange (Foerderer 2020). The gap that we address is to understand the consequences of enforcing stricter user privacy, in particular by regulating the use of ad targeting. Closest in this regard are the following studies. Kummer and Schulte (2019) report that developers on the Android platform offer greater privacy in their apps in return for charging an upfront price. Al-Natour et al. (2020) suggest that users’ uncertainty about privacy in an app can reduce their intention to use an app. Mayya and Viswanathan (2021) find that Android app developers strategically avoid stricter privacy regimes. Sokol and Zhu (2021) analyze Apple’s iOS14 update that requires developers to obtain users’ consent for tracking. They argue that the now required explicit opt-in decimates the ad revenues of developers. Moreover, it should shift market power toward Apple because the platform now benefits from a greater adoption of paid monetization models and decreasing competition for its own services.

Our study also relates to research that investigates the monetization of digital goods (Sun and Zhu 2013, Kraemer et al. 2019, Bhargava et al. 2020, Bhargava 2021, Yan et al. 2022), in particular work on targeted ads (Chellappa and Shivendu 2010, Lambrecht et al. 2014, Casadesus-Masanell and Hervas-Drane 2015, Grewal et al. 2016). Several empirical papers have outlined the importance of targeting for ad effectiveness as inferred from click-through rates, purchase intent, and conversion (Manchanda et al. 2006; Goldfarb and Tucker 2011a, b; Ghose and Todri-Adamopoulos 2016; Rafieian and Yoganarasimhan 2021). Other studies have documented how the effectiveness differs depending on ad attributes (Lambrecht and Tucker 2013, Bleier and Eisenbeiss 2015). However, it remains to be understood how the availability (or ban) of ad targeting influences product development.

Given that we study firms’ product development decisions, our study is also related to the innovation management literature, especially the streams of work that examine the innovation process and the determinants of innovation (Wolfe 1994, Hauser et al. 2006, Ahuja et al. 2008). Our focus is on product innovation as opposed to process and technological (Sood et al. 2012), and on exploitative or incremental forms, as opposed to explorative (Jansen et al. 2006) or radical ones (Crossan and Apaydin 2010). Prior work has yielded various determinants of product innovation, including resources in terms of creativity (Woodman et al. 1993), human capital (Faems and Subramanian 2013, Wang and Zatzick 2019), and slack (Damanpour 1991); organizational attributes such as specialization (Crossan and Apaydin 2010); and management decisions regarding resource allocation (Klingebiel and Rammer 2014), external research and development (R&D) (Cassiman and Veugelers 2006), and openness (Laursen and Salter 2006). However, this research has yet to fully address the question of how a ban on ad targeting affects the behavior of firms that use customer data as an indirect (i.e., as a profit source) input factor for innovation.

From a broader perspective, given that online advertisement represents the commercial exploitation of consumer data (Posner 1981, Taylor 2004), our study is informed by an extensive literature on the economics of privacy in information systems, management, and marketing (for a survey of the literature, see Acquisti et al. 2016). Our study addresses the gap that the effects of users’ privacy concerns for firms’ product development decisions have primarily been addressed using theoretical methods (Campbell et al. 2015, Casadesus-Masanell and Hervas-Drane 2015). Although various privacy-induced policy changes have been studied, these tend to be ones that are government imposed (Miller and Tucker 2018), whereas the one we study is implemented by a platform. With any investigation of privacy’s consequences being highly specific in terms of what is being regulated and affected (Acquisti et al. 2016), our study can provide a data point from a relevant form of privacy, namely the ban on ad targeting, and an important affected product market, namely mobile games for children.

3. Empirical Setting

3.1. Android Games for Children and Advertisement

Android is a major platform for the development and distribution of mobile games. As of 2021, thousands of firms (“developers”) have developed mobile games and offered them on the Google Play Store marketplace. As of 2022, mobile games accounted for almost half of video gaming revenues worldwide, estimated at $91 billion (Statista 2022). Children (i.e., persons below the age of 13) use mobile devices to engage in a range of activities, including gaming. It is estimated that approximately two thirds of children in the United States regularly engage with mobile devices, and playing games is a major reason for use (Pew Research Center 2020). According to estimates, children spend on average more than three hours each day on mobile devices (The Telegraph 2019). Even among the youngest children under 8, approximately 42% possess a device (Rideout 2017). This makes children an important user group.

Android mobile games are largely monetized via advertising, which implies the display of banner or video ads during use. As of February 2021, 96% of apps in the Google Play Store can be downloaded for free (AppBrain 2021). For app developers, several reasons make advertising an essential revenue source. First, digital goods such as apps are experience goods, which makes it difficult to charge upfront prices. Second, they are nonrival and incur negligible marginal costs of production and distribution, facilitating freemium business models (Shapiro et al. 1998). Third, moving from price zero—a psychologically special price—to small upfront prices can cause a discontinuous decline in demand. Fourth, users of digital goods spend time when using them, allowing app developers and content providers to sell “eyeballs” in the form of advertisement space (Lambrecht et al. 2014, p. 336). It is therefore not surprising that 47% of developers obtain revenues from advertisement, and for 28%, it is the most important source of revenues (Statista 2019a).

Among the different forms of mobile advertisement, targeted advertising typically yields the highest compensation (Bleier and Eisenbeiss 2015). To deploy targeted ads, developers collect user data such as device identifiers, location, or clickstreams and transmit this data to ad networks, which match the user data received from a game with other data they already have on that very user, for instance from other apps (Lambrecht and Tucker 2013, Grewal et al. 2016). Examples of ad networks are Google AdMob, Facebook Audience Network, and Unity Ads.

Children have become a major segment of the online advertising industry. Although children’s games represent a large share of app downloads, they generate comparably little revenue from in-app-purchases compared with other genres (Barton 2019). With $1.2 billion spent in 2019, around one third of total expenditures, advertisers that want to reach children allocated a considerable portion of their budgets to digital channels, which previously almost exclusively went into nondigital channels (Statista 2019b). Because of children’s use of smartphones rather than computers, advertisers buy advertising inventory in the mobile subsegment when they want to reach children.

Children’s privacy in mobile games is regulated by, among others, the Children’s Online Privacy Protection Act (COPPA), a U.S. federal law (U.S.C. §§6501-6506). COPPA is applicable to any online service that knowingly collects personal information from children or that is directed at children. It mandates that firms must obtain parental consent when they collect personal information of children, thereby giving parents control over their children’s data sharing online. COPPA came into effect in 2000 and was amended in 2013 (Federal Trade Commission 2022).

3.2. Google’s Ban on Targeted Ads to Children

In December 2018, a consumer protection group, which included the Center for Digital Democracy and the Campaign for a Commercial-Free Childhood, filed an FTC complaint against Google. The complaint alleged that apps in the Google Play Store had violated COPPA. Subsequently, the Federal Trade Commission (FTC) launched an investigation. On May 29, 2019, Google announced new privacy requirements for app developers (Online Appendix Figure B1 shows the announcement; Google 2019a). Google required all developers to determine the audience of their apps. If an app was partially or fully directed to children, it had to comply with the new rules. Only if an app was not appealing and not used by children, it was excluded from the ban. To support the assessment, developers had to provide information about the content and audience of their app. All apps that target children now had to comply with the so-called Family Policy Requirements (Online Appendix Figure B2 shows the new rules; Google 2019b). The Family Policy Requirements forbid the collection of personally identifiable data from child users and explicitly ban targeted advertising—also referred to as personalized ads, interest-based advertising, and remarketing—to child users. Any advertising must be catered through a set of certified ad networks.

Google’s decision went beyond COPPA. Whereas COPPA permits ad targeting provided there is parental consent, Google banned ad targeting entirely. The new rules became effective three months later, on September 1, 2019. Online Appendix A1 provides a timeline.

Several reasons make this setting a unique real-world laboratory to investigate our research question. First, the ban can be considered as a plausibly unanticipated exogenous shock to developers. Even further, the ban was unlikely a fully deliberate choice by Google. Some media sources speculated that the move was done to forestall FTC charges and to respond to competitor Apple’s move toward greater user privacy (TechCrunch 2019, 2020b). Second, the setting is well suited for reasons of observability. Because the time between announcement and enforcement was only three months, developers were forced to take immediate action. This permits defining sharp bounds for the observation periods; it also helps ruling out confounding events. Finally, the context provides rich data. It allows many decisions of developers to be observed, including rolling out app updates as well as changes in pricing or data collection.

4. Theoretical Background

On average, the ban on targeted advertising is likely to curb app developers’ revenues. Targeted advertising is more profitable than nontargeted advertising because it is more effective in matching products to consumers and evoking user interest and clicks (Chandra 2009, Bergemann and Bonatti 2011, Bleier and Eisenbeiss 2015, Rafieian and Yoganarasimhan 2021). Ad networks tend to pay greater compensation if ads can be targeted, and revenues of firms that target ads are estimated to be higher. Even though a revenue increase is not guaranteed, in some cases the revenue even doubles when targeted advertising is used (Chen and Stallaert 2014). Goldfarb and Tucker (2011a) find that the Privacy and Electronic Communications Directive 2002 (ePrivacy Directive), which restricted websites’ use of cookies for targeting, reduced consumers’ purchase intent for advertised products. Johnson et al. (2020) suggest that opt-out advertisements without tracking yield less revenue compared with targeted advertisements.

The loss of ad revenues will entail app abandonment. First, given game developers’ reliance on ad revenues, a loss would reduce the financial means available for product development. Developing games is costly, especially as they represent a complex combination of code, animation, texture, and sound elements (Anderson et al. 2014, Cennamo et al. 2018). Development implies fees for development kits and game engines; the purchase of hardware equipment; licensing intellectual property rights for characters or stylistic elements; and salaries of software developers, artists, audio engineers, and voice actors. In addition, a loss in financial resources is also likely to reduce slack resources for development. The innovation management literature documents that firms use slack resources to fund more risky product innovations (Singh 1986, Damanpour 1991, Gibbert et al. 2014). As slack resources decline, it is likely that the riskier game improvements, especially the development of new features, levels, or characters, are halted.

Second, reduced ad revenues decrease firms’ incentives to invest in their games; for example, they will lose their financial incentive to advance or improve their games. In line, Sun and Zhu (2013) find that web bloggers provide content of higher quality if there are opportunities to generate revenues via advertisement. Bhargava (2021) models the quantity of content provided by creators as a linear function of the share of ad revenue net the costs of the provided content, assuming that the ad revenue is creators’ primary motive for publishing their content. In turn, if stricter privacy leads to a loss in ad revenues, developers’ incentive for enhancing their games is compromised.

At the same time, it is difficult for developers to compensate a drop in ad revenues. To counteract, increasing the quantity of ads unlikely is a viable option. There are technical limitations on the total number of ads that an ad network shows per user or within a time period (Google AdMob 2022). Moreover, users have a distaste for excessive ads (Zhang and Sarvary 2015, Aseri et al. 2020); thus, including more ads might alienate users. Another counteraction could be to switch from an ad-based toward a paid monetization model (Voigt and Hinz 2016, Rusell et al. 2020). However, this is challenging and risky. The literature outlines the importance of advertising revenues for digital experience goods such as apps (Lambrecht et al. 2014). Moving from free to paid can curb demand substantially (Ghose and Han 2014, Oh et al. 2016, Bond et al. 2019).

A decline in development might not be the case for all games and several boundary conditions are plausible. Regarding game characteristics, we expect that well-rated games and those with a large user base are likely to be less impacted by the ban. For developers of well-rated games, the ban represents an opportunity to monetize with upfront prices or in-app purchase elements. Consumers might trust well-rated games more and be willing to pay a price for them (Ghose and Han 2014, Kummer and Schulte 2019). For games in high demand, there is the opportunity to still make considerable ad revenues from their existing user base. Additionally, in the case of games with a significant number of users, even if only a small percentage of those users are willing to pay for the game, the revenue generated may still be substantial enough to support its development. App markets are also characterized by a high degree of rivalry (Ghose and Han 2014, Wang et al. 2018). The ban might crowd out many games, thus enhancing visibility and reducing competition for highly rated and high-demand games. Regarding firm characteristics, we expect that games of undiversified and young developers will be most adversely affected. The model of Campbell et al. (2015) predicts that if advertising-supported firms are required to obtain informed consent to collect consumer data and cannot increase prices, young firms as well as those with a small scope of services might even exit the market entirely. For such firms, the adaptation of the business models to stricter privacy regimes is challenging because they tend to have fewer slack resources (Brekke et al. 2006).

5. Method and Data

5.1. Research Design

Figure 1 illustrates the research design. We embed the ban on targeted advertising in a quasi-experimental DiD analysis (Angrist and Pischke 2009). Our primary analysis is on the game level. To estimate the effect of the ban, we compare the outcomes of games affected by the new rules to those of games not affected, accounting for their pre-existing difference. To identify which games are affected, we rely on their content ratings. The purpose of content ratings is to inform parents whether a game is suitable for their children. In the Google Play Store for the United States, content ratings are derived from the categorization of the Entertainment Software Rating Board (ESRB), which distinguishes between “Everyone” (i.e., for all ages); “Everyone 10+” (i.e., age 10 and above); “Teen 13+” (i.e., age 13 and above); “Mature 17+” (i.e., age 17 and above); and “Adults Only” (i.e., age 18 and above). Assigned by Google in a questionnaire-based multistage review process, each game must have a content rating. Content ratings differ, among other factors, on the level of violence and explicit word use in a game. Online Appendix A2 describes the ESRB ratings and shows examples.

Figure 1. Research Design
Note. This figure illustrates the quasi-experimental research design of our study.

Games are affected by the ban if their content rating is “Everyone” or “Everyone 10+.” We assign games to the treatment group if they have a content rating just below the child threshold of 13 years (i.e., “Everyone 10+”) and to the control group if they have a content rating just above the cutoff (i.e., “Teen 13+”). Through this strategy, we ensure that the groups cater to similar users but differ as to whether they are affected by the ban.

One design choice is the definition of the pre- and postperiods. Google made the announcement on May 29, 2019 (i.e., the announcement date), but developers were given until September 1, 2019 (i.e., the enforcement date), to become compliant. We use the announcement date to define the pre- and postperiods to capture developers’ immediate reactions. The observation period begins in June 2018, one year before the policy change, and ends in March 2020, 10 months after the policy change. We decided on this observation period because it provides sufficient data to assess pretrends but also avoids capturing confounding effects of a further privacy-related platform change in April 2020.

5.2. Data Collection and Sample

We obtained a proprietary data set from the app analytics provider AppMonsta that contains weekly snapshots (“index”) of all apps in the Google Play Store along with their characteristics (e.g., prices, ratings). The starting point for the construction of the sample is the index from May 27, 2019 (i.e., two days before the announcement). Of the total 2,981,709 apps, 413,899 are games. Following our identification strategy, we exclude all games with content ratings other than “Everyone 10+” and “Teen 13+,” dropping 353,897 games. The Google Play Store has been criticized for containing games that are not downloaded at all, have been abandoned, are maintained by nonprofessionals (e.g., hobbyists or amateurs), or are copycats. These games can create noise for estimation. To overcome, we drop games that fulfill at least one of the following criteria at this point in time: no update in the 1.5 years preceding the observation period; fewer than 25 (50) ratings for games older than 6 (12) months. The remaining games total 27,929.

Data on the use of advertisement in games comes from Apkmonk. From there, we obtain each game’s so-called “manifest”—metadata about the advertising networks and data permissions used by a game.1 This restricts the sample to 25,130 games that use advertisements or collect personal data. To ensure that these games are not already compliant, we drop 85 games that were advertised in the Google Play Store as being compliant with the Family Policy Requirements before the announcement. Importantly, to avoid capturing anticipation and selection effects, we drop games whose content rating was switched during the six months before the announcement. In a final step, we dismiss 5,509 non-English games and remove 64 with missing values. Online Appendix A3 provides details on the data sources and data set construction.

5.3. Variables

5.3.1. Dependent Variables.

Our primary dependent variable are so-called feature updates of a game. Feature updates, in contrast to bug fixes or other kinds of updates, deliver new content, features, characters, levels, and modes of play, extending games with richer functionality. To measure feature updates and distinguish them from other types of updates (e.g., patches, bug fixes), we text-analyze the update descriptions that developers publish with their updates. The Google Play Store displays the update description in a section titled “What’s New.” Update descriptions are limited to 500 characters. For classification, we rely on a dictionary-based approach (Bao and Datta 2014). This approach classifies a document based on the occurrence of keywords for topics of interest. We construct a dictionary by tabulating the frequency of words in a sample of update descriptions. The resulting dictionary contains the words “new,” “added,” “upgrade,” and “major.” An update is classified as feature update if it contains at least one of the dictionary words. To validate the classifier, two independent research assistants coded 100 changelogs manually. The manual coding matched the dictionary-based coding in 94 of the 100 cases. The resulting variable is Feature Update, which is one if game i received a feature update in month t. For robustness checks, we create the variable Update, which is one if game i received any type of update in month t. In addition, Bug Fix takes the value of one if a game i experienced an update in month t with an update description that contains at least one of the words “bug,” “minor,” “crash,” or “error.”

We assess development outcomes by two further dimensions. First, we consider the market exit of a game. We create the variable Discontinued, which is one if game i was no longer listed in the Google Play Store at the end of the observation period. This variable may capture removals of apps by Google (e.g., because of rule violations). This is a limitation of the measure; however, regardless of how an app is removed from the Google Play Store, any delisting of a game informs about app abandonment. Second, on the developer level, we measure new game releases. New Game is one if developer j released a new game in month t and otherwise is zero.

5.3.2. Independent Variables.

The DiD framework relies on two indicator variables: one for the treatment assignment and one for the months after the treatment. The treatment indicator variable is Treat, which takes the value of one if game i is affected by the policy change as previously defined. The postannouncement indicator is After, which takes the value of one in the months after the announcement of the policy change.

5.3.3. Further Variables (Heterogeneity, Controls, and Mechanism).

We create several additional variables that capture game-specific characteristics. As a proxy for game quality and in line with prior research (Zhu and Iansiti 2012, Wang et al. 2018, Miric and Jeppesen 2020), RATING is the average user rating of game i, on a scale ranging from one to five. We create the binary TOP RATING, which is one if game i is above the 90th percentile of RATING. Given that precise download data are not available, we use the number of user reviews of game i as a proxy for its demand, stored in Demand (Yin et al. 2014, Foerderer 2020). We log the variable to account for skewness. Top Demand is one if game i is above the 90th percentile of Demand. Age is the number of days since the release of game i for each t. Category holds the genre of a game. To avoid issues of too little within-group variation, we aggregate the Google Play Store category (e.g., action, arcade, racing) into 11 different genres based on their semantic similarity. We also measure the degree of data collection. PERMISSIONS is a count of the total permissions requested by game i for the collection of user data (Kummer and Schulte 2019, Mayya and Viswanathan 2021).

We create further variables that capture the intensity of ad usage in the games. User-identifying information is a key input for targeted advertising; therefore, a measure for advertising dependency is whether a game collects personally identifiable information from its users. Collector User ID is one if a game required at least one of the following permissions from users before the policy change: Read_Phone_Status_And_Identity, Approximate_ Location, or Precise_Location. These permissions are privacy sensitive and nonessential for game functionality, but their purpose is to enable targeted ads (Kummer and Schulte 2019, Adjust 2021, Mayya and Viswanathan 2021). Next, we infer advertising dependency from the number of ad networks to which a game connects. Ad networks auction the ad space in a game among advertisers. Technically, games provide ad networks with data on their users, and in return are provided with the ad to display as well as compensation (Lambrecht and Tucker 2013, Appodeal 2021). Ad Networks counts the number of ad networks to which a game is connected.

Moreover, we proxy for advertising dependency using data on the so-called ad impressions (i.e., the average number of ads viewed by users daily) on the category level. Ad views capture the frequency and thus the intensity of advertising. The higher the number of ad views, the more ads are displayed to users (Casadesus-Masanell and Zhu 2010, Zhang and Sarvary 2015). Data on ad views are not available on the game level because developers do typically not disclose this information. For this reason, data on ad views are only available at the level of the category. We obtain ad views data as average views per day per user in each category in 2019 from the “Mobile Game Monetization Report” (Irpan et al. 2020). The report provides the ad views on a per user basis, that is, indicating how many ads are displayed per user, on average, which helps account for category-specific differences in the user base. The resulting variable Ad Views takes the value of one if game i was in a category with above median ad views per user before the policy change.2

Further variables describe the game developer. Firm Size is developer j’s number of apps published in the Google Play Store. We log the variable to adjust for skewness. One-Employee is an indicator variable that is one if game i’s developer is an individual instead of a legal entity, which we determined by inspecting the developer’s name for legal entities such as “Inc.” Young is an indicator that takes the value of one if the age of game i’s developer j is below the median. Undiversified is an indicator that takes the value of one if all the games of the portfolio of game i’s developer j are affected by the policy change. Charges Price is an indicator that takes the value of one if the developer j of game i charges an upfront price for at least one of its games.

Table 1 describes the sample.3

Table

Table 1. Summary Statistics

Table 1. Summary Statistics

VariableDescriptionMeanStandard deviationMinimumMedianMaximum
Feature UpdateOne if game i received a feature update in month t, else zero0.030.17001
Feature UpdatesCumulative count of feature updates in month t since the first month observed for game i0.571.590018
UpdateOne if game i was updated in month t, else zero0.140.35001
Bug FixOne if game i received a bug fix update in month t, else zero0.040.20001
DiscontinuedOne if game i is not listed in the Google Play Store at the end of the observation period, else zero0.260.44001
New GameOne if developer j released a new game in month t, else zero0.140.34001
RatingAverage user rating for game i in month t4.060.521.004.105.00
Top RatedOne if game i is above the 90th percentile of rating, else zero0.300.46001
DemandNumber of total user reviews of game i in month t (in thousands)22.81141.2200.626690.72
Top DemandedOne if game i is above the 90th percentile of demand, else zero0.260.44001
AgeAge of game i in month t in number of days since release696.62613.6914893,639
PriceOne if game i charges an upfront price in month t, else zero0.000.070.000.001.00
File SizeSize (in megabytes) of game i in month t46.2324.441.0043.00185.00
PermissionsNumber of requested data permissions of game i in month t6.734.041633
Collects User IDOne if game i requests one of the permissions: Read_Phone_Status_And_Identity, Approximate_Location, Precise_Location, else zero0.360.48001
Firm SizeNumber of games of developer j in month t30.3580.491111,392
One-EmployeeOne if developer j is an individual, else zero0.860.35011
YoungOne if age of developer j is below the median age of developers, else zero0.500.50011
UndiversifiedOne if all games of developer j are affected by the policy change, else zero0.190.39001
Charges PriceOne if developer j charges an upfront price for at least one game, else zero0.160.36001
Ad NetworksNumber of ad networks to which game i is connecting3.083.170218
Ad ViewsAverage number of ad views per user and per day of game i, specified by app category3.610.193.273.553.99
Category (%)
Action and Racing28.46Casual8.26
Adventure and Strategy17.48Educational0.32
Arcade10.18Role Playing and Simulation26.07
Board and Puzzle4.97Sports2.09
Card0.70Other1.41
Casino0.07


Note. The table summarizes the full sample (N = 99,714).

5.4. Matching

To reduce preban heterogeneity between groups regarding game characteristics and to balance group size, we use coarsened exact matching (Iacus et al. 2012). The matching variables are as follows: We match on Category because we expect that games require different development efforts and have different consumer demands depending on their type (Rietveld and Eggers 2018). In addition, we match on Log(Demand) to account for differences in consumer feedback and demand (Ghose and Han 2014). We also match on Log(Price) to adjust for differences in monetization (Kummer and Schulte 2019). Furthermore, we match on Age to account for a game’s product lifecycle (Boudreau 2012). We also match on File Size to account for differences in maintenance and operations costs (Ghose and Han 2014). Last, we match on the outcome variable (i.e., Feature Update) to reduce the risk of preannouncement imbalance and differences in trends. We do not match on Young because we match on Age, which is more precise information. In addition, we cannot match on Undiversified because—by definition—this indicator is only defined within the treatment group (i.e., it is zero by definition for all control games because the control group only contains developers who have games unaffected by the ban). We match based on the variables’ average values over the six months before the announcement (Sun and Zhu 2013). Regarding the cutoff points, we follow the recommendation to choose coarsening values based on “knowledge of the measurement scale of each variable” (Iacus et al. 2012, p. 9). We enforce k-to-k (k2k) matching to obtain balanced group sizes. The final sample consists of 5,834 games, of which 2,917 games reside in the treatment group and 2,917 in the control group. The panel comprises an effective total of 93,881 game-months. The panel is unbalanced because we allow games to enter and exit the sample in the different time periods and because we do not observe every game in every month due to data availability. Coverage is high: On average, we observe a game in 17 of the 22 total months.

6. Results

6.1. Average Effects of the Ban on Feature Updates

6.1.1. Main Model.

We estimate the effects of the policy change on the roll out of feature updates using a fixed effects DiD framework (Angrist and Pischke 2009):

Feature Updatei,t=β0+β1Treati×Aftert+ψi+ϕt+φi,t+εi,t,(1)
where Feature Updatei,t is the dependent variable of interest in month t for game i, ϕt are month (i.e., time) fixed effects, which absorb the term After, and ψi are game fixed effects, which absorb the term Treat. We include game level and month fixed effects to account for time-invariant heterogeneity within games and time-varying heterogeneity constant across games. The vector φi,t contains the following controls: We control for Category because different game types incur different development efforts and are situated in different markets (Rietveld and Eggers 2018). We control for Demand to account for differences in consumer feedback and demand (Ghose and Han 2014). We also include Price to account for differences in monetization (Kummer and Schulte 2019). Moreover, we adjust for a game’s product lifecycle by controlling for Age (Boudreau 2012). We also consider differences in developer characteristics by adding Firm Size and One Employee as control variables (Foerderer 2020). We do not control for Rating and Permissions because they could directly be affected by the ban and thus could be considered “bad controls,” in terms of variables that “might just as well be dependent variables too” (Angrist and Pischke 2009, p. 64). The coefficient of interest is β1, which gives the DiD. We use heteroscedasticity-robust standard errors clustered on games to account for potential serial correlation and heteroscedasticity in the residuals (Bertrand et al. 2004). Given that a logit estimation can be problematic in the presence of the interaction term and fixed effects, we follow the recommendations and use Ordinary Least Squares (OLS) for estimation. In particular, simulations indicate that the incidental parameters bias can be substantial in fixed effects models when the number of observations per group is small (Greene 2004, p. 690). The conclusions of Greene (2004) were based on panels with a length between 2 to 20 periods, similar to ours.

Table 2 summarizes the estimates. Column (1) is the baseline, regressing Feature Update on the DiD term, as well as game, time, and category fixed effects. We find a statistically significant negative coefficient on Treat × After. On average, the policy reduced games’ likelihood of experiencing a feature update by −0.8 percentage points. To interpret the effect, we use a marginal probability approach (Gallino et al. 2017, p. 2821): relating the DiD coefficient of 0.008 × 100 = 0.8 percentage points to the baseline average marginal probability over the prepolicy period (i.e., 4.8%) suggests a −16.7% decline in the likelihood of a feature update. Column (2) adds controls, and we obtain consistent results (−16.7%). Column (3) adds a one-month lag of Feature Update to adjust for potential serial correlation, and the estimate is consistent in magnitude and significance (−16.7%).4 Figure 2 plots the marginal probabilities of Feature Update for both groups over time.

Figure 2. Marginal Probability of Feature Update over Time
Notes. This figure illustrates the marginal probability of Feature Update for treated (solid) and control (dashed) games over time as estimated by a fixed effects linear probability estimator. The figure includes the 95% confidence interval of the marginal probabilities.
Table

Table 2. Effect on Feature Updates

Table 2. Effect on Feature Updates

EstimatorDependent variable = Feature Update
(1)(2)(3)
BaselineBaseline + controlsBaseline + lagged DV
LPMLPMLPM
Treat × After−0.008**−0.008**−0.008**
(0.003)(0.003)(0.003)
Controls
 Log(Demand)−0.008**−0.009***
(0.003)(0.003)
 Age0.0000.000
(0.000)(0.000)
 Price0.0480.048
(0.041)(0.040)
 Log(Firm size)−0.014***−0.014***
(0.003)(0.003)
 One Employee−0.002−0.002
(0.010)(0.010)
 Feature Updatet-10.005
(0.009)
Category
 Adventure and  strategy0.0230.0250.025
(0.021)(0.021)(0.021)
 Arcade0.0020.0020.002
(0.027)(0.027)(0.026)
 Board and puzzle−0.015−0.016−0.016
(0.028)(0.028)(0.028)
 Card0.3700.3670.366
(0.200)(0.199)(0.199)
 Casino0.0200.0230.023
(0.034)(0.034)(0.034)
 Casual0.0350.0380.038
(0.026)(0.026)(0.026)
 Educational−0.011−0.006−0.006
(0.043)(0.043)(0.043)
 Role playing  and simulation−0.014−0.013−0.013
(0.015)(0.015)(0.015)
 Sports−0.022−0.016−0.016
(0.011)(0.013)(0.012)
 Other−0.013−0.012−0.012
(0.012)(0.012)(0.012)
Effect size (in %)−16.7%−16.7%−16.7%
Observations93,88193,88193,881
Game fixed effectsxxx
Month fixed effectsxxx
Adjusted R20.0090.0100.010
F12.11***11.02***10.81***


Notes. OLS estimates of Equation (1). Column (1) is the baseline and includes game, month, and category fixed effects. Column (2) adds controls. Column (3) adds a one-month lag of the dependent variable. The category “Action and racing” is the baseline category. Observations are game-months. Standard errors are reported in parentheses. Adjusted R2 excludes the explanatory power of game and month fixed effects. x, fixed effects are included.

 *, **, *** indicate significance at the 5%, 1%, and 0.1% levels, respectively.

6.1.2. Sensitivity: Alternative Estimators and Time Windows.

Supplementary sensitivity analyses reported in Online Appendix B corroborate the result. First, we use alternative estimators (Table B1). We estimate the regressions with a conditional (fixed effects) Logit estimator and a regular Logit estimator and find the results are confirmed. Given the substantial share of zeros in the dependent variable, we additionally apply a Firth Logit estimator (Heinze and Schemper 2002) and again obtain consistent results. Second, we consider variations of the postban period (Table B2). Our preferred choice is to let the postperiod begin with the announcement to capture immediate effects; however, arguably it could take time for developers to adjust, so that letting the postperiod begin with the enforcement of the ban could be more appropriate. Our results are robust to either choice: If the postperiod begins with the enforcement of the ban (as opposed to the announcement), the resulting effect is significant but smaller (−12.5%). Moreover, we estimate the equation for different lengths of the postperiod (i.e., 3, 6, and 10 months). In all models, the DiD coefficient is significant, which corroborates the finding. We also estimate a relative time model (i.e., we interact dummies for each month with Treat) to allow for month-specific treatment effect magnitudes (Greenwood and Wattal 2017) (Table B3).5 Before the ban, the DiD coefficients are consistently insignificant. After the ban, the estimates are consistently negative, and significant in months t + 6 and t + 7. Finally, we observe a significant decline in the release of any update (−35.4%) and bug fixes (−20.8%) in reaction to the ban (Table B4). When modeling the dependent variable as a count (i.e., Feature Updates), we find the negative effect confirmed.

6.2. Heterogenous Effects

To assess the outlined potential heterogeneity, we consider heterogeneity by interacting the DiD term with the moderator, which gives the difference-in-difference-in-differences (DiDiD):

Feature Updatei,t=β0+β1Aftert×Xi/j+β2Treati×Aftert+β3Treati×Aftert×Xi/j+ψi+ϕt+φi,t+εi,t,(2)
with an identical notation as before, except that Xi/j holds the moderator variable for game i or developer j. The coefficients of interest are β2 (DiD) and β3 (DiDiD). Controls are identical to Equation (1).6

We begin by assessing the effects dependent on game characteristics.7 Table 3 summarizes the results. Column (1) reports the effects when distinguishing top rated games. We find that the ban has a negative effect on games, except for the ones which are top rated. Column (2) shows consistent results when distinguishing between top demanded games and other games. Thus, well-rated and high-demanded games are being enhanced as opposed to be abandoned in reaction to the ban. To illustrate the effect magnitudes, Online Appendix Figure B3 plots the heterogeneous effects. In a series of further regressions, we address concerns over a seemingly subjective choice of the percentile that defines whether a game is classified as top. In these regressions, not reported for brevity, we observe that the 90th percentile is the decisive cutoff; that is, only games that fall in this percentile or above show positive effects. In addition, the games in the sample are not per se low-rated or low-demanded ones as the median values in Table 1 show.

Table

Table 3. Heterogeneity Along Game and Developer Characteristics

Table 3. Heterogeneity Along Game and Developer Characteristics

Dependent variable = Feature Update
(1)(2)(3)(4)(5)(6)
Treat × After−0.011**−0.012***−0.002−0.003−0.011***−0.003
(0.003)(0.003)(0.003)(0.003)(0.003)(0.004)
Game characteristics
Treat × After × Top Rated0.013*−0.006
(0.006)(0.015)
Treat × After × Top Demanded0.020***0.036*
(0.006)(0.015)
Developer characteristics
Treat × After × Undiversified−0.015***−0.014**
(0.005)(0.005)
Treat × After × Young−0.013*−0.016**
(0.005)(0.006)
Treat × After × Charges Price0.018*0.014
(0.008)(0.009)
Observations93,88193,88193,88193,88193,88193,881
Controlsxxxxxx
Game fixed effectsxxxxxx
Category fixed effectsxxxxxx
Month fixed effectsxxxxxx
Adjusted R20.0100.0100.0100.0100.0100.011
F10.89***11.13***10.91***10.57***10.48***9.75***


Notes. LPM estimates of Equation (2). Column (1) shows the effect conditional on Top Rated. Column (2) provides the effect depending on Top Demanded. Column (3) shows the moderating effect for Undiversified. Column (4) provides the effect contingent on Young. Column (5) reports the effect contingent on Charges Price. Column (6) includes all moderators. Observations are game-months. Standard errors are reported in parentheses. Adjusted R2 excludes the explanatory power of game and month fixed effects. x, fixed effects are included.

 *, **, *** indicate significance at the 5%, 1%, and 0.1% levels, respectively.

Next, we assess the effects conditional on developer characteristics to understand which of them are particularly cutting their development efforts in reaction to the ban. Table 3 proceeds with the results. Column (3) shows that the effects are stronger for games of undiversified developers, with the likelihood of a Feature Update decreasing by −35.4%. Column (4) further confirms the result by showing that the effects are stronger for games of young developers. The effect amounts to −33.3%. Column (5) reports the effects contingent on Charges Price, indicating that developers who entirely rely on ad-financed apps in their portfolio are detrimentally affected (−22.9%). Taken together, we conclude that the ban adversely affects games by undiversified, young, and ad-financed developers. Online Appendix Figure B4 plots the heterogeneous effects. For robustness, column (6) reports a joint test, which includes all previous interactions into one model. The effects regarding heterogeneity across games are consistent; the interaction for Top Rated falls below the significance level, but this is likely due to being correlated to Top Demanded. In fact, the correlation between these two variables is 0.89. For the heterogeneity on the developer level, we also observe that the coefficients are consistent in direction; the only exception is for Charges Price, which falls below the significance level.

6.3. Mechanism: Decline in Ad Revenues

Our argument is that developers abandoned their games because the ban on targeted ads reduced their revenues. To ideally test for this mechanism, we would require time series data on developers’ game-specific ad revenues, in addition to a second source of (quasi-)randomization. However, it is difficult, if not impossible, to observe ad revenues because developers do not disclose them in a structured manner. Although some analytics firms publish revenue estimates, these do not distinguish the source of revenue (e.g., ads versus payment), are only available for a few top-performing games, and lack transparency with regard to their estimation. Moreover, we lack a second identification that could accomplish randomization. Against this backdrop, we follow Pierce et al. (2015) by formulating and testing predictions that should hold if the mechanism is present.

For testing, we rely on split-sample analyses over interaction tests for the following reasons. Split-sample analyses are based on dividing the full sample into subsamples depending on one characteristic and reestimating the regression for each subsample. Split-sample analyses are the preferred choice in this case, because they allow us to infer whether a relationship holds in the sample for which it is expected and whether it does not hold in the sample for which it is not expected due to the missing characteristic (Williams 2015). By contrast, moderation models would test whether the effect for one group is statistically different from the effect for another group (Williams 2015).

We formulate three predictions; the tests are reported in Table 4. The coefficient of interest should be more pronounced in the sample that corresponds to the prediction. First, if declining ad revenues are driving game abandonment, then games that had collected data that was relatively higher compensated by advertisers should show a disproportionally large decline in updating compared with those that did not collect such data. This is because the more personally identifiable data a game collects, the higher should be its advertising-dependency (Lambrecht and Tucker 2013, Smaato 2021). Market analytics companies estimate that Android developers can double their ad compensation when providing ad networks with personal identifiers such as device IDs and location (Smaato 2021; Online Appendix Figure B5 compares the compensations for different types of data). Columns (1) and (2) support the first prediction. The negative effect of the ban is significant in the subsample of games that had collected identifiable user data and not significant in the subsample of games that had not collected such data. Moreover, the effect size is more than twice as large (−29.2%, Chow F = 6.57).

Table

Table 4. Tests for Ad Revenue Mechanism

Table 4. Tests for Ad Revenue Mechanism

Dependent variable = Feature Update
Split = Collects user IDSplit = Ad networksSplit = Ad views
(1)(2)(3)(4)(5)(6)
NoYesBelow medianAbove medianBelow medianAbove median
Treat × After−0.006−0.014*−0.009−0.012**−0.005−0.011*
(0.003)(0.007)(0.005)(0.005)(0.003)(0.005)
Chow test (F)6.57**4.70*7.25**
SpecificationLPMLPMLPMLPMLPMLPM
Observations75,23218,64934,36324,94253,23040,283
Controlsxxxxxx
Game fixed effectsxxxxxx
Category fixed effectsxxxxxx
Month fixed effectsxxxxxx
Adjusted R20.0120.0070.0130.0090.0070.014


Notes. LPM estimates. Columns (1) and (2) split the sample depending on Collects User ID. Columns (3) and (4) split the sample along the median of Ad Networks. Columns (5) and (6) split the sample along Ad Views. Observations are game-months. Standard errors are reported in parentheses. Adjusted R2 excludes the explanatory power of game and month fixed effects. x, fixed effects are included.

 *, **, *** indicate significance at the 5%, 1%, and 0.1% levels, respectively.

Second, if declining ad revenues are driving game abandonment, then games that integrate more ad networks should suffer greater drops in revenues and therefore should show stronger cuts in updating. By relying on several ad networks, developers can increase ad revenue because this allows the strengths of various ad networks to be combined, such as their specialization for particular ad formats or their geographical coverage. Moreover, integrating several ad networks enables the so-called “waterfall tactic,” which seeks to maximize developers’ revenues by sequentially sending requests to ad networks until all ad space is filled with the maximum revenue possible (Appodeal 2021). To test this, columns (3) and (4) report a median split along the number of ad networks used by the games. Among games above the median, the effects of the ban are significantly larger (−25.0%, Chow F = 4.70). This confirms the second prediction.

Third, we expect that games in categories characterized by a high number of ad views per user should suffer stronger declines in ad revenues and therefore show higher cuts to game updating. Ad revenues are a function of the number of views of ads and the effective cost per mille (eCPM) (IronSource 2022). To test this, columns (5) and (6) report the results when splitting the sample along Ad Views. We find that the negative effect of the ban is significantly more pronounced in the above-median group (−22.9%, Chow F = 7.25). This further corroborates the finding that the decline in feature updates is related to a drop in ad revenues. Taken together, these results indicate consistent evidence that the app abandonment is linked to reduced ad revenues after the ban on targeted advertising.

The Online Appendix reports further evidence. Corroborating the mechanism, we find that for the ad-intensive category of casual games, the negative effects of the policy are more than twice as large in magnitude than for noncasual games (Table B5). Moreover, there is descriptive evidence that developers compensate for the lost ad revenues by turning to “rewarded video ads,” which represent an alternative ad segment that provides relatively (compared with banner ads) high compensation (Figure B6). In addition, to triangulate our findings, we conducted semistructured interviews with individuals involved on the developer side (two CEOs of game developers firms, one monetization manager), the platform side (one regional business development manager), and the advertisement network side (one mobile advertising specialist). The interviews further corroborated the mechanism. Online Appendix A5 describes the interviewees and provides the insights of the interviewees.

6.4. Effects of the Ban on Developers’ Game Portfolios

We investigate how the ban impacted developers’ allocation of development efforts across games, in addition to their release of new games.8 First, we examine the effects of the ban on developers’ distribution of efforts within their game portfolio. For this purpose, we extend the data set so that it contains all games of developers in our sample. This allows distinguishing between developers’ release of feature updates for their games affected by the ban compared with those not affected. Technically, we estimate a DiDiD:

Feature Updatei,t=β0+β1Aftert×Affected Gamei+β2Treatj×Aftert+β3Treatj×Aftert×Affected Gamei+ψi+ϕt+φi,t+εi,t,(3)
with a notation of indices and included controls identical to previously shown. Treat now denotes whether developer j has at least one affected game. Game fixed effects absorb the terms Treat and Treat × Affected Game; the term After is absorbed by the time fixed effects. The coefficients of interest are β2 (DiD) and β3 (DiDiD). For consistency and because the treatment assignment remains on the game level, we use heteroscedasticity-robust standard errors clustered on the game level (Abadie et al. 2022).

Table 5 shows the results, which indicate that developers appear to relocate their development efforts to unaffected games. The coefficient on Treat × After × Affected Game is negative and significant, whereas the coefficient on Treat × After is positive and significant. This means that developers reduce feature updates for those games affected by the ban but increase the release of feature updates for those games that are not affected. We estimate that unaffected games of developers who have affected games in their portfolio experience an increase of 6.3% in the likelihood of a Feature Update, whereas the likelihood for affected games drops by −4.2%.

Table

Table 5. Effect on Game Portfolio

Table 5. Effect on Game Portfolio

EstimatorDependent variable = Feature Update
(1)(2)(3)
BaselineBaseline + controlsBaseline + lagged dependent variable
LPMLPMLPM
Treat × After0.003**0.003*0.003*
(0.001)(0.001)(0.001)
Treat × After  × Affected Game−0.005***−0.005***−0.005***
(0.001)(0.001)(0.001)
Controls
 Log(Demand)−0.003***−0.003***
(0.001)(0.001)
 Age0.0000.000
(0.000)(0.000)
 Price−0.002−0.001
(0.006)(0.006)
 Log(Firm Size)−0.005***−0.005***
(0.001)(0.001)
 One Employee−0.014*−0.014*
(0.006)(0.006)
 Feature Updatet-1−0.079***
(0.004)
Category
 Adventure  and strategy0.0190.0200.021
(0.010)(0.010)(0.011)
 Arcade0.0180.0180.018
(0.012)(0.012)(0.013)
 Board and puzzle0.037**0.036**0.037**
(0.012)(0.012)(0.012)
 Card0.0000.001−0.001
(0.018)(0.018)(0.019)
 Casino0.0150.0160.015
(0.015)(0.015)(0.015)
 Casual0.0180.0190.019
(0.012)(0.012)(0.012)
 Educational0.0230.0220.022
(0.015)(0.015)(0.016)
 Role playing  and simulation0.0110.0110.012
(0.006)(0.006)(0.007)
 Sports0.0100.0110.011
(0.008)(0.008)(0.009)
 Other−0.031−0.029−0.031
(0.045)(0.044)(0.046)
Observations353,251353,251353,251
Game fixed effectsxxx
Month fixed effectsxxx
Adjusted R20.0030.0040.010
F22.45***19.75***29.50***


Notes. OLS estimates of Equation (3). Column (1) is the baseline and includes game, month, and category fixed effects. Column (2) adds controls and category fixed effects. Column (3) adds a one-month lag of the dependent variable. The category “Action and racing” is the baseline category. Observations are developer-months. Standard errors are reported in parentheses. Adjusted R2 excludes the explanatory power of game and month fixed effects. x, fixed effects are included.

 *, **, *** indicate significance at the 5%, 1%, and 0.1% levels, respectively.

Second, we investigate the effect of the ban on a game’s likelihood of market exit. We aggregate the data on the postperiod and estimate the effects of the ban on the likelihood of games being delisted from the Google Play Store (Discontinued). We average the values of the control variables over the six months before the ban. Table 6 reports the results, which indicate that the likelihood of a game exit are 2.7 percentage points higher for affected than for nonaffected games, translating into a 10.9% increase in the probability of a game exit (0.027/0.247 baseline probability in the control group). Online Appendix Table B7 reports the estimates when using a Logit model, which are consistent. Taken together, these results support the interpretation that the ban caused app abandonment.

Table

Table 6. Effect on Games’ Market Exit

Table 6. Effect on Games’ Market Exit

SpecificationDependent variable = Discontinued
(1)(2)
Controls onlyBaseline
LPMLPM
Treat0.027*
(0.011)
Controls
 Log(Demand)−0.033***−0.033***
(0.002)(0.002)
 Age−0.000−0.000
(0.000)(0.000)
 Price−0.040−0.039
(0.083)(0.084)
 Log(Firm Size)−0.029***−0.029***
(0.005)(0.005)
 One Employee0.0230.025
(0.016)(0.016)
Category
 Adventure and strategy0.0330.031
(0.017)(0.017)
 Arcade0.039*0.040*
(0.020)(0.020)
 Board and puzzle0.0060.007
(0.025)(0.026)
 Card−0.041−0.041
(0.062)(0.062)
 Casino−0.043−0.043
(0.166)(0.169)
 Casual0.051*0.051*
(0.022)(0.022)
 Educational−0.111−0.114
(0.084)(0.085)
 Role playing and simulation0.0280.028
(0.015)(0.015)
 Sports−0.055−0.057
(0.036)(0.036)
 Other0.0680.066
(0.056)(0.057)
Observations5,8345,834
Adjusted R20.0900.091
F42.22***40.35***


Notes. LPM estimates. We estimate Discontinuedi=ß0+ß1Treati+Vi+εi. Column (1) is controls-only. Column (2) is the full model. The category “Action and Racing” is the baseline category. Observations are games. Standard errors are reported in parentheses.

 *, **, *** indicate significance at the 5%, 1%, and 0.1% levels, respectively.

Third, we investigate the impact of the ban on developers’ release of new games. To do so, we assign developers to the treatment group if at least one of their games was affected by the ban; and otherwise to the control group. We subsequently match developers on the same variables as in the main analysis, with the only exception being the exclusion of Category because this variable is only available on the game-level. The resulting data set is a developer-month panel of 198 affected and 198 unaffected developers. We estimate a linear probability model:

New Gamej,t=β0+β1Treatj×Aftert+θj+ϕt+ρj,t+εj,t,(4)
where New Gamej,t is the dependent variable of interest in month t for developer j, ϕt are month fixed effects, which absorb the term After, and θj are developer fixed effects, which absorb the term Treat. The variable list ρj,t contains the time-variant developer controls. We use heteroscedasticity-robust standard errors clustered on the developer level.

Table 7 provides the estimates. We observe consistent evidence that the ban reduced developers’ likelihood of releasing new games. Column (1) shows a statistically significant negative coefficient on Treat × After, translating into a decline by −36.3% (−0.098/0.270 baseline probability in the control group). The estimate remains comparable in magnitude and significance when adding controls, reported in column (2), and when adding a lag for the dependent variable, shown in column (3).

Table

Table 7. Effect on New Game Releases

Table 7. Effect on New Game Releases

EstimatorDependent variable = New Game
(1)(2)(3)
BaselineBaseline + controlsBaseline + lagged DV
LPMLPMLPM
Treat × After−0.098***−0.087***−0.087***
(0.026)(0.025)(0.025)
Controls
 Log(Demand)−0.076***−0.076***
(0.011)(0.011)
 Age−0.000−0.000
(0.000)(0.000)
 Price0.0010.001
(0.079)(0.078)
 Log(Firm Size)0.153***0.152***
(0.024)(0.023)
 New Gamet-10.006
(0.018)
Category
 Adventure  and strategy0.0050.0040.004
(0.040)(0.035)(0.035)
 Arcade0.025−0.003−0.003
(0.030)(0.029)(0.029)
 Board and puzzle−0.025−0.052−0.052
(0.035)(0.033)(0.033)
 Card−0.075−0.106−0.106
(0.064)(0.065)(0.065)
 Casino−0.045−0.066−0.066
(0.050)(0.044)(0.044)
 Casual0.008−0.038−0.038
(0.036)(0.035)(0.035)
 Educational−0.118−0.152−0.152
(0.082)(0.078)(0.078)
 Role playing  and simulation0.0220.0050.005
(0.030)(0.029)(0.029)
 Sports−0.027−0.038−0.038
(0.054)(0.052)(0.052)
 Other−0.032−0.077*−0.076
(0.040)(0.039)(0.039)
Observations5,3215,3215,321
Developer fixed effectsxxx
Month fixed effectsxxx
Adjusted R20.0540.1110.111
F4.96***7.51***7.42***


Notes. OLS etimates of Equation (4). Column (1) is the baseline and includes developer and month fixed effects. Column (2) adds controls. Column (3) adds a one-month lag of the dependent variable. The category is defined as a developer’s primary category (i.e., the category in which the majority of a developer’s games are listed). The category “Action and Racing” is the baseline category. One Employee is omitted because it does not vary on the developer level. Observations are developer-months. Standard errors are reported in parentheses. Adjusted R2 excludes the explanatory power of game and month fixed effects. x, fixed effects are included.

 *, **, *** indicate significance at the 5%, 1%, and 0.1% levels, respectively.

6.5. Quantifying the Effects

The obtained estimates permit a back-of-the-envelope quantification of the effects of the ban. Departing from the effects on feature updates, we estimate a total loss of 1,685 feature updates in the population of children’s games at the end of the observation period (16.7% × 0.10 feature updates per year × 10 of 12 months × 121,136 children’s games). Therefore, the ban on targeted advertising did not solely crowd out the development of low-quality or low-demand games but caused a widespread downturn. Quantifying game abandonment, we estimate that, until the end of our observation period, 3,270 children’s games were delisted (0.027 × 121,136 games). Departing from the effects on new game releases, we estimate that developers’ average number of games released per year declined from 3.35 to 2.13. Applying the estimate to the population of all game developers in the Google Play Store with children-oriented games, this translates into an annual loss of 65,712 games that would have been contributed if the ban had not been implemented (−36.3% decline in game releases × 3.35 games per year × 54,038 developers).

7. Robustness

7.1. DiD Diagnostics: Balance, “Parallel Trends,” and Anticipation

We conduct the standard tests for the assumptions of the DiD framework (Bertrand et al. 2004, Angrist and Pischke 2009). Table 8 tests for preban balance between the groups; we observe no statistically significant difference between the groups after matching. Next, Table 9 tests for differences in trends by interacting the month indicators for each of the six months before the policy change with the treatment group indicator (Greenwood and Wattal 2017). There are no significant differences between the trends of affected and unaffected games along these variables. Thus, there is no evidence of a violation of the “parallel trends” assumption or of an anticipation of the ban by developers. In addition, the Online Appendix reports falsification and “placebo” checks regarding anticipation and false positives (Bertrand et al. 2004, Angrist and Pischke 2009). One test randomly assigns treatment status to games in the sample; the other test places an artificial placebo event in the preperiod. Neither check indicates false positives (Table B6).

Table

Table 8. Matching Effectiveness and Preban Differences

Table 8. Matching Effectiveness and Preban Differences

Before matchingAfter matching
Control (N = 16,190)Treatment (N = 3,282)Difference in meansp value (t test)Control (N = 2,917)Treatment (N = 2,917)Difference in meansp value (t test)
Feature Update0.040.04−0.000.370.030.03−0.000.88
Rating3.553.80−0.250.003.733.75−0.020.46
Log(Reviews)4.755.65−0.910.005.395.42−0.030.71
Age544.93619.70−74.770.00561.33577.53−16.200.30
Price0.030.010.020.000.010.010.000.91
File Size39.4647.04−7.580.0045.6845.89−0.210.74
Permissions6.536.70−0.170.036.656.640.020.88


Note. The table tests for differences in means between affected and unaffected games before and after the matching using a t test, based on six-month averages before the ban.

Table

Table 9. Test for the Parallel Trends Assumption

Table 9. Test for the Parallel Trends Assumption

Estimator(1)(2)(3)(4)(5)(6)
Feature UpdateRatingLog(Demand)PriceFile SizePermissions
LPMOLSOLSLPMOLSOLS
Treat × t − 50.007−0.010−0.000−0.0000.067−0.029
(0.008)(0.007)(0.017)(0.001)(0.084)(0.021)
Treat × t − 4−0.0030.0020.003−0.0000.116−0.009
(0.008)(0.007)(0.019)(0.001)(0.118)(0.026)
Treat × t − 3−0.003−0.0030.0130.000−0.048−0.007
(0.008)(0.007)(0.021)(0.001)(0.147)(0.030)
Treat × t − 20.0050.0030.0090.0000.0290.030
(0.008)(0.007)(0.023)(0.001)(0.165)(0.035)
Treat × t − 1−0.0000.0080.0170.0010.1690.047
(0.007)(0.008)(0.025)(0.001)(0.178)(0.037)
Observations26,97827,38929,18729,18728,04529,187
Game fixed effectsxxxxxx
Category fixed effectsxxxxxx
Month fixed effectsxxxxxx
Adjusted R20.0070.0230.1350.0000.0040.003
Fn/a20.48***79.54***0.402.37***1.32


Notes. The table provides tests for differences in trends in the preban period, for the dependent variable in column (1) and game characteristics in columns (2) to (6). Observations are game-months. Standard errors are reported in parentheses. Adjusted R2 excludes the explanatory power of game and month fixed effects. x, fixed effects are included.

 *, **, *** indicate significance at the 5%, 1%, and 0.1% levels, respectively.

7.2. Enforcement and Compliance

A necessary condition for the validity of the research design is that Google actively enforced the new rules. Given that Android is an open platform, one may argue that Google has little control over enforcement, which raises questions over developers’ compliance with the ban. However, Figure 3 plots two pieces of evidence that indicate that games complied with the rules. The plots display changes within the treated group over time, relative to one month before the ban. Figure 3(a) plots the relative change in the number of treated games that request the so-called Read_Phone_Status_And_Identity (RPSI) permission (solid line) compared with the change in the request of all other permissions (dashed line). The RPSI permission gives a game access to the so-called Android Advertising ID, a unique identifier of the user’s device that is necessary for targeting ads but has negligible importance for a game’s functionality (Adjust 2021). The use of the RPSI permission can serve as a proxy for compliance. If Google enforced the new rules, we should see that the use of the RPSI declines over time, whereas the use of other permissions remains stable. This is indeed what we observe; the use of the RPSI permission declines after the ban. Further corroboration for enforcement is Figure 3(b), which plots the relative change in the number of games in the treatment group that connect to “forbidden” advertising networks (solid line) versus certified advertising networks (dashed line) over time. The new rules mandate the use of a set of certified ad networks, thereby effectively disallowing the use of some previously popular ad networks. In line with compliance, we observe that the use of forbidden ad networks declines after the ban.

Figure 3. Compliance and Enforcement
Notes. (a) Relative change in the number of games in the treatment group that request the Read_Phone_Status_And_Identity permission (black) versus request of all other permissions (gray) by games in the treatment group over time, relative to the month before the ban. We focus our analysis on 529 affected games that used the permission and are observed for the full observation period. (b) Relative change in the number of games in the treatment group that connect to “forbidden” ad networks (black) versus certified ad networks (gray) over time, relative to the month before the ban.

There is also descriptive and anecdotal evidence that Google suspended or removed noncompliant games. Particularly popular suspensions include Princess Salon, Number Coloring, and Cats & Cosplay, which were, despite their total 20 million downloads, taken off the Play Store due to their collection of personally identifiable data from children (TechCrunch 2020a). Moreover, developer and ad network forums showed posts of developers that reported the suspension of their app, asking for help (Unity Technologies 2020).

7.3. Switching of Content Ratings

One concern is that developers may evade compliance by switching the content rating of their game to nonchild audiences (i.e., from “Everyone 10+” to “Teen 13+” or “Mature 17+”). One could argue that if many developers do so, the estimates from our model would be biased upward as more updates would be released in the control group and fewer in the treatment group.9 However, the switching of content ratings is not problematic for our results for three reasons. First, Google announced to check content rating changes: “you must accurately answer the questions in the Play Console regarding your app and update those answers to accurately reflect any changes to your app. This includes […] accurately disclosing your app’s interactive elements on the Content Rating Questionnaire […]” (see Figure B2; Google 2019b). Moreover, “regardless of what [developers] identify, […] Google Play reserves the right to conduct its own review of the app information.” Google further outlined that the “misrepresentation of any information about your app in the Play Console, including in the Target Audience and Content section, may result in removal or suspension” (Google 2019c). Overall, any “failure to satisfy the [.] [Family Policy Requirements] may result in [.] removal or suspension” of a game (Google 2019c). In light of these statements, it is likely that any switching game would be checked and that games which appeal to children would be recognized. Indeed, with respect to actual behavior, we observe that only a tiny fraction of games switched from ?Everyone 10+? to ?Teen 13+? (Online Appendix Figure B7). Second, to understand whether switching implies differences or changes to updating behavior, we test for differences in means to nonswitching games on various variables, including feature updates (Table B8). None of the differences are significant, which refutes concerns of spuriousness. Finally, and most corroborating, the results hold when we exclude switching games from the sample (Table B9). The obtained estimate is significant and comparable to the baseline. Taken together, based on this evidence, it is unlikely that switching biases our findings.

7.4. Alternative Control Groups

The results are robust toward four alternative control groups (Online Appendix A4 reports details on the technical construction and data sources and reports the checks for balance and parallel trends). First, we construct a control group from games that had been compliant before the ban. In particular, games in the category “Educational” were required to comply with the Family Policy Requirements long before the announcement (Kidoz 2018). In Table 10, column (1) reports the estimate, which is also significant (−10.4%). Second, we create an alternative control group using the “Similar Games” information displayed in the Google Play Store (Wen and Zhu 2019, Mayya and Viswanathan 2021). It is likely that Google can leverage richer data for formulating recommendations than we can obtain from public sources. In Table 10, column (2) reports the thereby obtained coefficient, which is significant (−12.5%). Third, we construct a control group from games on the Apple iOS platform.10 In Table 10, column (3) shows the resulting coefficient, which is significant (−33.3%). Last, we implement a synthetic control approach to further address concerns over unobserved time-variant heterogeneity (Abadie et al. 2010). The synthetic control method provides a method of approximating an alternative counterfactual by creating a weighted average of observations that are similar to the affected games apart from not receiving the treatment. Originally developed for settings in which one treated observation is compared with a small number of control units (e.g., comparisons between countries or states), the synthetic control method has recently been extended to DiD models and settings with many units (Arkhangelsky et al. 2019, Schmitt et al. 2021). In Table 10, column (4) reports the estimate, which is significant (−14.6%). Taken together, the results hold for four alternative control groups.

Table

Table 10. Robustness Checks with Alternative Control Groups

Table 10. Robustness Checks with Alternative Control Groups

Control groupDependent variable = Feature Update
(1)(2)(3)(4)
Already compliantBased on “similar apps” featureiOS gamesSynthetic control method
Treat × After−0.005*−0.006*−0.016***−0.007***
(0.002)(0.003)(0.005)(0.002)
Effect size (in %)−10.4%−12.5%−33.3%−14.6%
Observations53,18797,03656,43661,945
Controlsxxxx
Game fixed effectsxxxx
Category fixed effectsxx
Month fixed effectsxxxx
Adjusted R20.0070.0110.0100.011


Notes. The table reports robustness checks that assess the validity of the control group. Column (1) relies on a control group comprised of games that had to be compliant with the new rules already before the announcement. Column (2) uses a control group which we constructed using the “similar games” recommendations in the Google Play Store. Column (3) uses a control group constructed from iOS games. Column (4) relies on a synthetic control group. LPM estimates. Observations are game-months. Standard errors are reported in parentheses. Adjusted R2 excludes the explanatory power of game and month fixed effects. x, fixed effects are included.

 *, **, *** indicate significance at the 5%, 1%, and 0.1% levels, respectively.

7.5. External Validity

Online Appendix Table B10 reports a robustness check for coverage error caused by our filtering procedure. We reestimate Equation (1) on the unfiltered sample (i.e., before removing inactive games and matching). This sample effectively makes up 10.2% of all games in the Google Play Store. The findings are consistent (−16.7%). We also expand the sample by considering all content ratings (i.e., the treatment group includes “Everyone” and “Everyone 10+”; the control group “Teen 13+,” “Mature 17+,” and “Adults only 18+”). This sample holds 8.5% of all games in the Google Play Store. In line, the estimate is negative and significant (−8.3%).

8. Discussion and Conclusion

This study empirically investigated the impact of Google’s ban on targeted advertising in the Android market for children’s games. The picture gained from our analyses is that the monetization via targeted advertising is crucial for app development as the ban caused substantial game abandonment. We consistently observe that developers released fewer feature updates to their games, and also fewer bug fixes and updates in general. These effects were confirmed in various sensitivity and robustness checks. Only exceptionally well-rated and demanded games experienced more feature updates, which could be interpreted as a sign of opportunity due to better monetization potential or weakened competition. However, considering that we observed these effects only for games in the highest decile of app quality and demand and given that the median user rating of a game is 4.1 of 5, our findings suggest widespread game abandonment. Particularly affected by the ban were firms that were young, undiversified, and dependent on ads. The analyses of developers’ portfolio-related development decisions provide further confidence for this conclusion: we observed that affected games were more likely to be delisted from the Google Play Store; developers shifted the development of feature updates toward their unaffected games; and developers released fewer new games. Additional tests link the decline in game development to falling advertising revenues. Thus, to a certain degree, our findings support claims made in connection with the event, such as the one of Clark Stacey, CEO of WildWorks, “if [the advertising] monetization model is removed[…], I don’t know how long [our firm] would be able to continue” (Washington Post 2019).

Our study makes the following theoretical contributions. First, we contribute to research on platform management by empirically investigating the effects of a ban on targeted advertisement on app development (Parker and Van Alstyne 2005, Bhargava 2021). Our findings highlight the importance of targeted advertising for app development on mobile platforms. Moreover, our study suggests that user privacy can conflict with platform firms’ critical goal of a variety of novel and continuously innovated apps that meet idiosyncratic needs (Miric and Jeppesen 2020, Janssen et al. 2021). Our empirical evidence helps understand the extent to which a ban on targeted ads affects app development and which apps are more and which ones are less affected.

Second, our study contributes to research on the monetization of digital content and products, especially to the stream of work on targeted advertisement (Chellappa and Shivendu 2010, Lambrecht et al. 2014, Casadesus-Masanell and Hervas-Drane 2015, Kraemer et al. 2019). Existing research has documented the effectiveness of targeted advertising and its revenue potentials. Our study links targeted advertising to actual product development outcomes of firms. Our findings show that targeted advertising plays a critical role for app developers and that switching to alternative forms of monetization does not appear to be a viable alternative. Instead, the ban on ad targeting caused widespread app abandonment.

Finally, our findings contribute to studies on the economics of privacy, particularly those investigating user privacy in relationship to advertisement (Acquisti et al. 2016). Our study complements the previous theoretical work by offering empirical evidence on the impact of a ban on targeted ads on product development (Goldfarb and Tucker 2012, Campbell et al. 2015). Our findings provide empirical evidence for the prediction of Campbell et al. (2015) that young and undiversified firms are most adversely affected by stricter privacy. We also add to the economics of the privacy literature by detailing the reactions of Internet firms when their ability to make money from “free” products is restricted. Furthermore, the observed shift of development toward apps unaffected by the ban is in line with the finding of Mayya and Viswanathan (2021) that developers might act strategically to avoid stricter privacy regimes.

Our investigation yields insights for managers. Our findings inform mobile platform firms about the consequences of banning targeted advertising on their platforms. Understanding these consequences is important, given increasingly privacy-aware users and the emerging competition for privacy. In light of Google’s ban on targeted ads and the documented decline in app development, we highlight a tradeoff between relieving users of targeted ads and promoting app development, both outcomes that are critical for the success of a two-sided development platform. Our analysis of a comprehensive set of app development outcomes, in addition to our quantification of the results, enables platform firms to assess the extent to which a ban on targeted advertising affects app development. Considering the slump in app development due to the ban, platform managers are advised to implement additional measures to reduce the burden on app developers arising from the loss in ad revenues when restricting advertising, for instance, by designing alternative monetization opportunities. The heterogeneous effects—that is, that the effects turn positive for exceptionally well-rated and demanded games and that undiversified, young, and advertisement-dependent developers are more adversely affected—help platform firms design the balance between user privacy and app development in their specific setting. For app developers, our findings show the potentially severe consequences of a ban on ad targeting. To survive in stricter privacy environments, developers are advised to concentrate on prioritizing product quality and demand, to diversify, and to consider different platforms’ (expected) long-term policy regarding ad targeting.

Our study is not without limitations. Our research design cannot observe the effects on game development beyond 10 months after the ban. Moreover, our findings are specific to mobile platforms, and it remains an open question how banning ad targeting affects platforms that rely less on ad-based monetization. For creator platforms where content generation is mostly sunk costs, and compliance implies few additional costs, we expect less negative effects. Our findings also need to be considered in light of the fact that we studied a ban. Our findings might not be directly transferrable to opt-in or opt-out policies. Last, children’s games represent a particular type of games, and the findings might not generalize beyond these (Radesky et al. 2020).

Acknowledgments

The authors thank the department editor Hemant Bhargava, associate editor, and anonymous reviewers; participants at the Workshop on Information System Design and Economic Behavior 2021, the Research on Innovation, Science, and Entrepreneurship Workshop 2021 of the Max Planck Institute for Innovation and Competition, and the Workshop on Information Systems and Economics 2020, with distinct gratitude for the insightful feedback of Joachim Henkel, Ting Li, Klaus Miller, Imke Reimers, and Bernd Skiera; Alessandro Acquisti for helpful comments on an early version of this manuscript; and participants in presentations at the Erasmus University Rotterdam, University of Passau, University of Bamberg, Tilburg University, Vienna University of Economics and Business, and Technical University of Munich.

Endnotes

1 The data collection procedure is compliant with the fair use policy of Management Science.

2 Data is available on the annual level only; therefore, the data at least partially captures the ad impressions after the enforcement of the ban. This is a limitation, but the best data available to us because the data is not reported for 2018 and because data on ad impressions is rarely disclosed.

3 The minimum value for RATINGS is in line with the data filtering described in Section 5.2 because the filtering thresholds are applied in the treatment month, but apps can have less reviews at the beginning of the observation period. The same holds true for Age.

4 The sample size stays identical to before because we compute the lag based on the month preceding the observation period.

5 We thank an anonymous reviewer for suggesting this analysis.

6 Please note that the control variable Age is not identical to Young because Young is defined for the developer and Age for the game. The same logic applies to Charges Price and Price.

7 We thank an anonymous reviewer for this suggestion.

8 We thank an anonymous reviewer for suggesting these analyses.

9 We thank an anonymous reviewer and the associate editor for raising this comment.

10 We thank the review team for suggesting this test. In 2019, Apple rolled out protections for kids’ apps on iOS. Apple’s rollout is unlikely to influence the estimates of the robustness check because it affected apps listed in the “Kids” category of the App Store. Apps listed in this category are assigned special content ratings, which technically are different to the content rating “9+” that we used to construct the control group.

References

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