Bijlage 8_Banning unsolicited store flyers does helping the enviroment hurt retailing

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BANNING UNSOLICITED STORE FLYERS: DOES HELPING THE ENVIRONMENT HURT RETAILING?

Jonne Y. Guyt1 Arjen van Lin Kristopher O. Keller

September 2024

Jonne Y. Guyt1 is an associate professor, Amsterdam Business School, University of Amsterdam, The Netherlands (e-mail: j.y.guyt@uva.nl). Arjen van Lin is an associate professor, Tilburg School of Economics and Management, Tilburg University, The Netherlands (e-mail: avanlin@uvt.nl). Kristopher O. Keller is an assistant professor, Kenan-Flagler Business School, University of North Carolina at Chapel Hill, USA (e-mail: kristopher_keller@kenan-flagler.unc.edu). We thank Bart Bronnenberg, Els Gijsbrechts and participants at various conferences for helpful comments on an earlier version. We are indebted to AiMark/GfK for providing the data. We also thank the A Sustainable Future research platform and Marketing Science Institute (MSI) for financial support (MSI Research Grant # 4001614).

2 BANNING UNSOLICITED STORE FLYERS: DOES HELPING THE ENVIRONMENT HURT RETAILING?

ABSTRACT Retailers often use store flyers to communicate the availability, price, and promotions of their products. Many households inspect store flyers for promotions, and the majority still prefer to receive store flyers in print. Yet, many are said to throw out store flyers unread, creating excessive waste that is environmentally damaging due to the excess use of paper, ink, and logistics. Legislation to reduce the distribution and waste associated with unsolicited store flyers has been proposed, but if and how much such a cut in distribution would affect households’ grocery shopping behavior remains unclear. This paper investigates a recent policy change by seven Dutch municipalities that implemented a ban on unsolicited store flyers by moving from an opt-out to an opt-in policy at some point between 2018 and 2020. Using household scanner data, the authors assess changes in shopping behavior along nine comprehensive dimensions relevant to retailers, brand manufacturers, and policymakers, using a stacked, synthetic difference-indifferences approach. Although store flyer distribution decreased by 50% under the new policy, the drastic change did not substantially affect grocery shopping behavior. These findings are robust to different time windows and modeling approaches.

KEYWORDS: retailing, store flyer, natural experiment, advertising, responsible retailing, feature promotions.

3 INTRODUCTION Store flyers, also known as store circulars or weekly ads, help retailers communicate about the availability, price, and promotions on the products in their assortment (Pieters, Wedel, and Zhang 2007). Even in the digital age, grocery retailers continue to invest in delivering physical store flyers to shoppers’ homes, an investment that can reach $1 million for a single run, such that store flyers often account for the largest share of grocery retailers’ marketing budgets (Kapner 2015b; Vericast 2020). In the United States, more than 80% of shoppers frequently inspect weekly flyers for promotions, and 60% prefer to receive store flyers in print format (Kapner 2015a; Vericast 2020). Such reliance is not unique to the United States either; store flyers account for more than half of the average retail marketing budget for grocers in several European countries (Gázquez-Abad and Martinez-Lopez 2016), where readership is also reported to be high. In the Netherlands, for example, 95% of all households that receive print store flyers read them, 86% use them, and 54% indicate they would miss them if the flyers stopped appearing in their mailboxes (GfK/NMO 2024).

But some environmental groups and policymakers doubt these claims, noting alternative evidence that many households throw out store flyers unread, creating unnecessary, excess uses of paper, ink, and logistics that have detrimental environmental implications (Retailtrends 2016). For example, in the Netherlands, a typical household receives approximately 1,300 store flyers annually, which could translate into 30 kilograms of paper waste per household (NOS 2021). In response to this concern, similar to several other national and regional governments (e.g., Australia, New Zealand, Quebec), the Netherlands has introduced legislation to reduce waste due to store flyers and other unsolicited advertising mail (Haas 2021; Woolf 2019). Others, such as France and Luxembourg, are in the process of introducing similar legislation (EUWID Pulp and Paper 2022; Near 2022).1 But, not all stakeholders agree on the environmental impact or that it comes without costs. For

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Most unsolicited advertising mail consists of store flyers, but current and proposed national policies address all its forms. In interviews with flyer distributors, we confirmed that most bulk mail involves store flyers, and retailers represent the majority of their clients. Hereinafter, reflecting our research focus, we use the term “store flyers”.

4 example, in the Netherlands, several municipalities are hesitant to adopt the legislation, being worried about its net impact on society. Indeed, these plans have prompted strong opposition from flyer distributors, who fear that banning unsolicited store flyers will lead to negative downstream consequences in the distribution ecosystem, such as job losses. As importantly, such a ban may hurt retailers’ business as a large percentage of their sales involve products promoted through the flyers (Gedenk, Neslin, and Ailawadi 2010). The effects of such a ban on household shopping behavior remains an open question, however, that neither trade press nor academic literature has answered. The effects on grocery shopping behavior will depend on the extent to which households rely on store flyers in practice. Industry reports suggest that households not only use store flyers to decide where to buy their groceries, but also what to buy (Grocery Dive 2018; Vericast 2020). For households using store flyers to guide their shopping, no longer receiving flyers can increase their search costs and may influence their grocery shopping behavior. Households often visit multiple retail chains in a given week (Gauri, Sudhir, and Talukdar 2008; Guyt and Gijsbrechts 2020) and may stop visiting some of these chains when they no longer receive their flyers and learn of their promotions.

For instance, a household may purchase most of its groceries at its “primary” chain A but may purchase another product (e.g., cereal) at chain B in a particular week, having seen a price discount for that product in chain B’s store flyer. Without receiving store flyers, the household may purchase all its groceries at its primary chain A that week. In addition, without flyers, the household may buy the private label product it always does instead of the brand advertised in chain B’s store flyer or may not buy the product at all. However, if environmental groups and policymakers are correct in that most households throw out store flyers unread, a ban’s impact on shopping behavior is likely to be small. A common implementation of a ban on unsolicited store flyers is an opt-in approach in which only households that explicitly request flyers receive them. If households that use store flyers opt in to receive them and those who throw them out unread do not, waste can be reduced without any effects on shopping behavior. The policy change thus might act like an effective sorting mechanism. Yet, we also might anticipate more nuanced outcomes because households make trade-offs

5 between the benefits (e.g., learning about product availability, prices, and promotions, which can guide consumers’ shopping) and costs of receiving store flyers. A default change could lead to higher costs (Johnson and Goldstein 2003), which might shift the balance of the cost-benefit trade-off—and thus households’ shopping behavior. The costs of receiving flyers involve not just opportunity costs but also environmental costs and the potential or perceived costs of contradicting social norms (cf. Johnson and Goldstein 2003). Indeed, retailers and flyer distributors fear that households may stick to the default option of not receiving store flyers because the additional costs of are too high. That is, a default change may change the cost-benefit balance of receiving store flyers of a large group of households, leading to noticeable changes in shopping behavior. In this study, we aim to understand to what extent such concerns are warranted, i.e., whether a ban on unsolicited store flyers affects households’ grocery shopping behavior. To answer this pertinent research question, we consider a recent policy change by seven Dutch municipalities that implemented a ban on unsolicited store flyers, by switching from an opt-out to an optin policy for households, at some point between 2018 and 2020.

That is, they moved from a setting where households receive store flyers unless they explicitly opt out to a setting where store flyers are not delivered unless households explicitly request them. Using household panel scanner data from GfK, we assess the change in shopping behaviors of about 900 households across the seven affected municipalities, using nine dimensions that are relevant to retailers, brand manufacturers, and policymakers: (1) total grocery expenditures, (2) total number of units purchased, (3) share of private labels, (4) share of purchases on promotion, (5) number of shopping trips, (6) number of different retail chains visited, (7) share of trips to traditional retailers versus hard discounters, (8) grocery expenditure at the primary chain, and (9) number of shopping trips to the primary chain. As an identification strategy, we use the recently developed, stacked, synthetic difference-indifferences (SynthDID) approach (Arkhangelsky et al. 2021; Berman and Israeli 2022; Li et al. 2022) that enables us to compare households’ shopping behavior before and after the policy change, relative to a set of control households in markets without the ban (i.e., still subject to the opt-out policy). The stacked

6 SynthDID approach offers several advantages in our setting. First, it creates a synthetic control group, matched on pre-treatment purchase behavior, which enhances the compatibility and face validity of the control households vis-à-vis the treatment households. Second, it comes with a desirable bias-variance tradeoff compared to alternative methods such as DID or synthetic control. Third, it reduces the risk of overfitting that can occur with synthetic control. Fourth, it accounts for the staggered implementation of the ban across municipalities, which renders the standard DID approach biased (Goodman-Bacon 2021). The findings show that instituting an opt-in policy reduces the distribution of store flyers dramatically: Under the previous opt-out policy, close to 75% of all households received store flyers, whereas that level fell to 37.5% under the opt-in policy. Contrary to concerns by retailers and flyer distributors, the stacked SynthDID findings show that this drastic change does not substantially affect any of the nine dimensions of grocery shopping behavior of households in the treated areas. That is, the intent-to-treat (ITT) estimates are statistically not distinguishable from zero and are economically small. These findings remain remarkably robust to different time windows and modeling approaches.

Results from a subgroup analysis, in which we estimate the local average treatment effect (LATE) for households that did not opt in, i.e., that stopped receiving store flyers, similarly show no economically meaningful change in behavior. Specifically, for eight of our nine dimensions of grocery shopping, we find small and insignificant effects, while for the share of purchases on promotions, we find a significant but economically small effect of less than one percentage point decrease. We also provide policy-relevant insights as to whether some households are differentially affected from others by this legislative change. Our results provide limited evidence of this; only older and moderately price-sensitive households appear to be impacted as they modestly reduce their share of purchases on promotions. We explore three explanations for this lack of meaningful effects: Retailers changing their marketing communication in treated municipalities, households switching to digital rather than print flyers, or an overstated dependence of some households on store flyers. We find no evidence for the first two explanations. As such, our findings suggest that the 50% of households that no longer receive flyers after the ban did not rely on them and, hence, were largely unresponsive to these marketing efforts.

7 Thus, this study contributes to academic literature, practice, and policy. Store flyers and feature promotions have been analyzed extensively in marketing literature (Ailawadi and Gupta 2014), primarily in efforts to understand the implications of featuring certain products in store flyers (e.g., Guyt and Gijsbrechts 2018; Van Lin and Gijsbrechts 2016) or establish the role of store flyers in the conversion funnel (Seiler and Yao 2017). No study considers a situation in which households do not receive any unsolicited flyers at all. Our unique research setting makes it possible to ascertain reactions to banning unsolicited store flyers in a quasi-experimental way. Importantly, we study a ban on unsolicited store flyers through a change in the default option, not an outright ban, which forbids distribution to all households. As such, we evaluate to what extent retailers are hurt by an increasingly common policy where interested households could still opt in, rather than evaluate the value of store flyers themselves. Managerially, our findings provide relevant insights for both retailers and brand manufacturers. First, retailers that worry about a ban on unsolicited story flyers benefit from understanding its business impact. This is particularly relevant for traditional retailers, for which store flyers often are the main vehicle to communicate deals and promotions.

Second, national brand manufacturers also rely heavily on feature promotions and may also lose from a ban. Yet our results show that neither retailers nor manufacturers are meaningfully affected by a ban on unsolicited store flyers. These insights help retailers and manufacturers facing such bans understand their impact with greater confidence. Finally, our results are relevant for policymakers. A ban on unsolicited store flyers could reduce substantial amounts of paper used as well as the energy and water used to produce and transport flyers. Yet responsible policymakers also must acknowledge potentially unintended consequences of the legislation they propose, including potential adverse downstream consequences for flyer distributors, less than expected materialization of environmental benefits, and the risk of adverse implications of an opt-in default for grocers, which still heavily rely on store flyers. Critically, our findings indicate that at least concerns regarding changes in shopping behavior appear unfounded.

8 RELEVANT LITERATURE Store Flyers and Feature Advertising Our study relates and contributes to literature on store flyers and the promotions featured in these flyers, which also are known as feature ads. Store flyers are distributed regularly, often weekly or biweekly, to households, and communicate the availability of products (i.e., a retailer’s assortment) and information on current prices (Pieters et al. 2007). As such, consumers may use store flyers for various reasons, including deciding what and how much to buy and which store to visit (Gauri et al. 2017). Store flyers are a form of advertising mail, and in terms of their effect on consumers’ decision process (the “mechanism”), store flyers and the information provided therein can guide consumers’ shopping behavior by creating awareness for promoted products and lowering search costs (similar to the effects of advertising; Honka, Hortaçsu, and Wildenbeest 2019). That is, the information provided in the store flyer makes it easier to identify the best deals, and to determine what to buy and which stores to visit, such that they may, for instance, buy a certain national brand vs. a private label product or visit an additional retail chain to benefit from its current promotions. Academic research has shown that store flyers drive store traffic and sales (e.g., Gabel, Molitor, and Spann 2024; Guyt and Gijsbrechts 2020).

For instance, Gabel, Molitor, and Spann (2024) show how households shift their purchases from retailers that use store flyers to retailers that do not use them during a three-week suspension during COVID-19. In further studying its value, many studies consider the composition of the store flyer (e.g., size, allocation of space to particular categories or brand types, average depth of the discount; Gijsbrechts, Campo, and Goossens 2003; Gázquez-Abad and MartinezLopez 2016). For example, Gijsbrechts, Campo, and Goossens (2003) show that store flyers featuring deeper discounts are more effective for driving sales and traffic. Another subset of studies addresses the effect of individual feature promotions in the store flyers, which can increase both product sales and category purchases (e.g., Fox and Hoch 2005; Guyt and Gijsbrechts 2018). Their impact depends on specific factors, such as discount depth (van Lin and Gijsbrechts 2016) and the type of retailer (traditional

9 versus hard discounter; Widdecke et al. 2023) or product (private labels vs. national brands; Lemon and Nowlis 2002). That is, some feature promotions may be more relevant for certain products or retailers. Providing a more nuanced picture, Srinivasan and Bodapati (2006) show that feature advertising drives the store choice decisions of only certain consumers. Indeed, several studies indicate that not all consumers who receive store flyers use them to decide on their shopping (Gázquez-Abad et al. 2014; van Lin and Gijsbrechts 2016). Moreover, using path-tracking data, Seiler and Yao (2017) find that feature advertising prompts existing consumers to buy more of the featured brand rather than encouraging more consumers to visit the product category. However, among these various investigations of store flyers, their feature promotions, and their effects on consumers’ grocery shopping behavior, we find no study that addresses the effects of banning unsolicited store flyers. Summarizing the existing literature, two abstract findings can guide our intuition for the implications of a ban on unsolicited store flyers. First, store flyers can direct households’ shopping in terms of the choice of store and what and how much to buy, i.e., basket composition within a store.

As such, it is important to cover a wide set of grocery shopping dimensions to understand the impact of a default change. Second, there appears to be considerable heterogeneity in the usage of the store flyer. In our setting, we also expect that not all households value store flyers equally and differ in whether they use them to guide their shopping. Some households may not use them at all because they see little benefit in the provided information, whereas others may use flyers more intensively. In the next section we detail how a change in the default (i.e., from opt-out to opt-in) may translate into material changes to the shopping behavior of households. The Effect of a Default Change If households appreciate and want to use store flyers, a ban on unsolicited advertising would require them to opt in to continue receiving them. The policy change thus might act like a sorting mechanism, with little effect on behavior, because only households that did not use store flyers (but received them by default) stop receiving them, whereas households that derive benefits from them opt in and continue to receive them. Yet we also might anticipate more nuanced outcomes, because households

10 make trade-offs between the benefits and costs of receiving store flyers. A default change could lead to higher costs (Johnson and Goldstein 2003), which might shift the balance of the cost-benefit trade-off— and thus households’ shopping behavior. We discuss the effects below, after which we discuss the size of any potential imperfect sorting. As explained above, the benefits of receiving print store flyers for households include learning about product availability, prices, and promotions, which can help consumers decide what and how much to buy and which store to visit. The costs of receiving flyers involve not just opportunity costs but also environmental costs and the potential or perceived costs of contradicting social norms (cf. Johnson and Goldstein 2003). For example, with regard to the opportunity costs, households might resist the cognitive effort required to choose whether to (still) receive store flyers,2 in line with descriptions of people’s status quo bias (Fernandez and Rodrik 1991; Samuelson and Zeckhauser 1988). Such effort had not been required previously, because households received store flyers by default. Once those flyers stop arriving, households must undertake some non-trivial cognitive effort to evaluate the benefits, such as the potential to learn about the retailer’s assortment or opportunities to save by reviewing the printed store flyers.

If the cognitive efforts seem likely to outweigh the benefits, they might accept the new default option of not receiving store flyers. Furthermore, to obtain a mailbox sticker (e.g., filling in a form to receive it, learning where to obtain it, seeking it out at a local office) and preparing their mailbox, households must engage in logistical efforts (Stantec 2024). According to the Dutch Directorate General for Public Works and Water Management, some households express aesthetic concerns about stickers on their mailbox too (Stantec 2024). Prior to the ban, these costs only applied to households that actively sought to opt out; after the ban, households would incur the costs of receiving store flyers. If the costs outweigh the perceived benefits, households likely accept the new default and no longer receive store flyers, even though they might derive benefits from them.

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A report commissioned by the Dutch Directorate General for Public Works and Water Management (Stantec 2024) indicates that about 10% of all households do not know which policy (opt-in or opt-out) is in effect in their municipality, giving credence to the claim that households might avoid investing effort into understanding whether they should deviate from the default option.

11 Default changes also offer institutional signals of societal norms (Tankard and Paluck 2016) and an implicit recommendation about whether receiving store flyers is (still) societally preferable. When receiving store flyers is the default (i.e., opt-out regime), households have little reason to pay attention to the negative (environmental) effects of receiving store flyers. When not receiving store flyers becomes the default (i.e., opt-in regime), households likely reevaluate and recognize the potential negative effects, guided by environmental regulations (Mettler and Soss 2004; Schultz 1999). According to queue theory, changing the default option affects the order and type of arguments considered, prompting earlier retrieval of more positive aspects of the default and negative features of the non-default option (Dinner et al. 2011). In turn, we predict that the benefits provided by the store flyer get considered earlier in an opt-out regime, but environmental gains (by not receiving store flyers) are considered more in an opt-in regime. If social perceptions then suggest that continuing to receive print store flyers (which eventually end up in the trash) is not socially acceptable, they might lead to social judgments.

If the perceived costs of receiving store flyers increase due to such reevaluations of their environmental impact and social frictions, more households might accept the new default, even if they find the store flyer useful. We predict that these cost shifts, due to the default change, affect many households and their decision to accept the new default or opt in to continue receiving flyers. But for some households, such as those at extreme ends of the cost–benefit trade-off, such changes appear less likely. These households are either very positive or very negative about receiving store flyers, so they either opt in after the regulatory change or have opted out previously. But because the cost increase can overwhelm the benefits of store flyers for shoppers who fall somewhere between these extremes they may not choose to opt in (i.e., no longer receive store flyers), so the net balance of the trade-off could shift for a non-trivial group of households. Empirically, there is evidence of default changes resulting in large shifts in other settings, such as organ donation (from 82 to 42%; Johnson and Goldstein 2003). This, combined with survey statistics suggesting only roughly 50% would opt-in out of the households that currently receive store flyers (Markteffect 2022), suggests many households may experience a shift in their net balance and stop

12 receiving store flyers once an opt-in policy is in place. A priori, it is unclear whether these households predominantly consist of households that obtain few benefits from the flyer, as policymakers suggest, or households that do obtain substantial benefits, as suggested by the industry. Importantly, according to supporters of the opt-in policy, the opt-out policy leads to imperfect sorting as there are many households that are receiving but not using flyers, whereas opponents typically argue that an opt-in policy leads to imperfect sorting as many households derive benefits from flyers but would stop receiving them. To summarize, the degree to which shopping behaviors change due to the new default depends on the share of households that see a shift in their net balance and the degree to which they derive benefits from store flyers that drive their shopping behavior, which are empirical questions.

SETTING AND DATA Setting and Institutional Details. The setting of our study is the grocery market in the Netherlands, where many retailers rely on store flyers as one of their main communication vehicles.3 Between 2018 and 2020, seven municipalities introduced a ban on unsolicited store flyers. An opt-out approach has been in place since the early 1990s and about 20%–30% of Dutch households had opted out of receiving store flyers. But environmental groups and local politicians questioned its effectiveness. By 2016, Amsterdam was the first municipality to approve a ban, such that its opt-in policy came into effect in January 2018. Flyer distributors questioned the legality of the policy and filed lawsuits, which delayed its approval and introduction in other municipalities. The courts ultimately ruled in favor of the municipalities, leading to the new policy implementation in Haarlem, Leiden, Tilburg, and Utrecht in January 2020; The Hague in July 2020; and Rotterdam in November 2020. However, several other municipalities have not banned unsolicited store flyers thus far and retained the opt-out policy, as depicted in Figure 1.

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All but one of the national retail chains use store flyers, and, across the other chains, there was no variation in distribution across municipalities before the ban. A separate analysis that assesses shopping behavior at this chain vs. others shows that the new policy does not affect this chain differently.

13 FIGURE 1: MUNICIPALITIES THAT BANNED UNSOLICITED STORE FLYERS (GREY) OR NOT (WHITE) IN THE NETHERLANDS UNTIL THE END OF 2021

The most important driver in favor of adopting the opt-in policy, according to municipalities, is whether it could lead to a meaningful reduction in paper and environmental waste related to the printing and distribution of store flyers (Stantec 2024). Other drivers mentioned are a (potentially sizable) reduction in garbage collection costs and stimulating environmental awareness among its citizens. Municipalities that have not (yet) introduced a ban question the effectiveness of the policy in reducing paper and environmental waste and may expect other measures to be effective in that regard too. Additionally, municipalities differently evaluate how feasible implementation and enforcement of the policy is. Another factor is the degree to which municipalities evaluate the risks in terms of local business (and job losses). Lastly, municipalities have been cited as ‘not wanting the hassle’ related to implementation in the form of legal issues (Stantec 2024). Indeed, as indicated above, the first municipality to introduce a ban (Amsterdam) dealt with numerous lawsuits, which may be too costly for smaller municipalities to bear.4

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Rotterdam, Utrecht, and the Hague also dealt with lawsuits surrounding the implementation (and its details). For an overview of all lawsuits, see Stantec (2024, appendix B).

14 Mailbox stickers indicate households’ opt-out/in preferences, i.e., the treatment is at the household level. Before the ban was introduced, households could put a “NO” sticker on their mailbox, indicating they did not want to receive any unsolicited store flyers. After its introduction, households could put a “YES” sticker on their mailbox to indicate that they still want to receive such mail. The stickers are available online or at the local city hall, free of charge. Any previously used “NO” stickers remain valid but are equivalent to not using a sticker. Table 1 clearly details whether households receive store flyers (✓) or not (✗) according to these two approaches.5 TABLE 1: RECEIVING STORE FLYERS (✓) OR NOT (✗) PRE AND POST BAN Pre-ban Post-ban Without sticker ✓ ✗ Mailbox sticker usage “NO” sticker ✗ ✗ “YES” sticker n/a ✓ Data We use GfK household scanner panel data for the period 2017–2021. These data contain purchase information of more than 10,000 households in any given year, representing a stratified national sample; for each trip made, they reveal the specific retail chain visited and exact purchase records (i.e., items and quantities bought, prices paid, whether the item is a private label product, and whether the item was purchased on promotion).

We use these data to compute households’ weekly shopping behavior along nine dimensions: (1) total grocery expenditure, (2) total number of units purchased, (3) share of private labels, (4) share of purchases on promotion, (5) number of shopping trips, (6) number of different retail chains visited, (7) share of trips to traditional retailers versus hard discounters, (8) grocery expenditure at the primary chain, and (9) number of shopping trips to the primary chain. The share-based measures and the number of different retail chains visited are computed conditional on a trip observed in a given week. Next to their purchases, panelists also provide information about their demographics and home location (four-digit zip code and municipality). About 12% of the households live in one of the seven treated

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In addition to indicating their preferences regarding unsolicited advertising mail, households can indicate their choice to receive community newspapers separately; the new policy does not apply to community newspapers. We provide more information on the implementation and different stickers in Web Appendix A.

15 municipalities. To understand how the ban affects their receipt of store flyers, we also need data about their opt-out/in choices (i.e., use of a mailbox sticker). We obtain these data from GfK and NOM, a Dutch media research organization, which survey a sample of panel households annually. In the first week of 2021, just after the latest introduction of the ban, we ran a survey of all treated households to supplement the data from GfK/NOM, asking households if they used a mailbox sticker and when they started using it. We obtained information about the decision to (not) opt in for about 60% of the treated households.6 Model-Free Evidence Before presenting our model, we provide some descriptive statistics and model-free evidence regarding the distribution of store flyers and household shopping behavior. First, in terms of circulation, we observe that 37.5% of the households in municipalities with a ban opted in to receive the flyers. Prior to the ban, we observe an opt-out of only 25.7%, implying that 74.3% of the households received flyers before the ban was introduced. Therefore, the number of flyers distributed declined by about 49.5% (from 74.3% to 37.5%).

Second, when we compare households’ shopping behavior 52 weeks before versus after the ban, across all households living in the treatment municipalities, we find only small differences in the nine grocery shopping behaviors, even though circulation dropped by almost half (see Table 2, Panel A). The largest difference we observe is for the average number of shopping trips to the primary retail chain, which decreases from 1.49 to 1.39 (-6.7%). Yet, other developments could have affected household shopping behavior in the study period too. Indeed, a comparison of shopping behavior of households from municipalities where a ban was not (yet) present across the same period (in Table 2, Panel B) shows a similar decrease. Despite retailers' concerns that reducing their flyers’ distribution would hurt their business, this evidence suggests that the ban had only marginal effects on household shopping behavior. Still, the typical caveats with before and after comparisons apply, and we address these next.

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A comparison of the demographics of households for which this information is available vs. not shows negligible differences between the two groups in terms of age, household size, and social class. However, the information is more likely to be available for households in higher income brackets. In our analysis, we use a random forest algorithm to impute the sticker usage of other households using households’ income class as input (amongst other variables). As alternative, we condition on households for which we have the information in our analysis.

16 TABLE 2: DESCRIPTIVE STATISTICS HOUSEHOLD SHOPPING BEHAVIOR A: HOUSEHOLDS IN TREATED MUNICIPALITIES Pre-Ban Post-Ban Mean SD Mean SD Total grocery expenditure (in euros) 55.08 40.58 58.08 42.70 Total number of units purchased 45.02 35.66 45.68 35.75 Share of private labels (%) 53.71 22.92 53.47 22.90 Share of purchases on promotion (%) 21.58 18.50 21.17 17.94 Number of shopping trips 2.59 1.88 2.46 1.78 Number of different retail chains visited 1.96 1.04 1.91 1.02 Trip share HDs vs. traditional retailers (%) 17.55 27.13 17.16 27.40 Grocery expenditure at primary chain (in euros) 37.44 34.98 38.18 37.28 Number of shopping trips to primary chain 1.49 1.19 1.39 1.19 B: HOUSEHOLDS IN CONTROL MUNICIPALITIES Pre-Ban Post-Ban Mean SD Mean SD Total grocery expenditure (in euros) 60.30 41.54 62.17 43.06 Total number of units purchased 50.46 37.17 50.44 37.05 Share of private labels (%) 55.98 23.57 56.06 23.44 Share of purchases on promotion (%) 20.24 17.73 20.28 17.52 Number of shopping trips 2.64 1.85 2.49 1.79 Number of different retail chains visited 2.06 1.05 2.01 1.04 Trip share HDs vs. traditional retailers (%) 23.77 29.49 23.66 30.00 Grocery expenditure at primary chain (in euros) 39.88 35.17 39.82 36.85 Number of shopping trips to primary chain 1.46 1.14 1.35 1.11 Notes: Pre-ban and post-ban refer to 52 weeks before and after the ban, respectively.

Number of treated (control) households: 892 (32,303) for variables unconditional on a trip observed in a week, and 361 (13,474) for variables conditional on a trip observed in a week. For a description of the sample selection process see the section “Estimation Sample (Treated and Control Households)”. Share of private labels is the percentage of private label units, out of total units purchased in a given week. Share of purchases on promotion is computed in a similar way. HD = hard discounter. Aldi and Lidl are coded as HDs, all other retailers as traditional retailers. The primary chain is defined as the chain to which the household allocated most of its expenditure prior to the introduction of the ban.

METHOD We analyze the impact of introducing a ban on unsolicited store flyers by comparing changes in households’ shopping behavior using households from municipalities where a ban was introduced to households from municipalities where such a ban was not (yet) present. In terms of the comparative approach, two characteristics of our setting require special care. First, as Figure 1 indicates, the adoption of the ban has been limited and concentrated in larger cities in the western part of the Netherlands. The average household from the control municipalities thus may not only differ in location but may also differ in other dimensions relevant to grocery shopping behavior compared to households in the treatment municipalities. Because our approach relies on a before-after-with-control household framework, we need

17 an approach that ensures a good comparison group. Second, the ban was introduced in a staggered manner, so we need a model that can accommodate staggered treatments (Goodman-Bacon 2021). Before discussing our comparative approach in detail, we discuss how we select an identification strategy suitable for our study setting. Identification Strategy Commonplace methods to analyze such settings are the difference-in-differences (DID) method, the synthetic control (SC) method, and the recently proposed synthetic difference-in-differences (SynthDID) method. While these models all rely on a parallel trends assumption,7 these models differ in how control units and time periods are selected, reflected in different model restrictions. We summarize these differences in Table 3. The regular DID places the strongest restrictions by weighting all controls equally. The SC method relaxes this restriction and creates a weighted combination of controls with weights chosen such that the average pre-treatment outcome of the controls is approximately equal to the average pre-treatment outcome of the treated units (with the weights restricted to be positive and to sum to one and without allowing for a baseline difference between treated and control units, i.e., a “zero intercept” restriction; Li and Shankar 2023).

Importantly, in our case, the treatment is not randomly allocated to municipalities in the Netherlands and tends to focus on the larger ones. Households living in control municipalities may be different from households living in treatment municipalities and exhibit different shopping behavior, on average. Given these differences, equally weighting all households (as in DID) is theoretically unappealing, and a method like SC that flexibly adjusts the weight of each control household would be preferred. Indeed, by “dropping some controls that are (often weakly) negatively correlated or uncorrelated with the treated unit” (Li 2020, p. 2068), SC can reduce the estimation variance compared to DID. At the same time, as Arkhangelsky et al. (2021) note, SC weights tend to be sparse

7

While DID relies on the assumption that a treated unit’s outcome would have been parallel to the average control unit’s outcomes in the absence of the treatment, both SC and SynthDID rely on the assumption that a treated unit’s outcome would have been parallel to a weighted average control unit’s outcome in the absence of the treatment. An untestable part of the identifying assumptions is that the correlation structure between treatment and (potentially weighted) control units continues into the post-treatment period.

18 such that a few controls may be very influential (see their Figure 1, p. 4095). Yet, these few controls may be matched on noise (i.e., the SC method may overfit in the case of many potential controls; see Abadie 2021 and Li and Sonnier 2023), challenging the validity of the counterfactual outcome, and thereby, the validity of the estimated treatment effect. The synthetic difference-in-differences (SynthDID) method proposed by Arkhangelsky et al. (2021) is attractive because it introduces a regularization parameter to increase the dispersion of the weights (such that none of the controls have a particularly strong influence), which is particularly attractive in the case of many potential controls (as is the case in our setting). It also allows for baseline differences between treated and control units (relaxing the “zero intercept” restriction of the SC method), which, together with the regularization parameter, enables a more balanced weighting with less sparse weights (Arkhangelsky et al. 2021, p. 4094). Next to that, the SynthDID method also introduces time weights next to unit weights that can further “remove bias and improve precision by eliminating [pre-treament] time periods that are very different from post-treatment periods” (Arkhangelsky et al. 2021, p.

4090), relaxing the equal weights or zero weights restriction of DID and SC, respectively.8 As Arkhangelsky et al. (2019, 2021) show, the SynthDID method comes with a good biasvariance tradeoff and the additional parameters come at limited costs of additional variance.9 Nevertheless, we note that estimates stemming from more restrictive approaches should be more precise if their respective assumptions hold. Last, we note that in the case of a staggered adoption we rely on an additional assumption, namely that of adoption exogeneity, which deals with the order of the treatment across cohorts. More specifically, the effect of each treatment should be mean independent of the cohort treatment sequence.

8

While our setting provides a theoretical rationale for the usage of unit weights, an equally strong motivation for the time weights is absent. In our main model, and based on the empirical findings of Arkhangelsky et al. (2021), we include both types of weights, whereas in a robustness check we restrict the time weights to be equal. Should such a restriction be warranted, our estimate for the treatment effect should be more precise in this restricted version. 9 Specifically, Arkhangelsky et al. (2019) show in simulations how SynthDID outperforms SC (both with and without penalized weights) in terms of both RMSE and bias in most cases (Tables 1, 2, 4 and 5). Next to SynthDID, other approaches have been introduced that relax some of the restrictions of DID and SC. A comparison of all these approaches is beyond the scope of this paper and we refer to Li and Shankar (2023) and Li and Van den Bulte (2023) for an excellent discussion on some of these approaches.

19 This assumption “rules out the possibility that a group gets treated because it experiences negative shocks” (De Chaisemartin and d’Haultfoeuille 2020, p. 2968). As discussed in the “Setting and Institutional Details” section, there is no coordination across municipalities that would make this assumption untenable. We next discuss the SynthDID approach in more detail, which we use in our focal analysis. In the “Results” section, we show the results of the DID method as a robustness check.10 TABLE 3: COMPARING DID, SYNTHETIC CONTROL, AND SYNTHDID Control Units Pre-Treatment Time Periods Equally weighted but allowing for a Equally weighted but allowing for a baseline difference between treated and baseline difference between precontrol units treatment and post-treatment periods

DID

Synthetic Control Weights chosen such that the weighted average pre-treatment outcome of the controls is approximately equal to the average pre-treatment outcome of the treated units

Zero weighted

SynthDID

Weights chosen such that the weighted average of the pre-treatment outcome of the controls is approximately equal to the post-treatment outcome of the same controls, allowing for a baseline difference between pre-treatment and post-treatment periods

Similarly weighted as in SC but regularized to increase the dispersion of the weights and allowing for a baseline difference between treated and control units

Synthetic Difference-in-Differences The identification strategy relies on a stacked, SynthDID approach (for similar approaches see Berman and Israeli 2022 and Li et al. 2022), which not only can handle staggered introductions but also minimizes pre-treatment differences in the relevant grocery shopping behavior between households in treated and control municipalities. As noted above, the SynthDID estimator constructs a synthetic control group that matches the pre-treatment outcomes of the treated households up to a constant. Importantly, matching on pre-treatment outcomes allows us to indirectly match on unobservable factors. That is, to the degree that these factors cause co-variation in pre-treatment shopping behavior between treated and control households, they are implicitly included in the weighting approach (for a similar reasoning, see

10

As discussed, the SC method does not regularize the weights on the potential controls, resulting in potentially overfitting issues. We return to the SC method in the “Results” section.

20 Abadie 2021). In addition, as explained above, SynthDID also allows for time-varying weights, because some pre-treatment periods may be more relevant in constructing the synthetic control. That is, the time weights allow for a focus on a subset of pre-treatment time periods, such that the weighted average of pretreatment periods predicts average post-treatment outcomes (up to a constant). In sum, what SynthDID does is to reweight control units and time periods and subsequently apply a DID. Next, we formally discuss the implementation of the staggered SynthDID for our setting. The staggered introduction of the ban requires careful computation and aggregation of treatment effects (such as to a common treatment time), to avoid making comparisons between units that are both already treated (Roth et al. 2023). Thus, to analyze the multiple introductions of the ban at different times, we follow Berman and Israeli (2022) and Li et al. (2022) and determine the effect of the ban per cohort (r) of introductions separately and then aggregate them into an overall treatment effect (Arkhangelsky et al. 2021, p. 4114). Formally, to evaluate the effect on grocery behavior Yitr of household i in week t in cohort r we use: arg min (τ#! , & α"! , α 12 &#! , γ#$! ) = τ! , α"! , α#! , γ$!

ℓ!,#$%

2 (Y#$! − α"! − α#! − γ$! − ban_post #$! ∙ τ! )% ω & #! λ>$! ?, (1)

#∈)! $'ℓ!,#&'

where τ#! is the estimated effect of the introduction of a ban in cohort r; α"! is an intercept; α#! and γ$! are household and week fixed effects, respectively; N! is the set of eligible households in both the treated and control municipalities for a given cohort for which we observe a balanced panel; ℓ!,+#, denotes the start of the analysis window for cohort r, whereas ℓ!,+-. is the end; ban_post #$! is an indicator of whether household i in cohort r resides in a municipality in which the ban was active during period t; ω & #! and λ>$! are unit weights for the control households and time weights, respectively, where the unit weights are chosen such that the pre-treatment period of the controls has a parallel trend to the households in treated municipalities and the time weights are chosen such that the pre- and post-period for the controls are similar (up to a constant). As in Arkhangelsky et al. (2021), the remaining idiosyncratic error is assumed to be Gaussian. We compute the overall treatment effect (τ#), as well as its standard error using the treated

21 units in all cohorts following the approach outlined in Clarke et al. (2023). Before turning to the estimation results, we discuss the sample used for each cohort. Estimation Sample (Treated and Control Households) The total pool of eligible households for our estimation sample contains all households for which we have complete information (e.g., municipality in which they reside). The treatment group for each cohort consists of all households residing in a municipality that introduced a ban at that time. We begin with an intent-to-treat (ITT) estimate, where we include all households within a treated municipality, regardless of whether they opt in. An ITT is a useful measure to understand the effect of the introduction of a ban at the population level (cf. the treatment of not receiving flyers anymore unless they opt in) as this is the level of implementation and interest for policymakers (Imbens and Rubin 2015, p. 514).11,12 Moreover, ITTs are advised in the presence of incomplete data on treatment compliance (Gupta 2011), which is the case for households’ opt-in decision. To estimate the effect of not receiving unsolicited flyers anymore, we also consider a local average treatment effect (LATE) estimate for households that did not opt in and stopped receiving flyers.13 We report these in the “Subgroup Analysis” section.

In terms of the control households, we consider all households as potential controls for each cohort, as long as the municipality in which they are located has not yet been treated. The degree to which any such household is relevant as a control for each treatment cohort is determined by the SynthDID procedure, which allocates weights according to the pre-treatment period similarity between treatment and control households on the dependent variables. Table 4 specifies the timeline of the introduction of bans across cohorts and households serving as controls for each.

11

The FDA, for example, requests ITT estimates for approval of new drugs (Pearl 2000, p. 261). We mainly expect an effect for households that do not opt in and stop receiving store flyers. Including households for which the situation did not change may therefore dilute the effects. Nevertheless, other households may have adjusted their grocery shopping behavior too. For instance, previous research shows that opting in tends to make consumers more responsive to marketing communications (Godinho de Matos and Adjerid 2022). We explore this heterogeneity in a subgroup analysis where we report results separately for each set of households depending on their opt-in decision. 13 In the terminology of Imbens and Rubin (2015, p. 514), our ITT estimate reflects the assignment to treatment (i.e., default change), while our LATE estimate reflects the receipt of treatment (i.e., not receiving flyers anymore). 12

22 TABLE 4: BANS ACROSS COHORTS AND TREATED AND CONTROL GROUPS N N Coh. Municipality Introduction 2017 2018 2019 2020 2021 Treated Control 1 Amsterdam January 2018 174 7,336 2 Haarlem January 2020 Tilburg January 2020 293 7,001 Utrecht January 2020 3 The Hague July 2020 183 6,027 4 Leiden October 2020 29 5,971 5 Rotterdam November 2020 213 5,968 Other Notes: coh. = cohort.

= Pre-ban period

= Post-ban period

= Households in municipality eligible as control

For each of the cohorts, we use an analysis window of ±52 weeks around the introduction of the ban to ensure pre-treatment similarity encompasses any seasonal variations (see also Table 4).14 We only retain households in each cohort that are part of the household panel for the entire period. Furthermore, this analysis requires a balanced panel (i.e., no gaps or left- or right-censoring). Although for some dependent variables (e.g., grocery expenditure), we do not require the household to have made a trip to a store in all weeks to remain in the panel, for other dependent variables (e.g., share-based measures), we drop households for which we do not observe a trip in all weeks considered. Table 5 reveals the total number of households included: The total number of observations we used to estimate our model equals 3,452,280 for dependent variables unconditional on a trip and 1,438,840 for dependent variables conditional on a trip. Web Appendix B contrasts average household characteristics of treated and control households, both overall and by cohort. Web Appendix C shows the pre-treatment outcomes for the SynthDID control and the treated group for all cohorts, which indicates that seasonality is similar for the SynthDID control and the treated group prior to the implementation of each ban.

We also provide figures showing the average pretreatment evolution of the raw (i.e., unweighted) data series. To contrast the quality of the SynthDID control vs. the raw data vis-à-vis the treated group, Table 6 shows the average pre-treatment correlations

14

In robustness checks, we set the window to one quarter (±13 weeks) and half a year (± 26 weeks), which capture more short- and medium-term effects. We find substantively the same results across all three windows.

23 by dependent variable across cohorts. On average, the outcomes of the SynthDID control are more highly correlated with the outcomes of the treated group (.86) than the raw data (.64) in the pre-treatment period, but not so high as to cause concerns of overfitting. TABLE 5: NUMBER OF HOUSEHOLDS AND OBSERVATIONS USED IN SYNTHDID Number of Households Number of Observations Treated Control Total Unconditional on trip observed in a week Total grocery expenditure Total number of units purchased Number of shopping trips 892 32,303 33,195 3,452,280 Grocery expenditure at primary chain Number of shopping trips to primary chain Conditional on trip observed in a week Share of private labels Share of purchases on promotion 361 13,474 13,835 1,438,840 Number of different retail chains visited Trip share HDs vs. traditional retailers Notes: The total number of eligible households consists of all 15,486 households for which we have background information (e.g., municipality in which they reside). Of these households, 1,883 reside in a treatment municipality and 13,603 in a control municipality. A household can used as a control for multiple cohorts as long as it is not (or not yet) exposed to any treatment itself. The number of households in this table reflects the treated and control households that are part of the panel for the entire 104-week period.

The number of observations reflects the 104 weeks of data that we consider for each household. HD = hard discounter.

TABLE 6: PRE-TREATMENT CORRELATION TREATED AND CONTROL Raw SynthDID Total grocery expenditure .87 .94 Total number of units purchased .82 .91 Share of private label .37 .78 Share of purchases on promotion .64 .82 Number of shopping trips .71 .87 Number of different retail chains visited .51 .82 Trip share HDs vs. traditional retailers .17 .77 Grocery expenditure at primary chain .81 .92 Number of shopping trips to primary chain .83 .92 Average .64 .86 Notes: Correlations are averaged across cohorts. For SynthDID, the control households are weighted as described in the “Synthetic Difference-in-Differences” section.

RESULTS Table 7 reveals that the effect of a ban on unsolicited store flyers on total grocery expenditures is .40 euro, with a standard error of .43. The 95% confidence interval ranges from -.45 to 1.24 and includes zero. Irrespective of statistical significance, an effect of .40 indicates a change of less than 1% (i.e., mean

24 spending across treated households prior to the ban was 55.08; .40/55.08 = .73%), with just .01 standard deviations (i.e., .40/40.58 = .01). That is, the effect appears, managerially and economically, unimportant. For the other dependent variables, we similarly find estimated parameters that are statistically not significant and economically small.15 Following suggestions by McShane et al. (2024), Web Appendix D shows interval estimate curves for each dependent variable, for all levels from 0% to 99.9%. Importantly, across all dependent variables, the confidence interval includes zero across a wide range of values. TABLE 7: SYNTHDID ESTIMATES OF THE IMPACT OF INTRODUCING A BAN 95% Confidence Estimate Interval Jackknife Lower Upper 𝛕# p-Value SE Bound Bound Total grocery expenditure (in euros) .40 .43 -.45 1.24 .36 Total number of units purchased .09 .36 -.62 .80 .81 Share of private labels (%) -.26 .38 -1.02 .49 .49 Share of purchases on promotion (%) -.41 .26 -.92 .10 .12 Number of shopping trips .01 .02 -.02 .05 .46 Number of different retail chains visited .00 .01 -.03 .02 .88 Trip share HDs vs. traditional retailers (%) -.05 .53 -1.09 .98 .92 Grocery expenditure at primary chain (in euros) .19 .40 -.60 .98 .64 Number of shopping trips to primary chain .00 .01 -.02 .03 .74 Note: HD = hard discounter.

Standard errors are derived using the Jackknife method using the procedure outlined in Clarke et al. (2023). The bootstrap procedure leads to virtually similar standard errors.

To understand if the null results are driven by particular choices in our research design or a lack of power, we ran several robustness checks and conducted a power analysis. We first discuss and report the robustness checks. First, for outcome measures that are not expressed in shares, we estimate the same model for a log-transformed version of the dependent variables (i.e., total grocery expenditure, total number of units purchased, number of shopping trips, grocery expenditure at primary chain, and number of shopping trips to primary chain).16 Second, estimating the model using a ±52-week window might

15

Next to grocery expenditure and number of shopping trips to the primary chain, we also assessed changes in these variables at the secondary and tertiary retail chain and similarly did not find any significant changes. 16 The choice of functional form is important (Goldfarb, Tucker, and Wang 2022), as applies for DID frameworks (Roth et al. 2023). Our SynthDID approach maximizes the degree to which the treatment and control households have parallel trends in the pre-treatment period. The assumptions that such parallel trends hold for the monotonic transformation of the dependent variable are relatively strict (Roth and Sant’Anna 2023). For the transformed dependent variables, we estimate another SynthDID regression that creates a control group based on the transformed, rather than original, dependent variables, again increasing similarity in pre-treatment trends.

25 restrict the sample and decrease statistical power. 17 Therefore, we re-estimate our SynthDID model using ±26-week and ±13-week windows and including all households for which we observe panel membership in these shorter windows, such that we expand the set of eligible households.18 Third, considering that the ban was implemented in a staggered way, regulators may have paid special attention to the first ban, in Amsterdam in 2018, as it predates the other implementations by at least two years. Thereafter, regulators in other municipalities may have adjusted the way they implemented the subsequent bans. We recompute the estimates for Amsterdam only, as well as for all other municipalities, dropping Amsterdam. Fourth, to understand if our SynthDID estimator yields different results from a staggered two-way fixed effects DID estimator, we estimate the main model using this method. We also re-estimate the SynthDID model restricting the time weights to be equal, which should result in more precise estimates in case such a restriction is warranted.19 Table 8 contains the parameter estimates for all robustness checks. Log-transforming the measures does not alter the findings, as all estimates are not significant and economically small. Changing the analysis window to ±26 or ±13 weeks does not substantially alter our findings either.

The parameters are comparable in size, and continue to fail to reach significance, despite the increase in the number of households in the sample. For this overlapping but slightly different sample, only the number of different retail chains visited appears to decrease somewhat in the analysis with a ±13-week window, yet the effect is economically negligible (.03 fewer retail chains per week, i.e., it would take more than 33 weeks for a

17

In our main analyses for each cohort, we only include people who do not leave the panel throughout the estimation window (±52 weeks). Thus, our analysis is based on households who stay in the panel for at least two years. We also run our analyses on households who stay in the panel for the entire period (2017-2021) and find results that are substantially the same: For eight out of nine measures the treatment effects are not significant. Only for the share of purchases of promotion, do we find a small decrease of .74%-points (τ" = -.74, p = .02). However, we note that by conditioning on households that stay in the panel for the entire period, older households (which are more likely to stay in the panel) make up a larger share of the sample. Our treatment heterogeneity analysis reported in a next section shows an effect on the share of purchases on promotion for this group, and their effect thus gets a larger weight in the overall treatment effect. Regardless, economically this change of less than one percentage point is small compared with the average share of purchases on promotion in the pre-treatment period of 21.6%.