2.1 The health club

The study was carried out in collaboration with one of the largest health clubs in Gothenburg, Sweden. The club is a nonprofit organization, has four facilities and records over 800,000 visits per year. Three facilities offer free workout areas, as well as a large range of group exercise classes led by fitness instructors (more than 200 per week). The fourth facility is a large climbing hall. Contracts can be bought for access to a single facility, or to all facilities (‘Multi card’). Access to each of the four facilities requires the scanning of an electronic membership card. Participation in a group exercise class requires an additional scan. Gym attendance is thus almost perfectly observed. Because many classes are at risk of being crowded, each class has a participant limit, and members can sign up for classes in advance. We discuss the booking and cancellation policy in Sect. 3.4.

Fig. 1 Gym attendance (July 1, 2016–June 30, 2017)

2.2 Sample selection, randomization and balance

From the health club, we received all data on gym attendance, class bookings, class booking cancellations and class no-shows for the time period from July 1, 2016, to June 30, 2017, for all individuals who purchased a 12-month contract between July 1, 2016, and December 1, 2016 (2881 individuals).Footnote ⁸ We select individuals who remained active members on December 1, 2016, which was true for almost all members, as an annual membership cannot be canceled during its duration.Footnote ⁹ Furthermore, we exclude members who did not provide a valid email address when registering with the gym, leaving us with a final sample of 2463 gym members.

In Fig. 1, we show attendance statistics for this sample. Altogether, we observe 115,963 gym visits, of which 88,217 are free training and 27,746 are class attendances. Panel (a) shows the distribution of free training visits across the four facilities. Facility 1 is the most popular facility, with 55% of all visits. The gym classes vary across more than 37 different types, which we break down into six categories. The distribution of participation across these six categories is presented in panel (b) of Fig. 1, while the distribution of visits across all 37 specific class types is shown in Fig. 1 in the Online Appendix. The most popular classes are indoor cycling (spinning), bodypump (muscle strength training using free weights) and yoga.

Table 1 Pre-treatment characteristics of the treatment and control groups

	Control group				Treatment group
	mean	sd	min	max	mean	sd	min	max	p-val. t-test
Age	30	10	14	79	30	11	16	80	0.77
Male	0.59	0.49			0.58	0.49			0.50
Student	0.51	0.50			0.54	0.50			0.10
Recurring member ${}^a$	0.49	0.50			0.44	0.50			0.01
Membership type:
Multi card (and CrossFit) ${}^b$	0.41	0.49			0.40	0.49			0.66
Facility 1	0.32	0.47			0.34	0.47			0.43
Facility 2	0.10	0.30			0.10	0.31			0.73
Facility 3	0.12	0.32			0.10	0.30			0.34
Facility 4	0.05	0.23			0.06	0.23			0.86
Daytime card	0.04	0.19			0.06	0.23			0.05
Date of purchasing contract ${}^c$	23 sep 2016	38	01 ju l2016	01 dec 2016	23 sep 2016	39	01 jul 2016	01 dec 2016	0.66
Weekly (pre-experiment) attendance: ${}^d$
Gym visits	0.98	1	0	7	0.88	0.96	0	5.8	0.02
Free training	0.77	0.97	0	6.8	0.69	0.89	0	5.8	0.03
Class training	0.21	0.49	0	3.4	0.19	0.46	0	3.4	0.43
Observations	1232				1231

${}^a$ A ‘Recurring member’ is someone who had an active contract at some point during the six months prior to our sample inflow period (January 1, 2016 –June 30, 2016).

${}^b$ A CrossFit membership is similar to a ‘Multi card’ membership but also allows entry to CrossFit.

${}^c$ For the distribution of the dates of contract purchases in the control and treatment groups, see Fig. 2 in the Online Appendix.

${}^d$ Attendance statistics are computed over the period from December 2, 2016 to January 8, 2017 (this is the pre-experiment period for which we have attendance data for all individuals)

We randomly assigned these individuals into treatment and control groups in the first week of December 2016. The experiment, which we describe in detail below, began on January 9, 2017 (see Fig. 2 for a timeline of our setup). We present descriptive statistics in Table 1, which contains the mean, standard deviation, minimum and maximum for the control group (columns 1–4) and for the treatment group (columns 5–8) and the p-value of a t-test for equal means (column 9). The top panel presents individual characteristics, the second panel membership and contract details. The average age is 30, a share of 58% of the gym members are males, 52% registered as students and 46% had been members of this gym previously. A total of 40% bought a Multi card, and 5% bought a membership that is valid only during daytime hours (a ‘daytime card’). The mean date of purchasing the contract is September 23 for both groups (see Fig. 2 in the Online Appendix for the full distributions of contract buying dates). Most variables do not differ significantly between control and treatment groups, with the exception of a slightly lower share of recurring members and a slightly higher share of members who bought a daytime card in the treatment group.

The five-week period of pre-experiment gym visit observations (December 2, 2016–January 8, 2017) allows us to compare the control and treatment groups in terms of attendance. In the lower panel of Table 1, we find that the treatment group has a significantly lower number of weekly visits in the pre-experiment period, and this difference is caused by a lower number of free training visits. In Sect. 3.1, we discuss that we control for these differences by including individual fixed effects when estimating the impact of the reminders. Note that the number of weekly visits is lower in this pre-experiment period than is typically the case because this time period includes the Christmas holidays, during which gym attendance is low. In Fig. 3 in the Online Appendix, we compare the distributions of gym visits of the control and treatment groups across facilities, class types and weekly number of visits and find that the groups are similar.

Fig. 2 Timeline of the experiment

2.3 Experiment details

The intervention consisted of a series of email reminders that were dispatched to the treatment group between January 9, 2017, and April 9, 2017 (see Table 7 in “Appendix” for the dates).Footnote ¹⁰

The reminders were sent from the gym’s email account once per week, and they contained a short message (typically no longer than three sentences) encouraging the recipient to attend the gym. In addition, they contained a picture related to the gym and a link to the club’s website (for an example, see Fig. 4 in the Online Appendix). Header, text and picture differed every week in order to attract the recipients’ interest and make them more likely to open and read the reminders. Most emails referred to the various exercise options available at the club or reminded the reader about the potential benefits of attending the gym.Footnote ¹¹ An example of a reminder is the following: “Did you know that we offer more than 200 classes per week? Drop in any time to work out, or sign up for a class on www.fysiken.nu/en/book/. We hope to see you soon!” The complete list of reminders can be found in “Appendix”.Footnote ¹²

Each reminder email contained a line at the bottom explaining that the readers had received this email because of their gym membership and that they could unsubscribe by clicking on a link. When members unsubscribed, they were removed from our email list and did not receive any further email communication related to the study.

Receiving emails from the gym is not unusual for members. The gym has a policy of sending out an automated welcome email when a new member signs up. Furthermore, automated emails are sent when a new member has not attended the gym for 90 days (though these emails were suspended during our experiment). A few times per year, all members receive a newsletter (unless they have unsubscribed from this service). Both the control and the treatment groups received such a newsletter once during the experiment. The starting date and the end date of the email reminders were unknown to participants. Finally, the days on which the reminders were dispatched were randomized between Sundays, Mondays and Tuesdays in order to make sure that members in the treatment group did not expect to receive a reminder on a particular weekday.

The effectiveness of email reminders obviously depends on whether the recipient receives (and notices) the reminders. An email might not be received because, for example, members have misspelled their email address or registered an address that they fail to use, or the emails have ended up in their spam folders. Even if the email appears in the user’s inbox, it may be deleted without being opened (although in that case, its impact could already have been achieved if it brought the gym to the top of the receiver’s mind). Since email reading behavior is likely to depend on individual characteristics, selecting a sample of recipients who have responded to an email, as in Calzolari and Nardotto (Reference Calzolari and Nardotto2017), may imply that the sample is also more responsive to subsequent email reminders than the average gym population.

To what degree emails are received is difficult to assess, because whether someone opens and reads a particular email is not typically observed. We address this issue in two ways. First, we observe a proxy for whether each email has been opened using so-called ‘web beacons’, which record whether the picture included in the email has been downloaded. This measure of email opening is not perfect because not every email client downloads the picture by default. An email can thus be read without downloading the picture, implying that our obtained measure provides a lower bound for the opening rate.

Second, we sent out a ‘baseline email’ to our entire sample about five weeks prior to the start of the study. In this email, we briefly described the widely known challenge of achieving one’s exercising goals and asked the recipients whether they believed that regular email reminders could help them improve in this regard. If they thought that regular reminders could indeed be helpful, they were asked to click on a button in the email.Footnote ¹³ The baseline email provides a measure of which members—in both the control and treatment groups—open emails. In addition, when someone clicked on the button, we know with certainty that the email was read. We will make use of the web beacons and the baseline email in the empirical analysis to identify a subgroup of individuals who are likely to open and read emails so that we can estimate heterogeneous effects for this group (see Sect. 3.3).

2.4 Opening of emails and unsubscribing

Before we analyze the impact of our reminders, we show some statistics on the email opening rate for our reminders and on members’ unsubscription from our email list.

Fig. 3 Number of emails sent and opened

Weekly unsubscribing is measured after each reminder email. It is important to note that unsubscription is not equivalent to attrition in our study. We observe gym attendance (or nonattendance) for all individuals in the study. Unsubscription merely implies that fewer emails are received. In Fig. 3, we present the weekly number of emails that were dispatched. While the number of email addresses on our list declined steadily, 91% of all individuals in the treatment group remained on the mailing list at the end of the intervention. Thus, weekly unsubscription is approximately 1%. In the same figure, we show the number of delivered emails that we know with certainty were opened, i.e., those for which the picture was downloaded. Considering that this percentage is a conservative estimate, the opening rate is quite substantial: 46% in the first week, decreasing to 36% in the final week.

Table 2 Regression of the email opening rate on individual characteristics

	(1)
	Share of email reminders that is opened
Male	– 0.066***
	(0.020)
Age 21–25	0.12***
	(0.038)
Age 26–30	0.12***
	(0.039)
Age 31–40	0.079*
	(0.043)
Age >40	0.19***
	(0.048)
Student	0.028
	(0.022)
Recurring member	0.024
	(0.020)
Opened the initial email	0.11***
	(0.018)
Clicked link initial email	0.100**
	(0.046)
Constant	0.17***
	(0.048)
N	1111
$R^2$	0.166

*p < 0.10, ** p < 0.05, *** p < 0.01. Standard errors clustered by individual in parentheses. In addition to the variables above, six email client dummies are included in the regression. The sample contains only the treatment group and excludes 120 individuals for which the sex variable is missing

To assess whether certain types of individuals are more likely to open the email, we regress the share of reminders that are opened on individual characteristics. The results are shown in Table 2 (clearly only the treatment group is included). We find that men are significantly less likely to open emails (– 7%-points). The same holds for gym members aged below 20 years (with the difference between this group and most other age groups being more than 10%-points). We find no differences for students or recurring members. Furthermore, we find that responding to the baseline email is, unsurprisingly, a good predictor of opening the reminder emails. Opening the baseline email is associated with an 11%-points increase in the share of reminders that are opened during the study. Clicking on the link in the baseline email adds another 10%-points increase.

3.1 Impact on gym attendance

Fig. 4 Weekly gym attendance

We show the average weekly number of gym visits in the control and treatment groups in panel (a) of Fig. 4. On average, individuals visit the gym around once per week (with the exception of a large dip around the Christmas break). The time trend is negative and can have two possible explanations. First, our sample contains members with new contracts, and attendance typically declines over the course of the membership (e.g., DellaVigna and Malmendier Reference DellaVigna and Malmendier2006; Garon et al. Reference Garon, Masse and Michaud2015). Second, higher temperatures and longer hours of sunshine might drive gym members from indoor to outdoor activities in spring and summer.Footnote ¹⁴

The first vertical line in Fig. 4 indicates the start of the experiment period in which the email reminders were sent. As mentioned earlier, the control group has a slightly higher gym attendance than the treatment group in the weeks before the experiment begins (but the trends look extremely similar). Almost directly after the reminders begin, this pattern reverses, and the treatment group has a slightly higher attendance than the control group, see panel (a). In panel (b), we find that the impact of the reminders on class training is particularly pronounced. Class attendance is higher for the treatment group in all experiment period weeks, while the two groups have almost identical pre-experiment class attendance. In panel (c), we show the average number of free training sessions per week. Finally, in panel (d), the difference between the treatment and control groups for each of the three variables is depicted. The diagram clearly shows that the lower attendance of the treatment group in the pre-experiment period reverses to higher attendance after the email reminders begin.

The second vertical line indicates the end of the intervention, after which no further reminders are sent. We observe attendance until June 30. After that, the vacation period begins, during which gym attendance is traditionally very low and the number of offered classes is greatly reduced. Furthermore, extending the postexperiment period beyond this day would imply that we would lose participants in our sample since some of them will not prolong their contracts. The negative trend in weekly attendance clearly continues after the experiment ends. The difference between the control and treatment groups is smaller than it is during the experiment but still suggests a slightly higher average attendance for the treatment group (especially when taking the pre-experiment difference into account). As shown in panel (d), for each of the three lines, the difference is either (slightly) positive or close to zero during the postexperiment period.Footnote ¹⁵

To obtain estimates of the impact of the reminders, we compute the average weekly attendance in the pre-experiment and experiment period for the control and treatment groups.Footnote ¹⁶ The simple DiD estimate for the total number of gym visits is 0.12 additional visits per week as a result of the email reminders, which is equivalent to an 11% increase. The additional visits consist of 0.045 additional classes (17% increase) and 0.083 additional free training sessions (10% increase). Over the 12 weeks of the experiment, this effect aggregates into 1.5 extra visits on average for each individual who received the reminders. Given that marginal costs of the intervention are close to zero, this shift can be considered a substantial effect.

We now turn to a regression framework and estimate a DiD model. The impact of the reminders is identified from the assumption that in the absence of the intervention, the control and treatment groups would have had the same time trend in weekly gym attendance. Weekly gym attendance ( $A_{\mathrm{it}}$ ) of individual i in week t depends on week fixed effects ${\alpha }_t$ , individual fixed effects ${\gamma }_i$ and treatment assignment $T_{\mathrm{it}}$ , which is a dummy equal to 1 if individual i is in the treatment group and week t is in the experiment period. Furthermore, we control for membership duration in a flexible way by including a set of dummies for different membership duration intervals ( ${\pi }_{d\left(t\right)}$ ).Footnote ¹⁷ The error term is ${ϵ}_{\mathrm{it}}$ .

(1) $\begin{array}{c}{A}_{\mathrm{it}}={\alpha }_t+{\beta }_1{T}_{\mathrm{it}}^{\mathrm{during}}+{\beta }_2{T}_{\mathrm{it}}^{\mathrm{post}}+{\pi }_{d\left(t\right)}+{\gamma }_i+{ϵ}_{\mathrm{it}}\end{array}$

The parameters of interest are ${\beta }_1$ and ${\beta }_2$ , which measure the immediate and posttreatment effects of the reminders, respectively. From panels (c) and (d) of Fig. 3 in the Online Appendix, it is clear that weekly gym attendance is a count variable with many zeros. Thus, a Poisson regression is more suitable than a linear regression. We report the results for a linear model as a robustness check (see Sect. 3.2) and find that the results are very similar.Footnote ¹⁸ Standard errors are clustered by individual.

The regression results are presented in Table 3, where we report $exp\left(\beta \right)-1$ , which is the percentage effect. We first discuss the immediate impact of the reminders ( ${\beta }_1$ ), which is shown in the first row. We find that total visits increase by 13%, which is significant at the 1% level (column 1). We split these visits into class training and free training in columns (2) and (3) and find that attendance in class exercise training increases by 19%, while free training visits increase by 11%. Although the percentage effect for class training visits is larger than for free training, their much lower base level implies that the impact in terms of additional visits is actually greater for free training (and in fact the difference between the two estimates is not statistically significant).Footnote ^19, Footnote ²⁰

Table 3 Regressions on weekly gym attendance (Poisson models)

	DiD model			Simple difference
	(1)	(2)	(3)	(4)	(5)	(6)
	Visits	Class training	Free training	Visits	Class training	Free training
Experiment (during)	0.13***	0.19***	0.11***	0.072*	0.15*	0.040
	(0.035)	(0.077)	(0.038)	(0.040)	(0.092)	(0.046)
Experiment (post)	0.12***	0.11	0.13***	0.057	0.045	0.057
	(0.046)	(0.091)	(0.053)	(0.053)	(0.10)	(0.062)
Recurring member				0.21***	0.30***	0.19***
				(0.050)	(0.11)	(0.059)
Male				0.21***	– 0.62***	0.82***
				(0.048)	(0.034)	(0.092)
Student				0.0037	– 0.0025	0.016
				(0.048)	(0.11)	(0.056)
Daytime card				– 0.31***	– 0.67***	– 0.17*
				(0.074)	(0.12)	(0.095)
Week and duration FE	Yes	Yes	Yes	Yes	Yes	Yes
Individual FE	Yes	Yes	Yes	No	No	No
Include pre-period	Yes	Yes	Yes	No	No	No
N	66,960	31,530	62,910	55,825	55,825	55,825

Standard errors clustered by individual in parentheses. We report $exp\left(\beta \right)-1$ , which is the percentage effect. Seven age dummies and six gym location dummies are included but not reported in columns (4–6). Note that the number of observations in columns (1–3) varies because individuals with zero attendance in all time periods drop out in Poisson regressions with fixed effects (FE)

*p < 0.10, **p < 0.05, ***p < 0.01

As a robustness check, we also present regressions in which we exclude the pre-experiment period and thus do not include individual fixed effects (columns 4–6 in Table 3). Instead, we include a number of time-invariant individual covariates (a sex dummy, a student dummy, seven age category dummies and a dummy for being a recurring member of the gym).Footnote ²¹ The results are similarly positive, although somewhat smaller in magnitude. Combined with somewhat larger standard errors, only the effect on the total number of visits is statistically significant. This finding was expected, as the slightly lower attendance level of the treatment group in the pre-experiment period is ignored in these regressions. Note that while the control and treatment groups are balanced with respect to most observed characteristics (see Table 1), the share of recurring members is 5%-points higher in the control group. Recurring members typically exercise more frequently, which may explain the slightly higher pre-experiment number of visits within the control group. Thus, we prefer the DiD model that corrects for these (and potentially other) differences.

So far, we have looked at the immediate effect of email reminders on gym attendance. One might expect that once the reminders cease, treated individuals will stop attending the gym at an increased frequency. Persistent effects of a short-term intervention might, however, be explained by habit formation. Habits are acquired when ‘repetition of a behavior in a consistent context progressively increases the automaticity with which the behavior is performed when the situation is encountered’ (Lally et al. Reference Lally, van Jaarsveld, Potts and Wardle2010, p. 998). In our context, the higher frequency of attending the gym might make it easier to attend even when the reminders have ended. Only weak or no evidence of habituation has been found by studies in the field of health behavior (see, e.g., Charness and Gneezy Reference Charness and Gneezy2009; Acland and Levy Reference Acland and Levy2015; Calzolari and Nardotto Reference Calzolari and Nardotto2017; Carrera et al. Reference Carrera, Royer, Stehr and Sydnor2018a, Reference Carrera, Royer, Stehr and Sydnor2020), although this might be due partly to a lack of statistical power.

We present estimates of the impact of the reminders during the postexperiment period ( ${\beta }_2$ ) in the second row of Table 3. We find the surprising result that the postexperiment impact on total visits is—in relative terms—of a similar magnitude as the immediate impact (a 12% increase). The same result holds for the impact on free training visits (column 3). The coefficient for class training in column (2) is slightly smaller, which, combined with less precision due to a lower base rate of attendance of class trainings, leads to the impact not being statistically significant. However, the magnitude of the class training coefficient is very similar to that of the free training coefficient. In contrast to Calzolari and Nardotto (Reference Calzolari and Nardotto2017), our postexperiment effects have the same size as the effects during the experiment period, at least in relative terms, and are statistically significant for the whole sample.Footnote ²²

While these postexperiment results are perhaps larger than expected, it should be stressed that they are less robust, and, in absolute terms, somewhat smaller than the during-experiment effects. First of all, standard errors are larger, indicating less precision. Second, the baseline level of attendance of our sample decreases over time. In particular, this level is lower in the postexperiment period than during the experiment. Since our Poisson model estimates percentage effects, an equal coefficient implies a smaller number of additional visits in the postexperiment period. Third, there is a large outlier in terms of attendance in the treatment group in week 22 (see Fig. 4). The gym sent out a newsletter email to all members in this week, and it appears as if this had more influence on our treatment group than on the control group. This particular week drives some of the positive posttreatment difference. In “the Online Appendix”, we show that the postexperiment effect is smaller than the during-experiment effect if we use a linear model and exclude the outlier in week 22 (see Table 2).Footnote ²³

To conclude, we find clear evidence of a persistent positive effect of reminders on attendance. Interestingly, the effect of the reminders remains substantial after the reminders have ended. We interpret this finding as a sign of habit formation.

3.2 Robustness checks

We perform a series of robustness checks to investigate whether our results are sensitive to choices in the empirical model. First, we estimate the baseline models with simple OLS to assess the sensitivity of the results to the Poisson model. The results are presented in Table 1 in “the Online Appendix”. The statistically significant increase of 0.12 weekly visits translates into a 13% increase, which is very similar to the Poisson regression estimate (13%). The same holds for the effects on class training and free training.

Second, we perform robustness checks with respect to the last two weeks of 2016 (weeks 51 and 52) and the first week of 2017 (week 1), in which gym attendance was substantially below its long-run level (see Fig. 4). Since these weeks are part of the pre-experiment period, they may affect the DiD estimates. In Table 5 in “the Online Appendix”, we exclude either week 52 or weeks 51, 52 and 1 from the analysis. Note that the total pre-experiment period consists of weeks 49, 50, 51, 52 and 1, and thus, we can estimate the DiD model even when excluding the Christmas holidays. We find that excluding either one or three weeks hardly affects our results.

Third, we consider the length of the pre-experiment period. In all DiD estimations, the pre-experiment period consists of five weeks. This period is restricted by the fact that our sample consists of gym members who purchased their contracts between July 1, 2016, and December 1, 2016. As a robustness check, we select a subsample of individuals who purchased their contracts earlier (July 1–October 1) and extend the pre-experiment period accordingly. The results are presented in “the Online Appendix” in Table 6. The DiD estimates for all visits are still positive but smaller in magnitude, which, combined with somewhat larger standard errors, makes them no longer significant. The effect on class training is still large and significant.

Fourth, we consider using daily data on gym visits instead of aggregated weekly data (see Fig. 6 in the Online Appendix). We use a linear specification that is similar to the one used for weekly visits, but we include additional day-of-the-week fixed effects. The results are presented in Table 7 in the Online Appendix. We find that the impact of reminders is very similar to our baseline model in terms of magnitude and statistical significance.

We conclude that the positive effect of reminders on gym attendance is robust against several alternative specifications.

3.3 Heterogeneous effects

The impact of email reminders may vary, depending on an individual’s characteristics. Given our large sample size, we can investigate different sources of heterogeneous effects, and we focus on sex, baseline gym attendance, previous gym membership (at the same gym), student status and a pre-experiment measure of the likelihood of opening emails. We estimate the same model for each particular subsample.Footnote ²⁴ Identification follows from a similar standard DiD assumption as before. We report results only for the total number of weekly gym visits (rather than distinguishing between classes and free training).

We first consider heterogeneous effects by sex. While men and women have similar average numbers of weekly visits (1.16 for men and 1.00 for women), they exercise in different ways. One-third of gym visits by women are class trainings, while the corresponding number is less than 10% for men. In Table 4, we present estimation results for men in column (1) and for women in column (2). We find that the estimates are very similar, and we conclude that reminders are equally effective for both sexes.

Table 4 DiD regressions on weekly gym attendance (Poisson models): heterogeneous effects

	(1)	(2)	(3)	(4)	(5)
	Men	Women	High attenders	Low attenders	Recurring members
Experiment (during)	0.13***	0.11*	0.083**	0.16**	0.13***
	(0.046)	(0.059)	(0.034)	(0.078)	(0.047)
Experiment (post)	0.11**	0.10	0.093**	0.12	0.18***
	(0.060)	(0.076)	(0.049)	(0.10)	(0.066)
N	36,870	26,190	35,070	31,830	31,020

	(6)	(7)	(8)	(9)	(10)
	New members	Student	No student	Opened baseline	Not opened baseline
Experiment (during)	0.13***	0.13***	0.13***	0.12***	0.14***
	(0.053)	(0.050)	(0.049)	(0.045)	(0.056)
Experiment (post)	0.077	0.14**	0.10*	0.12**	0.12*
	(0.065)	(0.068)	(0.061)	(0.061)	(0.070)
N	35,880	35,280	31,620	38,670	28,230

Standard errors clustered by individual in parentheses. We report $exp\left(\beta \right)-1$ , which is the percentage effect. All regressions include individual fixed effects and membership duration dummies

*p < 0.10, **p < 0.05, ***p < 0.01

Second, we consider heterogeneous effects by baseline gym attendance. We split the sample at the median weekly attendance in the pre-experiment period, which is 0.6 visits per week. The estimation results are presented in column (3) for high attenders and column (4) for low attenders and suggest a greater impact on members who attended less frequently than the median. This finding is in line with the results by Calzolari and Nardotto (Reference Calzolari and Nardotto2017) and is not surprising since for high attenders, there is a lower scope to increase the amount of exercising beyond the current level (e.g., due to time constraints). Note, however, that a formal test cannot reject equal coefficients for high and low attenders.

Third, we test whether recurring members are more or less affected by the reminders. Since recurring members extended their previous contract, they are likely to be more committed to exercising, and thus, we expect them to benefit less from email reminders. We do not find evidence supporting this hypothesis, with the coefficients for the two groups being almost identical (columns 5 and 6). This finding suggests that the group of recurring members is perhaps less selective than one might expect.Footnote ²⁵

Fourth, we consider student status. As shown in Table 1, approximately half of our sample consists of students.Footnote ²⁶ While we have no strong hypothesis for differing impacts of the reminders for students and nonstudents (except for maybe differently binding time constraints), we still believe it is important with respect to external validity. For example, previous findings on the effectiveness of reminders by Calzolari and Nardotto (Reference Calzolari and Nardotto2017) were based only on a student population, and thus, we are interested in whether the impact extends to a more general population. The results are presented in columns (7) and (8), and we find that the estimates are virtually identical for students and nonstudents. Thus, the positive effect is present even for a population that is more likely to be (full-time) employed and that has (perhaps) more stringent time restrictions for exercising.

Finally, we consider heterogeneous effects according to whether one opens the baseline email (1405 out of the 2463 individuals in the sample opened this email; see Sect. 2.3). Ideally, one would measure whether those who actually opened the reminders were more likely to visit the gym. However, since those members are a selective subset of the treatment group and because we do not observe opening rates for the control group, we have no valid control for those who opened the reminders. Thus, we use opening the baseline email as a proxy for opening gym emails in general. The results for those who opened the email are presented in column (9) and for those who did not open the email in column (10). We find the rather surprising result that there is no significant difference between the two groups. The coefficient for those who did not open the baseline email is even slightly larger than the coefficient for those who opened the email.Footnote ²⁷ Thus, even for those who are (relatively) less likely to open and/or read emails, we find a significantly positive effect. While somewhat puzzling, this finding can have various explanations.

First, it might be that seeing the email appear in one’s inbox is sufficient to bring the gym to one’s attention and thus overcome limited attention (without actually opening the message). Second, the statistics on downloading web beacons may severely underestimate the actual reading rate: some recipients read the email without downloading the image. It is possible that this kind of measurement error is to some extent correlated with whether individuals open the email, resulting in less reliable estimates. Third, we cannot rule out the possibility that individuals that generally open fewer emails also differ in other personality traits. For example, individuals who are less organized in their daily lives might be more prone to not read emails and, simultaneously, more likely to forget about attending the gym. As a result, the reminders that they do open are particularly effective in nudging them to attend the gym.

In summary, we do not find strong evidence for heterogeneous effects of email reminders, except for some suggestive evidence that low attenders are more affected than high attenders (but the difference is not statistically significant). These findings suggest that nearly all groups benefit from reminders in terms of overcoming their limited attention, which strengthens the case for reminder policies.

3.4 Booking and canceling

In the previous sections, we established that gym members who received email reminders attended gym classes more frequently both during the treatment period and in the three months after the reminders had ended. In this section, we shed light on whether reminders lead only to an almost immediate response of visiting the gym or whether they also stimulate the recipient to plan a future visit by booking a gym class.Footnote ²⁸ Before we proceed with the empirical analysis, we briefly describe the features of the booking and cancellation system and provide some descriptive statistics on booking and canceling behavior.

The classes offered at the gym have a maximum capacity. Members can book a spot in a class online or through a mobile app up to seven days prior to the class. After a booking, the gym does not send any reminders for the booked class. Once all spots are booked, new bookings are placed on a waiting list and result in a spot when earlier bookings are canceled. A booking can be canceled online or through the mobile app up to one hour prior to the class. In the last 60 minutes before the class, members without a booking can claim a spot with the gym’s reception staff if a spot is still available (we refer to this as ‘drop-in attendance’). Finally, those with a prior booking must show up at least 10 minutes prior to the class; otherwise, the booking is canceled and the spot becomes available for drop-in attendance. If a booking is not canceled in time and the individual does not show up, his or her card is blocked from further bookings until a fine of SEK25 (approximately $3) is paid. We refer to these cases as ‘no-shows’.Footnote ²⁹ It is not uncommon for all spots in a class to be taken, often several days in advance. For example, of all 9513 classes for which we have data, 30.7% had a waiting list (at some point). This does not mean that all spots were eventually taken for one-third of the classes because canceling is also very common. However, it does illustrate that booking classes beforehand is often necessary and very common.

Fig. 5 Distribution of bookings and cancellations

Our dataset contains observations for class bookings, cancellations and no-shows of the experimental sample for the period from July 1, 2016, to June 30, 2017. In total, we observe 43,953 bookings and 6114 drop-in attendances. In the upper panel of Fig. 5, we show the distribution of class bookings. In panel (a), we find that the number of daily bookings is approximately uniform across the first six days prior to a class (roughly 10% per day). Around 15% of all bookings are made on the day before a class and another 28% on the day of the class (‘day zero’). Most of the bookings on day zero are made in the very last hours before the class (panel b).Footnote ³⁰ Furthermore, most gym class visits are booked prior to the class (79%) and are not made through drop-in (see also Table 8 in the Online Appendix). In the lower panel of Fig. 5, we show how cancellations are distributed across days prior to the class (no-shows are included in the figure as canceling zero minutes prior to the class). We observe that a significant share of bookings are canceled (42%) and that the vast majority (82%) of all cancellations occur on the day of the class (panel c), 61% of all cancellations even within the final six hours (panel d). Furthermore, slightly more than 5% of all bookings or, equivalently, 13% of all cancellations are no-shows, i.e., never followed up on. As the cancellation costs seem rather low as compared to the costs of not showing up to a booked class (around $3), we take no-shows as evidence for limited attention.

There is substantial variation in the popularity of the classes. In the Online Appendix, we show that a majority of those who attend unpopular classes (which never have a waiting list), still make an early booking. This even holds for experienced attenders of these unpopular classes. We take this finding as evidence that many individuals value bookings as a commitment device to overcome time-inconsistent preferences, i.e., present bias: through making a booking, they reduce their likelihood not to attend the class. See the Online Appendix for further details and discussion.

Table 5 Regressions on weekly class bookings and cancellations of bookings

	(1)	(2)	(3)	(4)	(5)
	Number of bookings (Poisson)	Number of bookings (linear)	Positive # of bookings (linear)	Number of cancellations (linear)	Share of bookings canceled (linear)
Experiment (during)	0.10	0.057*	0.014*	0.026	– 0.023
	(0.068)	(0.032)	(0.0080)	(0.018)	(0.026)
Experiment (post)	0.048	0.017	0.0013	0.0028	– 0.038
	(0.088)	(0.031)	(0.0083)	(0.018)	(0.028)
Mean value dep. var.	0.42	0.42	0.16	0.18	0.37
Percent effect (during)		13	9	14	– 6
N	33,270	73,890	73,890	73,890	11,653

Standard errors clustered by individual in parentheses. In column (1), we report $exp\left(\beta \right)-1$ , which is the percentage effect. Note that the number of observations is lower in column (1) because individuals with zero bookings in all time periods drop out in Poisson regressions with fixed effects. In column (3), the outcome is an indicator variable equal to 1 in the case of a positive number of bookings

*p < 0.10, **p < 0.05, ***p < 0.01

We now proceed with estimating the impact of the reminders on booking and canceling. Limited attention potentially affects bookings and cancellations and thus class participation. First, members may forget to make a booking. Second, given that they have made a booking, they may forget about the booked class. Third, they may not have forgotten about the booked class but they may forget to cancel the booking for this class. We thus expect that email reminders lead to i) more bookings, and ii) fewer no-shows. To test these hypotheses, we estimate a DiD model with individual fixed effects, similar to equation (1), but with different outcome variables.

First, we estimate the impact of the reminders on the number of weekly bookings (column 1 in Table 5), using a Poisson regression. We find an increase in the number of bookings per week equal to 10% (though not statistically significant). Using a linear model (column 2), we find an increase of 0.057 in the number of bookings per week (significant at the 10% level), which translates into an increase of 13%. Given the relatively small share of gym members who attend classes, we also consider the extensive margin of making any positive number of bookings in column (3). We find that reminders lead to significantly more members making at least one booking (an increase of 9%).

We next consider cancellations. In column (4), we show that the number of weekly cancellations increases during the experiment; however, the coefficient is small and not statistically significant. Cancellations are obviously possible only if a booking was made earlier. Thus, we consider in column (5) the share of bookings that are canceled. This regression thus includes only observations for weeks in which the individual made at least one booking. We find a negative coefficient, although it is again small in magnitude and not statistically significant. We conclude that the increase in class visits as a result of the reminders is due to (1) an increase in the number of bookings and (2) a lack of an increase (and perhaps even a decrease) in the share of bookings that are canceled.

The effects of the reminders for the postexperiment period all share the sign of the effect during the experiment. However, none of the effects are statistically significant. This finding is in line with the estimated impact on class attendance for the postexperiment period, which is smaller in magnitude than the estimate for the experiment period and not statistically significant (see Table 3).

3.5 Impact on contract duration and renewal

Having seen persistent effects of the intervention in terms of increased attendance in the postexperiment period, we now investigate whether these increases carry over to the decision on contract renewal once the 12-month contract period ends. One would expect that individuals who were induced by the intervention to exercise more regularly are more likely to remain members of the gym.

Table 6 Contract renewal after initial 12-month period

	Control group	Treatment group	p-value test equal proportions
Full sample:
Active after 13 months	0.57	0.59	0.55
Active after 14 months	0.56	0.55	0.92
N	1232	1231
Upfront (12-month) paid contract:
Active after 13 months	0.49	0.48	0.77
Active after 14 months	0.51	0.48	0.39
N	579	554
Monthly direct debit payments:
Active after 13 months	0.65	0.67	0.38
Active after 14 months	0.60	0.61	0.59
N	653	677

We obtained data on whether individuals buy a new contract (or extend the first contract) and define as the outcome measure an indicator for being a member 13 or 14 months after purchasing the initial contract.Footnote ³¹ Table 6 shows the share of individuals in the control and treatment groups that were members 13 and 14 months after the initial contract began. In the upper panel, we observe that slightly more than half of our sample had contracts both 13 and 14 months after the initial contract began. The share of members with active contracts is very similar in the treatment and control groups, and the difference is not significant (with a p-value of 0.55 after 13 months and 0.92 after 14 months).

The type of payment of the initial contract (upfront or monthly) is likely to affect the likelihood of contract renewal, and thus, we report the same statistics, split by the type of payment, in the lower panels of Table 6. Again, we find no significant differences between the control and treatment groups for both payment methods after 13 months or after 14 months. Interestingly, the number of contracts is much higher among those who had initially chosen direct debit payments compared to those who had paid upfront. This finding suggests that there is some kind of cancellation delay for contracts with direct debit payment, as also reported by DellaVigna and Malmendier (Reference DellaVigna and Malmendier2006), although some of this difference may result from self-selection into the two payment types.Footnote ³²

There are several explanations for why we do not observe any effects on contract duration and renewal. First, if the decision maker is perfectly rational, it could be that the magnitude of the increase in attendance induced by the intervention does not suffice to affect the bigger and financially consequential decision of buying another contract or prolonging the existing one. Second, assuming that the decision maker is not fully rational, she may not update her expectations about future attendance based on past experience and is, if she is in the treatment group, not more likely to prolong the contract than if she were in the control group. Third, some individuals may suffer from a status quo bias (Samuelson and Zeckhauser Reference Samuelson and Zeckhauser1988), taking the current baseline, i.e., being a member of the gym, as the reference point, and thus renew the contract, irrespective of any other considerations. That the majority of memberships in our sample are still active after 13 and 14 months speaks to this hypothesis. It is, of course, possible that a combination of these explanations leads to the observed outcome.