Abstract
This paper aims to understand the impact of temporal spacing between ad exposures on the likelihood of a consumer purchasing the advertised product. I create an individual-level data set with exogenous variation in ad exposure and its spacing by running online field experiments. Using this data set, I first show that (1) ads significantly increase the likelihood of the consumers purchasing from the advertiser and (2) this increase carries over to future purchase occasions. Importantly, I also find evidence for the spacing effect: the likelihood of a product’s purchase increases if it’s ads are spread apart rather than bunched together, even if spreading apart involves shifting some ads away from the purchase occasion. Accounting for the spacing effect is important to detect the effects of repeated advertising. Because the traditional models of advertising do not explain the data patterns, I build a new memory-based model of how advertising influences consumer behavior. Using a nested test, I reject the restrictions imposed by the canonical goodwill stock model (Nerlove and Arrow, Economica, 29(114):129–142, 1962), in favor of the memory-based model I propose. Additionally, I use the estimated parameters to simulate counterfactual scenarios and show that the advertisers’ profits might be lower if the features of the memory model are not accounted for.
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Notes
The experiments I report in this study are all the experiments that were conducted. Prior to these experiments, I conducted one pilot study which was a before and after comparison to judge the magnitude of the effect of ads. One experimental restaurant closed between planning and the data collection, therefore the focal restaurant had to be changed. After this paper, the data have been used for the analysis of the competitive effects of the experimental ads, described in Sahni (2014).
I use the term “learning” here to describe retaining of information, as opposed to gaining new information / learning about quality as, e.g., in Erdem et al. (2008).
The website claims to cover all restaurants in these markets; indeed, for the markets this study considers, the number of restaurants in this website’s database is roughly 40 % higher than those returned by searching on the next major competitor.
If the advertiser is a chain, clicking on the ad banners takes the user to a page with links to web pages for the chain’s outlets in the filtered geographic area.
(A) contained different randomized sub-conditions where characteristics of ads, such as their position, were randomized. For analysis in this paper, I pool data from all sub-conditions of (A) to estimate average effects of ads.
These banners show the name of the advertiser and are not too informative; some displayed the restaurant’s logo and included a short three to four-word phrase describing it.
Calls were tracked for 8 out of 11 experiments. The callers were notified of this before the call was forwarded.
Nine out of the 11 experimental restaurants are chains. When the users click on ads, they are shown links to restaurants from the chain located in the geographic area of search. Hence, clicking on ads might not always lead to a visit to the restaurant page.
None of the effects in this paper are driven by just one market. All effects reported in this paper hold even when data from any one of the markets are excluded from analysis.
Recall that clicking on an ad on this website does not imply a restaurant page visit, if the ad is for a chain. Clicking on the ad takes the user to a page with links to the chain outlets in the area of search. The user may then choose to visit the restaurant page.
For example, if an individual gets exposed to the experimental ad on 3 pages, then n E x p = 3.
For illustration, consider a set of individuals who browsed n pages. Within this set, individuals with higher ad exposure are the ones who continued browsing the website after being exposed to the ad a few times. Therefore, among the individuals who browsed n pages, ones with higher ad exposure might be the ones that have a lower preference for the advertiser. This possibility can lead to an underestimation of the effect of multiple ad exposures.
Also, I focus on individuals who have more than one day’s gap between sessions, so that the next session is likely to be a different purchase occasion. Because the number of users with multiple sessions is fewer, the dependent measure I use is a visit to the advertiser’s page; I take this step because the base level of sales lead is small, making precise estimation of the effects difficult.
An implicit assumption here is that consumers’ decisions to revisit the website are not correlated with past advertising exposure. I find no evidence for such correlation in the data, presented in Appendix B.
For analyzing carryover, I don’t include data from one experiment in which the advertiser was advertising before the experiments started.
The means I show here are not conditioned on n E x p 1 for the purpose of simplicity. In the data, the effects are larger when n E x p 1>0, as one would expect.
Estimating linear probability models using OLS instead of logit regression yields similar results for the model-free analysis throughout the paper.
I also estimated the specification in Column IV separately for the subsamples with (a) d a y s 1−2≤7 and (b) d a y s 1−2>7. The coefficient of n E x p 2 is positive and significant for (b), but statistically indistinguishable from zero for (a).
Prior lab evidence of the spacing effect has been shown for time intervals ranging up to a week (Janiszewski et al. 2003).
I use OLS in this case, to show the average slope. Running a logit regression and estimating the implied marginal effect gives similar results.
More recent research builds on this approach by allowing for wearin and wearout of advertising - repeated ad exposure decreases the attention consumers pay to it (Naik et al. 1998; Bass et al. 2007). However, the data patterns I observe do not comply with these models; columns V and VI of Table 6 show that an increase in d a y s 1−2 affects the carryover, but not the contemporaneous effect of n E x p 2. Therefore, the empirical evidence suggests an underlying data-generating process relating to long-term retention of ad effects as opposed to attention.
The age of an ad at a particular point in time is the time elapsed since the ad exposure.
This assumption is made to apply the model because in the context of advertising, one exposure may not lead to the consumers noticing the ad, unlike forced exposure occasions in the lab or general learning situations in which agents deliberately rehearse at every occasion. Therefore, in this setting, I define a session as a learning occasion, and the number of ad exposures represent the memory strength due to the ads at that occasion.
I fix β i = 0 (Eq. 2) because in the data, it is indistinguishable from the impact of \(A_{it}^{M}\) on choice.
I use data for individuals who repeat their website visits with a time interval of more than a day. Also, I did not use data from the experiment where the experimental restaurant had advertised before the time of the study. This step is taken to avoid the measurement problems caused by unknown initial value of any prior ad effect.
Other specifications provide a similar inference, and are presented in the accompanying Online Appendix.
Online ad networks such as DoubleClick and Facebook can directly apply this approach by estimating the models as above and performing counterfactual simulations because they can control ad exposure at the individual level in real time. Some advertisers who have access to the advertising medium can also follow directly (e.g., Amazon.com, Ebay.com). For other firms, advertising planning involves managing aggregate levers that can be set in a similar manner by making assumptions about consumer media consumption (see Dubé et al. (2005)). In practice, media consumption data available through third-party companies such as Nielsen, comScore and HitWise empirically support these assumptions.
I assume constant spacing between all occasions. For these calculations, I assume the profits resulting from the restaurant page visit to be $60 and the marginal cost of an ad impression to be $0.1.
If the consumer browses five pages in each of the eight sessions in the eight weeks of the month, the number of possible choices of a freq. cap is 6, from 0 to 5, and 28 combinations of switching the advertising on or off in any of the weeks are possible.
The integration is implemented using a Monte Carlo simulation method; I take draws of \(\theta _{i}^{\psi }\) and \(\xi _{i}^{\psi }\) from the distribution and compute the average value of \(\pi _{i}^{\psi }\) for these draws.
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Appendices
Appendix A: On measuring the impact of multiple ads
For most part of the analysis, the paper measures the effects of multiple exposures to the experimental ads in a session by regressing the outcome on the number of ad exposures, controlling for the number of pages browsed. If an ad exposure affects subsequent ad exposure (e.g., causes people to conclude their session) then controlling for the number of pages browsed may not solve its purpose of controlling for the browsing type. For example, consider the set of individuals who browsed 10 pages. Within this set, individuals with higher ad exposure are the ones who continued browsing the website after being exposed to the ad a few times. Therefore, among the individuals who browsed 10 pages, ones with higher ad exposure might be the ones that have a lower preference for the advertiser. This possibility can lead to an underestimation of the effect of multiple ad exposures.
1.1 Do experimental ads change the distribution of the number of pages?
One implication of this problem is that the number of pages browsed may change in the ad condition, which may change the number of ad exposures too. To check for this, I compare the empirical distributions of the number of pages browsed by sessions in the Experimental Ad and the No-Ad conditions. I use the two-sample Kolmogorov-Smirnov non-parametric test for this purpose and fail to reject the hypothesis (p-val =0.99) that the distributions are the same. Therefore, in these data, the assumption that the number of pages browsed in the ad condition is same as in the no-ad condition is not very strong.
In the rest of this section, I take an alternative approach to show that the assumptions made for the analysis in the paper are weak and the potential bias in the estimation of the effect of the ad exposures, if any, is insignificant. My approach is to re-construct the average treatment effect (the difference between the ad and the no-ad condition) using the estimate for the effect of one ad exposure. I show that a bias in the latter’s estimate will lead to a mismatch between the implied and the unbiased estimate of the average treatment effect. I take the following steps, (1) get an unbiased estimate of the average treatment effect, \(\hat {\gamma }\), by comparing the difference between the mean outcomes in the ad and the no-ad conditions; (2) estimate the average effect of an ad exposure, \(\hat {\alpha }\), by regressing the outcome on number of ad exposures, controlling for the number of pages browsed (model P); (3) estimate the average treatment effect predicted by the regression P, \(\hat {\gamma }_{P}\)(\(\hat {\alpha }\)); and (4) gauge the potential bias in \(\hat {\alpha }\) by comparing \(\hat {\gamma }\) and \(\hat {\gamma }_{P}\).
- Step 1::
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Measuring the average treatment effect
Recall that the experimental ad condition has a chance of an exposure to the experimental ad, whereas the no-ad condition always shows the dummy banner in the experimental slot. The average treatment effect is the difference in the mean chance of the outcome across the experimental ad and the no-ad condition. For the ease of the next steps in the replication process, I pick the sample from the time when the chance of getting the experimental ad exposure in the ad condition was exactly 60 % (more than half of the data qualifies). The ATE estimate, \(\hat {\gamma }\) for this subsample and its confidence interval are shown in Columns I and II of the Table 10 (this is essentially replicating Table 3 for this subsample). \(\hat {\gamma }\) is an unbiased estimate of the causal effect of being in a condition where the chance of getting exposed to the experimental ad condition is 60 %.
- Step 2::
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Measuring the effect of an ad exposure
Now within the ad condition, conditional on the number of pages browsed, the number of times the ad is displayed varies. This variation allows me to get an estimate of the population average effect of one ad exposure controlling for the browsing type, by estimating a model P (similar to Table 4, Column I)
$$ Y_{i}=c+\alpha nExp_{i}+\beta nPages_{i}+\eta_{i}, $$(9)where n E x p i is the number of times the experimental ad was displayed in the session and n P a g e s i is the number of pages browsed in the session i. However, the true model may have a subscript i on the coefficient for n E x p i . Therefore, a problem with estimating model P is that the independent variables, n E x p i and n P a g e s i , are chosen by the consumer i and may depend on the preferences of the individual; α i →n P a g e s i , n E x p i . Estimation of the regression (9) assumes this away, which may lead to a bias because of the unaccounted systematic heterogeneity.
So in the regression (9), the estimated parameter \(\hat {\alpha }\) may underestimate the true α = E(α i ). Let \(\hat {\alpha }=\alpha +a\), where a denotes the bias.
- Step 3::
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Reconstructing the ATE from the model estimate ( \(\hat {\gamma }_{P}\) )
I proceed as follows:
-
From the population in the No-Ad condition, I get the empirical distribution of n P a g e s.
-
For individual i∈{1,...,I}, I draw n P a g e s i from this empirical distribution.
-
As in the experiment design, i draws its treatment n E x p i ∼B i n o m i a l(n P a g e s i ,0.60).
For this simulated population of I individuals, average treatment effect is
$$\hat{\gamma}_{P}=\frac{1}{I}\sum\limits_{i}\left( \hat{Y}_{i}(nExp{}_{i},nPages_{i})-\hat{Y}_{i}(0,nPages_{i})\right).</p><p class="noindent">$$ -
- Step 4::
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Gauge the magnitude of the bias, ’a’
The idea is to rewrite the treatment effect \(\hat {\gamma }_{P}\) as a function of \(\hat {\gamma }\) and the bias. One can show using the law of iterated expectations that \(\hat {\gamma }_{P}\) is a function of a:
$$\begin{array}{@{}rcl@{}} \hat{\gamma}_{P} & = & \mathrm{E}\left( \mathrm{E}\left( \hat{Y}(nExp,nPages)-\hat{Y}(0,nPages)|nPages\right)\right)\\ & = & \mathrm{E}\left( \mathrm{E}\left( \hat{c}+\hat{\alpha}nExp+\hat{\beta}nPages-\left( \hat{c}+\hat{\beta}nPages\right)|nPages\right)\right)\\ & = & \mathrm{E}\left( \mathrm{E}\left( \hat{\alpha}nExp|nPages\right)\right)\\ & = & \hat{\alpha}\times\mathrm{E}\left( \mathrm{E}\left( nExp|nPages\right)\right)\\ & = & (\alpha+a)\times\mathrm{E}\left( \mathrm{E}\left( nExp|nPages\right)\right)\\ & = & (\alpha+a)\times\mathrm{E}\left( nExp\right)\\ & = & \alpha\times\mathrm{E}\left( nExp\right)+a\times\mathrm{E}\left( nExp\right)\\ & = & \gamma+a\times\mathrm{E}\left( nExp\right). \end{array} $$
The last step follows because E(α×n E x p) is the true average treatment effect γ. This analysis shows if a is large, \(\hat {\gamma }_{P}\) is more likely to be off the true value γ. If \(\hat {\gamma }\) and \(\hat {\gamma }_{P}\) are close, that is, if the model predicts the average treatment effect to be close to the unbiased estimator, the bias size may not be too big.
I compare these estimates shown in Table 10. Note that the estimated \(\hat {\gamma }_{P}\) is within the 95 % confidence intervals for \(\hat {\gamma }\) for for both visits and leads when used as outcomes. Therefore, this analysis suggests the potential bias a is not large relative to the absolute value of the population mean α. I can draw a similar conclusion if I use a logit regression model for P, instead of OLS.
Appendix B: Impact of ads on website revisit
An implicit assumption made in the analysis is that the future sessions on the website and the time intervals between sessions are not dependent on advertising exposure. In this section, I check for the presence of such correlations in the data. In column I of Table 11, I regress a dummy variable indicating that the user had only one session over the course of the experiments, on allocation of the user’s first session to the ad condition. I find that the coefficient for the dummy variable is statistically not different from zero, indicating no correlation between being in the ad condition and future revisit decisions. In columns II and III, I include the past decisions of whether to visit the advertised restaurant’s page or generate a sales lead as the explanatory variable. Again, I find no significant impact of the experimental ads on future revisit decisions. Next, for individuals that do visit more than once, I regress the time intervals between first two sessions on the allocation to ad condition in the first session. Column IV of Table 11 shows the results of this regression. Again, I find no significant correlation between allocation to the ad condition and website revisit frequency. This evidence supports the assumption that the future revisit frequency is uncorrelated with the experimental ad exposure.
Appendix C: Estimation methodology
I estimate the model parameters using the simulated maximum likelihood method. Given the parameters and data \(\left (X_{it}=\left \{ nPages_{it},\left \{nExp_{ik}\right \}_{k=1}^{t}, \{days_{ik}\}_{k=1}^{t},\right . \right .\!\!\!\) \(\left .\left .\{x_{ij}\}_{j=1}^{J}\right \} \right )\), the probability of an individual i visiting the advertiser’s page in session t (y i t = 1) according to model ψ∈{G,M G,M} is given by
The likelihood of the sequence of observed decisions \(y_{i}=\{y_{it}\}_{t=1}^{T_{i}}\) made by i is then
where T i is the total number of observed sessions for individual i. Next, because the parameters \(\left \{\theta _{i}^{\psi },\xi _{i}^{\psi }\right \}\) are random, I compute the expected likelihood by integrating the individual’s likelihood over the distribution of random parameters:
where Ω(.) is the density function for the distribution defined in (8).Footnote 33 So the log-simulated likelihood of observed data conditioned on parameters is given by
The estimates of parameters for the model are the ones that maximize the log-likelihood function.
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Sahni, N.S. Effect of temporal spacing between advertising exposures: Evidence from online field experiments. Quant Mark Econ 13, 203–247 (2015). https://doi.org/10.1007/s11129-015-9159-9
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DOI: https://doi.org/10.1007/s11129-015-9159-9
Keywords
- Advertising
- Search advertising
- Spacing effect
- Temporal spacing
- Repeated advertising
- ACT-R model
- Cognitive psychology
- Memory-based model
- Long-term effects of ads
- Carryover effects
- Goodwill model
- Advertising frequency
- Memory model
- Online advertising
- Internet advertising
- Randomized experiments
- Randomized field experiments
- Field experiments