80 Case Studies in Advertising

The constructs developed in Chapter 13—the persuasion chain, the two routes to attitude change, wear-in and wear-out, and above all the incremental effect above a baseline—are theoretical objects. An advertising case study is where those objects meet a real budget, a real schedule, and a real measurement problem. This chapter does not treat cases as decorative anecdotes about clever creative. It treats them as evidence, and its central discipline is the question every empiricist must ask of a campaign: did the advertising cause the outcome, or did the firm advertise because it already expected the outcome? That question is not pedantic. It is the difference between a celebrated campaign that paid and a celebrated campaign that merely coincided with sales the firm would have made anyway.

Three cases anchor the chapter, chosen because each has been studied with unusual rigor and each isolates a distinct lesson from Chapter 13. The first is the long program of split-cable field experiments run on consumer packaged goods, which established—decades before the digital-experiments literature—both that advertising can move sales and that its average effect is small, fragile, and easy to overstate (Lodish et al. 1995). The second is the eBay paid-search experiment, in which a firm that believed search advertising was highly profitable discovered, under randomization, that most of its measured return was selection rather than causation (Blake, Nosko, and Tadelis 2015). The third is the public-health advertising case, in which the dependent variable is widened from own-brand sales to societal behavior and a credible geographic baseline recovers a large effect that own-sales elasticities would have missed (Ghosh Dastidar, Sunder, and Shah 2023). Read together, the three cases trace the same arc the parent chapter draws: advertising works, most measured returns are illusory, and what separates the two is the quality of the counterfactual.

By the end of this chapter the reader should be able to map any campaign onto the formal apparatus of Chapter 13; state the baseline a credible evaluation requires and name the bias that contaminates the estimate when that baseline is missing; and distinguish a campaign that identified an advertising effect from one that merely correlated spending with sales. As with the branding cases of Chapter 78, the organizing unit is the construct, not the firm: each case is read through one piece of theory so that the theory is exercised and the case is disciplined.

80.1 The Inferential Problem, Restated for Campaigns

Chapter 13 establishes that the naïve sales-on-advertising regression

\[ y_{it} = \beta\, a_{it} + \mathbf{x}_{it}^{\top}\boldsymbol{\gamma} + \varepsilon_{it} \tag{80.1}\]

recovers the causal effect $\beta$ only when $\mathbb{E}[\varepsilon_{it}\,a_{it}]=0$, and that this condition fails whenever a firm sets advertising $a_{it}$ in anticipation of a demand shock that enters $\varepsilon_{it}$. Because firms target favorable conditions—their best markets, their peak seasons, their most promising launches—the omitted shock loads positively onto $\hat\beta$, so observational case readings overstate effectiveness (Gordon et al. 2019; Lewis and Rao 2015). A campaign that looks brilliant in a before–after sales chart may simply have been scheduled into a quarter the firm already knew would be strong.

The corrective concept, following Gordon et al. (2021), is the incremental effect: the lift in behavior above the baseline the consumer would have exhibited absent the exposure. Formally, with potential outcomes $Y_i(1)$ and $Y_i(0)$ under exposure and no exposure, the target is the average treatment effect

\[ \tau = \mathbb{E}\!\left[\,Y_i(1) - Y_i(0)\,\right], \tag{80.2}\]

and the entire difficulty is that $Y_i(0)$—what would have happened without the ad—is never observed for an exposed unit. A case study earns evidentiary value precisely to the extent that it constructs a credible estimate of $Y_i(0)$: a randomized control arm, a holdout of untreated markets, or a sharp discontinuity across an advertising boundary. The three traps below recur across all three cases and are worth naming once.

Trap	What it is	Antidote in a case
Targeting endogeneity	Firm advertises where/when it expects to sell	Randomize exposure, or hold out comparable untreated units
Selection in attribution	Credited touchpoints are chosen by the consumer, not assigned	Compare to who would have converted anyway
Survivorship	Only the campaigns that “worked” become famous	Ask what comparable campaigns that failed did

The arrangement of the chapter follows Figure 80.1: each case supplies relatively clean variation in one identification strategy from Chapter 13 and thereby teaches one construct with minimal confounding.

flowchart LR
  C1[Split-cable CPG<br/>experiments] --> S1[Randomized<br/>field experiment]
  C2[eBay paid<br/>search] --> S2[Randomized<br/>geo experiment]
  C3[Public-health<br/>advertising] --> S3[Border /<br/>discontinuity design]
  S1 --> K1[Small, fragile<br/>elasticities & wear-out]
  S2 --> K2[Selection vs.<br/>causation in attribution]
  S3 --> K3[Incremental effect on a<br/>widened dependent variable]

Figure 80.1: Mapping each advertising case (left) to the identification strategy it exemplifies (center) and the construct from the Advertising chapter it teaches most cleanly (right).

80.2 Case 1 — Split-Cable Experiments: How Big Is the Effect, Really?

The longest-running attempt to measure advertising’s effect causally predates the digital era. Through the 1980s and early 1990s, the IRI BehaviorScan system ran split-cable field experiments: in test markets wired so that matched panels of households could be served different television advertising while their purchases were tracked through scanner panels, the advertiser’s weight could be raised in a randomly assigned treatment group and held fixed in a control group. This is, in the language of Chapter 13, a genuine randomized field experiment—the benchmark row of Table 13.2—because exposure is assigned rather than chosen, so the control panel furnishes a direct estimate of the unobserved $Y_i(0)$ in Equation 80.2. Lodish et al. (1995) analyze roughly 389 such tests and report the empirical generalizations that have disciplined the field ever since.

Increasing the weight of advertising alone, with no change in copy, media plan, or target, has no reliable effect on sales for established products; about half of the heavy-up tests show no significant sales effect at all. When advertising does work, it tends to be because something other than weight—new copy, a new media strategy, a new product, or a category-expansion message—has changed.

Two lessons from Chapter 13 fall directly out of this corpus. The first is that short-run advertising elasticities are small, consistent with the meta-analytic benchmark that the short-term advertising elasticity for established brands is on the order of $0.1$ (Tellis and Wernerfelt 1987), and with the broader finding that elasticities decline over the product life cycle (Vakratsas and Ambler 1999). An established brand’s consumers already know it; additional gross rating points clear no new stage of the persuasion chain of Equation 13.1, because the presentation and attention stages were already cleared in prior years. The second lesson is wear-out: where weight increases did move sales, the effect was concentrated early and decayed with repetition, the field analogue of the laboratory wear-out Batra and Ray (1986) document when counterargument production rises with repeated exposure. The managerial implication the Lodish et al. (1995) authors draw is therefore not “spend more” but “spend differently”—change the message rather than the weight—precisely because weight operates on stages of the chain that are already saturated for a mature brand.

The split-cable program also illustrates why famous before–after charts mislead. A brand that ran a heavy fourth-quarter campaign and saw sales rise has not identified $\tau$; it has measured $\mathbb{E}[Y_i(1)\mid \text{advertised in Q4}]$ against its own pre-period, which mixes the ad effect with the seasonal shock the firm anticipated when it chose Q4. The split-cable design defeats this by holding the same weeks fixed across treatment and control panels in the same market, so the seasonal shock differences out. The following simulation reproduces the core finding: a small true weight effect, recoverable by the experiment but inflated by the naïve before–after read that targeting contaminates.

Code

set.seed(46)

n_house   <- 4000                 # panel households
true_lift <- 0.03                 # true incremental effect of the heavy-up: +3%

# A seasonal demand shock the brand SEES and schedules its heavy-up into.
season <- rnorm(n_house, 0, 1)

# Naive "field" data: the brand heavies-up where the season looks strong, so
# exposure is correlated with the shock (targeting endogeneity).
heavy_obs <- as.integer(season + rnorm(n_house, 0, 0.5) > 0)
base_sales <- 10 + 2.0 * season
sales_obs  <- base_sales * (1 + true_lift * heavy_obs) + rnorm(n_house, 0, 1)

naive_lift <- (mean(sales_obs[heavy_obs == 1]) -
               mean(sales_obs[heavy_obs == 0])) / mean(base_sales)

# Split-cable: RANDOM assignment within the same market and weeks, so exposure is
# orthogonal to the season.
treat_rand <- rbinom(n_house, 1, 0.5)
sales_exp  <- base_sales * (1 + true_lift * treat_rand) + rnorm(n_house, 0, 1)
exp_lift   <- (mean(sales_exp[treat_rand == 1]) -
               mean(sales_exp[treat_rand == 0])) / mean(base_sales)

cat("True incremental lift      :", paste0(round(100 * true_lift, 1), "%"), "\n")
#> True incremental lift      : 3%
cat("Naive before/after read    :", paste0(round(100 * naive_lift, 1), "%"),
    " (inflated by targeting)\n")
#> Naive before/after read    : 32.5%  (inflated by targeting)
cat("Split-cable experiment     :", paste0(round(100 * exp_lift, 1), "%"),
    " (recovers the truth)\n")
#> Split-cable experiment     : 3.2%  (recovers the truth)

The naïve contrast overstates the effect because exposure correlates with the season the brand targeted; randomization within the market severs that correlation and returns the small true lift. This is the same mechanism the parent chapter simulates for the geo-baseline case, here grounded in a real measurement system. The split-cable program’s enduring contribution is that it made the smallness of the average effect credible: it came not from a skeptical regression but from hundreds of randomized tests run by advertisers who expected to find large effects.

80.3 Case 2 — eBay Paid Search: When the Return Is Mostly Selection

If split-cable taught that weight effects are small, the eBay paid-search experiment taught the deeper lesson that an entire measured return can be an artifact of attribution selection. Blake, Nosko, and Tadelis (2015) study eBay’s search-engine marketing across two designs. For branded keywords—queries containing the word “eBay”—they exploit a natural experiment created when eBay stopped bidding on its own brand terms on one engine. For non-branded keywords, they run a large randomized geo experiment, switching paid search off in a random subset of designated market areas and comparing sales to the markets where it stayed on. Both designs construct $Y_i(0)$ honestly: the turned-off markets and the post-shutdown period estimate what sales would have been without the ads.

The result overturned the firm’s prior. The branded-keyword shutdown produced no measurable drop in sales: consumers who searched for “eBay” and would otherwise have clicked the paid link simply clicked the adjacent organic link to the same site, so the firm had been paying for traffic it would have received for free. The mechanism is pure attribution selection—the consumer, not the advertiser, had already selected eBay by typing its name, so the paid ad received conversion credit it did not cause. For non-branded keywords the picture was more nuanced: returns were positive for new and infrequent users but near zero or negative for the frequent users who dominate spend, so the average return on the search budget was far below the firm’s internal estimate and, on the relevant margin, negative.

The case is a clinic in why Equation 80.1 is biased even when the regression is sophisticated. The standard industry attribution model credits a sale to the last (or some weighted set of) clicks that preceded it. But the clicks a consumer makes are selected by the consumer, exactly the selection-in-attribution trap, so the correlation between paid clicks and conversions confounds the consumers the ads caused to convert with the far larger pool who would have converted regardless. The randomized holdout is what separates the two, and it revealed that the second pool dominated. The accounting is identical to the organic-versus-paid decomposition the parent chapter formalizes for the fake-news case (Equation 13.7): total demand is the sum of organic and ad-referred components, and a credible evaluation must net out the organic share that the advertising merely intercepted rather than created.

A small decision-theoretic calculation makes the managerial stakes concrete. Suppose a fraction $\theta$ of paid-search conversions would have occurred organically anyway. Then the true incremental cost per acquired customer is the reported cost-per-click figure divided by $(1-\theta)$ of conversions that are genuinely incremental, and the naïve return-on-ad-spend (ROAS) overstates the true ROAS by a factor of $1/(1-\theta)$.

Code

set.seed(460)

clicks            <- 100000          # paid clicks purchased
conv_rate         <- 0.05            # conversions per click
margin_per_conv   <- 12              # gross margin per conversion ($)
cost_per_click    <- 0.40            # paid CPC ($)

conversions       <- clicks * conv_rate
ad_spend          <- clicks * cost_per_click
naive_roas        <- (conversions * margin_per_conv) / ad_spend

# theta: share of paid conversions that would have happened organically (the eBay
# branded-keyword lesson: for brand terms theta is close to 1).
theta_grid <- c(0.0, 0.3, 0.6, 0.9)
incremental_roas <- (conversions * (1 - theta_grid) * margin_per_conv) / ad_spend

roas_table <- data.frame(
  theta_organic    = theta_grid,
  naive_ROAS       = round(naive_roas, 2),
  incremental_ROAS = round(incremental_roas, 2),
  profitable       = ifelse(incremental_roas > 1, "yes", "no")
)
roas_table
#>   theta_organic naive_ROAS incremental_ROAS profitable
#> 1           0.0        1.5             1.50        yes
#> 2           0.3        1.5             1.05        yes
#> 3           0.6        1.5             0.60         no
#> 4           0.9        1.5             0.15         no

When $\theta$ is large—as it is for branded keywords, where nearly every conversion would have arrived organically—the incremental ROAS collapses below one and the spend destroys value, even though the naïve ROAS looks handsomely positive. The eBay case is the empirical demonstration that this is not a hypothetical: a sophisticated firm spent for years on the high-$\theta$ margin because its attribution model could not see $\theta$. The lesson generalizes far beyond search. Any channel evaluated by crediting observed conversions, rather than by comparison to a randomized holdout, is exposed to the same upward bias, and the bias is largest exactly where the channel reaches consumers who were already going to buy.¹

80.4 Case 3 — Advertising as Public Policy: Widening the Dependent Variable

The first two cases shrink the estimated effect of advertising by measuring it honestly. The third shows the complementary move Chapter 13 recommends when own-brand sales elasticities are small and noisy: widen the dependent variable and find a setting where a credible baseline can be constructed for the broader outcome. Ghosh Dastidar, Sunder, and Shah (2023) study television advertising that carried COVID-19 narratives during the early pandemic and ask whether brand-sponsored advertising changed societal behavior—specifically, social distancing—rather than sales. The outcome is mobility measured from mobile-device data, and the identification strategy is a border design from Table 13.2: television-market (DMA) boundaries cut across county and even state lines, so two adjacent counties can sit in different ad markets and receive different advertising while sharing local conditions. Comparing mobility across that discontinuity estimates the advertising effect while differencing out the local shocks that confound a naïve comparison.

The estimated effect is large where one would least expect advertising to matter: TV ads with COVID narratives raised social-distancing behavior, and the effect was about eleven times larger in counties without government stay-at-home mandates than in counties with them. The interaction is the substantively important result. Where public policy already compelled the behavior, the marginal persuasive content of an ad added little; where policy was absent, brand-sponsored messaging substituted for the missing mandate. In the language of Chapter 13, the advertising cleared the yielding and behavior stages of the persuasion chain (Equation 13.1) for a population whose behavior was not already determined by law, and added nothing for a population whose behavior the law had already fixed.

The border design earns its credibility the way the split-cable and geo experiments earn theirs: by constructing $Y_i(0)$. The untreated side of the DMA boundary estimates what the treated side’s mobility would have been absent the COVID advertising, and the boundary’s arbitrariness with respect to local conditions is the identifying assumption. What would break it is the sorting flagged in Table 13.2—if counties on the treated side differed systematically in some mobility-relevant way that also tracks the DMA boundary—which is why the design restricts attention to narrow bands around the border where such sorting is least plausible. The following simulation reproduces the estimator and its central interaction.

Code

set.seed(4600)

n_pairs   <- 500                  # matched cross-border county pairs
true_eff_nomandate <- 0.11        # ad effect on distancing where no mandate (+11pp)
true_eff_mandate   <- 0.01        # ad effect where a mandate already binds (+1pp)

# Each pair shares a local baseline; one side is in the "treated" DMA (ran COVID ads).
local_base <- rnorm(n_pairs, 0.50, 0.08)        # baseline distancing rate
mandate    <- rbinom(n_pairs, 1, 0.5)           # does a local mandate bind?

treated_side <- local_base +
  ifelse(mandate == 1, true_eff_mandate, true_eff_nomandate) +
  rnorm(n_pairs, 0, 0.03)
control_side <- local_base + rnorm(n_pairs, 0, 0.03)

# Border estimator: within-pair difference (treated DMA minus control DMA),
# split by whether a mandate binds.
within_diff <- treated_side - control_side
est_nomandate <- mean(within_diff[mandate == 0])
est_mandate   <- mean(within_diff[mandate == 1])

cat("Effect where NO mandate (truth 0.11):", round(est_nomandate, 3), "\n")
#> Effect where NO mandate (truth 0.11): 0.109
cat("Effect where mandate binds (truth 0.01):", round(est_mandate, 3), "\n")
#> Effect where mandate binds (truth 0.01): 0.014
cat("Ratio (no-mandate / mandate):",
    round(est_nomandate / est_mandate, 1), "x\n")
#> Ratio (no-mandate / mandate): 7.7 x

The within-pair difference recovers both effects and their roughly order-of-magnitude ratio, illustrating how a discontinuity design isolates the advertising effect and the condition that moderates it. The case completes the chapter’s arc. Advertising’s own-sales effect is small and easily overstated (Case 1); much of its measured digital return is selection that a holdout dissolves (Case 2); yet when the dependent variable is widened to a behavior the firm genuinely moves and a sharp baseline is available, a real and policy-relevant effect emerges (Case 3). In every instance the verdict turns on the same thing: the credibility of $Y_i(0)$, not the fame of the campaign.

80.5 Cross-Case Synthesis

Reading the three cases together produces a comparison that is more instructive than any one of them. Table 80.1 records, for each, the construct it teaches, the strategy by which it builds a baseline, and the bias that would have contaminated the estimate had that baseline been missing.

Table 80.1: Cross-case synthesis of the three advertising cases: the construct each teaches, its baseline strategy, and the bias that would arise absent a credible baseline.

Case	Construct taught	Baseline strategy	Bias absent the baseline
Split-cable CPG (Lodish et al. 1995)	Small, decaying weight elasticities; wear-out (Tellis and Wernerfelt 1987; Batra and Ray 1986)	Randomized panels in-market	Targeting endogeneity inflates the effect
eBay paid search (Blake, Nosko, and Tadelis 2015)	Selection vs. causation in attribution	Randomized geo / shutdown holdout	Organic traffic credited to paid ads
Public-health TV (Ghosh Dastidar, Sunder, and Shah 2023)	Incremental effect on a widened outcome	Cross-DMA border discontinuity	Local shocks confounded with exposure

The single thread is Gordon et al. (2021)’s: an advertising effect is a credibly constructed increment above a baseline, and the three cases differ only in how they build that baseline—by randomizing within a market, by withholding a random set of markets, or by exploiting an arbitrary advertising boundary. None relies on the sophistication of a regression; all rely on the design of a counterfactual. The cases also rehearse the survivorship caution of Chapter 78 from the advertising side: campaigns that appear to have worked are over-represented in trade lore precisely because apparent success is what gets a campaign remembered, so a portfolio of celebrated campaigns is a sample drawn on the outcome. The corrective is the same one the split-cable program embodied at scale—measure against a control that was assembled before the result was known.

A final note connects these cases back to the behavioral theory of Chapter 13. The smallness of weight effects for mature brands (Case 1) is exactly what the persuasion chain of Equation 13.1 predicts once a brand’s consumers have already cleared its early stages; the dominance of selection in branded search (Case 2) is what one expects when the consumer has already yielded and is merely executing a known choice; and the mandate interaction in the public-health case (Case 3) is the behavior stage made visible—advertising moves behavior only where behavior is not already determined by another force. The econometrics and the psychology are not rival accounts. The identification design tells the analyst how large the effect is, and the behavioral model tells her why it is that large, and where.

80.6 Key Takeaways

An advertising case is evidence about an effect, not proof that a campaign paid; its value is entirely in the credibility of the counterfactual $Y_i(0)$ it constructs (Equation 80.2) (Gordon et al. 2021).
Decades of randomized split-cable tests established that pure weight increases for established brands usually do not move sales, and that elasticities are small and decay with repetition—wear-out made visible at scale (Lodish et al. 1995; Tellis and Wernerfelt 1987; Batra and Ray 1986).
Much of the measured return to digital advertising is selection: crediting observed conversions confounds customers the ad caused with customers who would have bought anyway, a bias that an experimental holdout dissolves (Blake, Nosko, and Tadelis 2015).
Widening the dependent variable—from own-brand sales to societal behavior—and exploiting a sharp geographic baseline can recover large, policy-relevant effects that own-sales elasticities miss (Ghosh Dastidar, Sunder, and Shah 2023).
Across all three, the verdict turns on the baseline, not the regression; naïve before–after and last-click reads overstate effectiveness because firms and consumers both select exposure (Gordon et al. 2019; Lewis and Rao 2015).

Batra, Rajeev, and Michael L. Ray. 1986. “Situational Effects of Advertising Repetition: The Moderating Influence of Motivation, Ability, and Opportunity to Respond.” Journal of Consumer Research 12 (4): 432. https://doi.org/10.1086/208528.

Blake, Thomas, Chris Nosko, and Steven Tadelis. 2015. “Consumer Heterogeneity and Paid Search Effectiveness: A Large-Scale Field Experiment.” Econometrica 83 (1): 155–74. https://doi.org/10.3982/ecta12423.

Ghosh Dastidar, Ayan, Sarang Sunder, and Denish Shah. 2023. “Societal Spillovers of TV Advertising: Social Distancing During a Public Health Crisis.” Journal of Marketing 87 (3): 337–58.

Gordon, Brett R., Kinshuk Jerath, Zsolt Katona, Sridhar Narayanan, Jiwoong Shin, and Kenneth C. Wilbur. 2021. “Inefficiencies in Digital Advertising Markets.” Journal of Marketing 85 (1): 7–25. https://doi.org/10.1177/0022242920913236.

Gordon, Brett R., Florian Zettelmeyer, Neha Bhargava, and Dan Chapsky. 2019. “A Comparison of Approaches to Advertising Measurement: Evidence from Big Field Experiments at Facebook.” Marketing Science 38 (2): 193–225. https://doi.org/10.1287/mksc.2018.1135.

Lewis, Randall A., and Justin M. Rao. 2015. “The Unfavorable Economics of Measuring the Returns to Advertising .” The Quarterly Journal of Economics 130 (4): 1941–73. https://doi.org/10.1093/qje/qjv023.

Lodish, Leonard M., Magid Abraham, Stuart Kalmenson, Jeanne Livelsberger, Beth Lubetkin, Bruce Richardson, and Mary Ellen Stevens. 1995. “How t.v. Advertising Works: A Meta-Analysis of 389 Real World Split Cable t.v. Advertising Experiments.” Journal of Marketing Research 32 (2): 125. https://doi.org/10.2307/3152042.

Tellis, Gerard J., and Birger Wernerfelt. 1987. “Competitive Price and Quality Under Asymmetric Information.” Marketing Science 6 (3): 240–53. https://doi.org/10.1287/mksc.6.3.240.

Vakratsas, Demetrios, and Tim Ambler. 1999. “How Advertising Works: What Do We Really Know?” Journal of Marketing 63 (1): 26. https://doi.org/10.2307/1251999.

The methodological remedy is the always-on holdout: a small, randomly withheld audience that never receives the channel, against which the treated audience is continuously benchmarked. This operationalizes Equation 80.2 at the level of a live marketing program and is the production-grade descendant of the split-cable design of Lodish et al. (1995). The cost is a deliberately forgone slice of reach; the return is an unbiased estimate of $\tau$ rather than a self-confirming attribution report.↩︎

# Case Studies in Advertising {#sec-case-advertising} The constructs developed in @sec-advertising—the persuasion chain, the two routes to attitude change, wear-in and wear-out, and above all the *incremental effect above a baseline*—are theoretical objects. An advertising case study is where those objects meet a real budget, a real schedule, and a real measurement problem. This chapter does not treat cases as decorative anecdotes about clever creative. It treats them as **evidence**, and its central discipline is the question every empiricist must ask of a campaign: *did the advertising cause the outcome, or did the firm advertise because it already expected the outcome?* That question is not pedantic. It is the difference between a celebrated campaign that paid and a celebrated campaign that merely coincided with sales the firm would have made anyway. Three cases anchor the chapter, chosen because each has been studied with unusual rigor and each isolates a distinct lesson from @sec-advertising. The first is the long program of **split-cable field experiments** run on consumer packaged goods, which established—decades before the digital-experiments literature—both that advertising can move sales and that its average effect is small, fragile, and easy to overstate [@lodish1995]. The second is the **eBay paid-search experiment**, in which a firm that believed search advertising was highly profitable discovered, under randomization, that most of its measured return was selection rather than causation [@blake2015]. The third is the **public-health advertising** case, in which the dependent variable is widened from own-brand sales to societal behavior and a credible geographic baseline recovers a large effect that own-sales elasticities would have missed [@ghosh2023societal]. Read together, the three cases trace the same arc the parent chapter draws: advertising works, most measured returns are illusory, and what separates the two is the quality of the counterfactual. By the end of this chapter the reader should be able to map any campaign onto the formal apparatus of @sec-advertising; state the baseline a credible evaluation requires and name the bias that contaminates the estimate when that baseline is missing; and distinguish a campaign that *identified* an advertising effect from one that merely *correlated* spending with sales. As with the branding cases of @sec-case-branding, the organizing unit is the construct, not the firm: each case is read through one piece of theory so that the theory is exercised and the case is disciplined. ## The Inferential Problem, Restated for Campaigns @sec-advertising establishes that the naïve sales-on-advertising regression $$ y_{it} = \beta\, a_{it} + \mathbf{x}_{it}^{\top}\boldsymbol{\gamma} + \varepsilon_{it} $$ {#eq-case-naive} recovers the causal effect $\beta$ only when $\mathbb{E}[\varepsilon_{it}\,a_{it}]=0$, and that this condition fails whenever a firm sets advertising $a_{it}$ in anticipation of a demand shock that enters $\varepsilon_{it}$. Because firms target favorable conditions—their best markets, their peak seasons, their most promising launches—the omitted shock loads positively onto $\hat\beta$, so observational case readings *overstate* effectiveness [@Gordon_2017; @Lewis_2015]. A campaign that looks brilliant in a before–after sales chart may simply have been scheduled into a quarter the firm already knew would be strong. The corrective concept, following @Gordon_2019, is the **incremental effect**: the lift in behavior above the baseline the consumer would have exhibited absent the exposure. Formally, with potential outcomes $Y_i(1)$ and $Y_i(0)$ under exposure and no exposure, the target is the average treatment effect $$ \tau = \mathbb{E}\!\left[\,Y_i(1) - Y_i(0)\,\right], $$ {#eq-case-ate} and the entire difficulty is that $Y_i(0)$—what would have happened without the ad—is never observed for an exposed unit. A case study earns evidentiary value precisely to the extent that it constructs a credible estimate of $Y_i(0)$: a randomized control arm, a holdout of untreated markets, or a sharp discontinuity across an advertising boundary. The three traps below recur across all three cases and are worth naming once. | Trap | What it is | Antidote in a case | |------|-----------|--------------------| | Targeting endogeneity | Firm advertises where/when it expects to sell | Randomize exposure, or hold out comparable untreated units | | Selection in attribution | Credited touchpoints are chosen by the consumer, not assigned | Compare to who would have converted anyway | | Survivorship | Only the campaigns that "worked" become famous | Ask what comparable campaigns that failed did | The arrangement of the chapter follows @fig-case-adv-framework: each case supplies relatively clean variation in one identification strategy from @sec-advertising and thereby teaches one construct with minimal confounding. ```{mermaid} %%| label: fig-case-adv-framework %%| fig-cap: "Mapping each advertising case (left) to the identification strategy it exemplifies (center) and the construct from the Advertising chapter it teaches most cleanly (right)." flowchart LR C1[Split-cable CPG experiments] --> S1[Randomized field experiment] C2[eBay paid search] --> S2[Randomized geo experiment] C3[Public-health advertising] --> S3[Border / discontinuity design] S1 --> K1[Small, fragile elasticities & wear-out] S2 --> K2[Selection vs. causation in attribution] S3 --> K3[Incremental effect on a widened dependent variable] ``` ## Case 1 — Split-Cable Experiments: How Big Is the Effect, Really? The longest-running attempt to measure advertising's effect causally predates the digital era. Through the 1980s and early 1990s, the IRI **BehaviorScan** system ran **split-cable** field experiments: in test markets wired so that matched panels of households could be served *different* television advertising while their purchases were tracked through scanner panels, the advertiser's weight could be raised in a randomly assigned treatment group and held fixed in a control group. This is, in the language of @sec-advertising, a genuine randomized field experiment—the benchmark row of @tbl-adv-identification—because exposure is assigned rather than chosen, so the control panel furnishes a direct estimate of the unobserved $Y_i(0)$ in @eq-case-ate. @lodish1995 analyze roughly 389 such tests and report the empirical generalizations that have disciplined the field ever since. > Increasing the *weight* of advertising alone, with no change in copy, media plan, > or target, has no reliable effect on sales for established products; about half of > the heavy-up tests show no significant sales effect at all. When advertising does > work, it tends to be because *something other than weight*—new copy, a new media > strategy, a new product, or a category-expansion message—has changed. Two lessons from @sec-advertising fall directly out of this corpus. The first is that **short-run advertising elasticities are small**, consistent with the meta-analytic benchmark that the short-term advertising elasticity for established brands is on the order of $0.1$ [@tellis1987], and with the broader finding that elasticities decline over the product life cycle [@vakratsas1999]. An established brand's consumers already know it; additional gross rating points clear no new stage of the persuasion chain of @eq-mcguire-chain, because the presentation and attention stages were already cleared in prior years. The second lesson is **wear-out**: where weight increases did move sales, the effect was concentrated early and decayed with repetition, the field analogue of the laboratory wear-out @batra1986 document when counterargument production rises with repeated exposure. The managerial implication the @lodish1995 authors draw is therefore not "spend more" but "spend *differently*"—change the message rather than the weight—precisely because weight operates on stages of the chain that are already saturated for a mature brand. The split-cable program also illustrates why famous before–after charts mislead. A brand that ran a heavy fourth-quarter campaign and saw sales rise has not identified $\tau$; it has measured $\mathbb{E}[Y_i(1)\mid \text{advertised in Q4}]$ against its own pre-period, which mixes the ad effect with the seasonal shock the firm anticipated when it chose Q4. The split-cable design defeats this by holding the *same* weeks fixed across treatment and control panels in the *same* market, so the seasonal shock differences out. The following simulation reproduces the core finding: a small true weight effect, recoverable by the experiment but inflated by the naïve before–after read that targeting contaminates. ```{r split-cable-sim, message=FALSE, warning=FALSE} set.seed(46) n_house <- 4000 # panel households true_lift <- 0.03 # true incremental effect of the heavy-up: +3% # A seasonal demand shock the brand SEES and schedules its heavy-up into. season <- rnorm(n_house, 0, 1) # Naive "field" data: the brand heavies-up where the season looks strong, so # exposure is correlated with the shock (targeting endogeneity). heavy_obs <- as.integer(season + rnorm(n_house, 0, 0.5) > 0) base_sales <- 10 + 2.0 * season sales_obs <- base_sales * (1 + true_lift * heavy_obs) + rnorm(n_house, 0, 1) naive_lift <- (mean(sales_obs[heavy_obs == 1]) - mean(sales_obs[heavy_obs == 0])) / mean(base_sales) # Split-cable: RANDOM assignment within the same market and weeks, so exposure is # orthogonal to the season. treat_rand <- rbinom(n_house, 1, 0.5) sales_exp <- base_sales * (1 + true_lift * treat_rand) + rnorm(n_house, 0, 1) exp_lift <- (mean(sales_exp[treat_rand == 1]) - mean(sales_exp[treat_rand == 0])) / mean(base_sales) cat("True incremental lift :", paste0(round(100 * true_lift, 1), "%"), "\n") cat("Naive before/after read :", paste0(round(100 * naive_lift, 1), "%"), " (inflated by targeting)\n") cat("Split-cable experiment :", paste0(round(100 * exp_lift, 1), "%"), " (recovers the truth)\n") ``` The naïve contrast overstates the effect because exposure correlates with the season the brand targeted; randomization within the market severs that correlation and returns the small true lift. This is the same mechanism the parent chapter simulates for the geo-baseline case, here grounded in a real measurement system. The split-cable program's enduring contribution is that it made the smallness of the average effect *credible*: it came not from a skeptical regression but from hundreds of randomized tests run by advertisers who expected to find large effects. ## Case 2 — eBay Paid Search: When the Return Is Mostly Selection If split-cable taught that *weight* effects are small, the eBay paid-search experiment taught the deeper lesson that an entire measured *return* can be an artifact of **attribution selection**. @blake2015 study eBay's search-engine marketing across two designs. For **branded keywords**—queries containing the word "eBay"—they exploit a natural experiment created when eBay stopped bidding on its own brand terms on one engine. For **non-branded keywords**, they run a large randomized geo experiment, switching paid search off in a random subset of designated market areas and comparing sales to the markets where it stayed on. Both designs construct $Y_i(0)$ honestly: the turned-off markets and the post-shutdown period estimate what sales would have been without the ads. The result overturned the firm's prior. The branded-keyword shutdown produced **no measurable drop in sales**: consumers who searched for "eBay" and would otherwise have clicked the paid link simply clicked the adjacent organic link to the same site, so the firm had been *paying for traffic it would have received for free*. The mechanism is pure attribution selection—the consumer, not the advertiser, had already selected eBay by typing its name, so the paid ad received conversion credit it did not cause. For non-branded keywords the picture was more nuanced: returns were positive for new and infrequent users but near zero or negative for the frequent users who dominate spend, so the *average* return on the search budget was far below the firm's internal estimate and, on the relevant margin, negative. The case is a clinic in why @eq-case-naive is biased even when the regression is sophisticated. The standard industry attribution model credits a sale to the last (or some weighted set of) clicks that preceded it. But the clicks a consumer makes are *selected by the consumer*, exactly the selection-in-attribution trap, so the correlation between paid clicks and conversions confounds the consumers the ads *caused* to convert with the far larger pool who would have converted regardless. The randomized holdout is what separates the two, and it revealed that the second pool dominated. The accounting is identical to the organic-versus-paid decomposition the parent chapter formalizes for the fake-news case (@eq-fakenews): total demand is the sum of organic and ad-referred components, and a credible evaluation must net out the organic share that the advertising merely *intercepted* rather than created. A small decision-theoretic calculation makes the managerial stakes concrete. Suppose a fraction $\theta$ of paid-search conversions would have occurred organically anyway. Then the true incremental cost per acquired customer is the reported cost-per-click figure divided by $(1-\theta)$ of conversions that are genuinely incremental, and the naïve return-on-ad-spend (ROAS) overstates the true ROAS by a factor of $1/(1-\theta)$. ```{r ebay-roas, message=FALSE, warning=FALSE} set.seed(460) clicks <- 100000 # paid clicks purchased conv_rate <- 0.05 # conversions per click margin_per_conv <- 12 # gross margin per conversion ($) cost_per_click <- 0.40 # paid CPC ($) conversions <- clicks * conv_rate ad_spend <- clicks * cost_per_click naive_roas <- (conversions * margin_per_conv) / ad_spend # theta: share of paid conversions that would have happened organically (the eBay # branded-keyword lesson: for brand terms theta is close to 1). theta_grid <- c(0.0, 0.3, 0.6, 0.9) incremental_roas <- (conversions * (1 - theta_grid) * margin_per_conv) / ad_spend roas_table <- data.frame( theta_organic = theta_grid, naive_ROAS = round(naive_roas, 2), incremental_ROAS = round(incremental_roas, 2), profitable = ifelse(incremental_roas > 1, "yes", "no") ) roas_table ``` When $\theta$ is large—as it is for branded keywords, where nearly every conversion would have arrived organically—the incremental ROAS collapses below one and the spend destroys value, even though the naïve ROAS looks handsomely positive. The eBay case is the empirical demonstration that this is not a hypothetical: a sophisticated firm spent for years on the high-$\theta$ margin because its attribution model could not see $\theta$. The lesson generalizes far beyond search. Any channel evaluated by crediting observed conversions, rather than by comparison to a randomized holdout, is exposed to the same upward bias, and the bias is largest exactly where the channel reaches consumers who were already going to buy.[^holdout] [^holdout]: The methodological remedy is the *always-on holdout*: a small, randomly withheld audience that never receives the channel, against which the treated audience is continuously benchmarked. This operationalizes @eq-case-ate at the level of a live marketing program and is the production-grade descendant of the split-cable design of @lodish1995. The cost is a deliberately forgone slice of reach; the return is an unbiased estimate of $\tau$ rather than a self-confirming attribution report. ## Case 3 — Advertising as Public Policy: Widening the Dependent Variable The first two cases shrink the estimated effect of advertising by measuring it honestly. The third shows the complementary move @sec-advertising recommends when own-brand sales elasticities are small and noisy: **widen the dependent variable** and find a setting where a credible baseline can be constructed for the broader outcome. @ghosh2023societal study television advertising that carried COVID-19 narratives during the early pandemic and ask whether brand-sponsored advertising changed *societal* behavior—specifically, social distancing—rather than sales. The outcome is mobility measured from mobile-device data, and the identification strategy is a **border design** from @tbl-adv-identification: television-market (DMA) boundaries cut across county and even state lines, so two adjacent counties can sit in different ad markets and receive different advertising while sharing local conditions. Comparing mobility across that discontinuity estimates the advertising effect while differencing out the local shocks that confound a naïve comparison. The estimated effect is large where one would least expect advertising to matter: TV ads with COVID narratives raised social-distancing behavior, and the effect was about **eleven times larger in counties without government stay-at-home mandates** than in counties with them. The interaction is the substantively important result. Where public policy already compelled the behavior, the marginal persuasive content of an ad added little; where policy was absent, brand-sponsored messaging *substituted* for the missing mandate. In the language of @sec-advertising, the advertising cleared the yielding and behavior stages of the persuasion chain (@eq-mcguire-chain) for a population whose behavior was not already determined by law, and added nothing for a population whose behavior the law had already fixed. The border design earns its credibility the way the split-cable and geo experiments earn theirs: by constructing $Y_i(0)$. The untreated side of the DMA boundary estimates what the treated side's mobility would have been absent the COVID advertising, and the boundary's arbitrariness with respect to local conditions is the identifying assumption. What would break it is the sorting flagged in @tbl-adv-identification—if counties on the treated side differed systematically in some mobility-relevant way that also tracks the DMA boundary—which is why the design restricts attention to narrow bands around the border where such sorting is least plausible. The following simulation reproduces the estimator and its central interaction. ```{r border-design-sim, message=FALSE, warning=FALSE} set.seed(4600) n_pairs <- 500 # matched cross-border county pairs true_eff_nomandate <- 0.11 # ad effect on distancing where no mandate (+11pp) true_eff_mandate <- 0.01 # ad effect where a mandate already binds (+1pp) # Each pair shares a local baseline; one side is in the "treated" DMA (ran COVID ads). local_base <- rnorm(n_pairs, 0.50, 0.08) # baseline distancing rate mandate <- rbinom(n_pairs, 1, 0.5) # does a local mandate bind? treated_side <- local_base + ifelse(mandate == 1, true_eff_mandate, true_eff_nomandate) + rnorm(n_pairs, 0, 0.03) control_side <- local_base + rnorm(n_pairs, 0, 0.03) # Border estimator: within-pair difference (treated DMA minus control DMA), # split by whether a mandate binds. within_diff <- treated_side - control_side est_nomandate <- mean(within_diff[mandate == 0]) est_mandate <- mean(within_diff[mandate == 1]) cat("Effect where NO mandate (truth 0.11):", round(est_nomandate, 3), "\n") cat("Effect where mandate binds (truth 0.01):", round(est_mandate, 3), "\n") cat("Ratio (no-mandate / mandate):", round(est_nomandate / est_mandate, 1), "x\n") ``` The within-pair difference recovers both effects and their roughly order-of-magnitude ratio, illustrating how a discontinuity design isolates the advertising effect and the condition that moderates it. The case completes the chapter's arc. Advertising's own-sales effect is small and easily overstated (Case 1); much of its measured digital return is selection that a holdout dissolves (Case 2); yet when the dependent variable is widened to a behavior the firm genuinely moves and a sharp baseline is available, a real and policy-relevant effect emerges (Case 3). In every instance the verdict turns on the same thing: the credibility of $Y_i(0)$, not the fame of the campaign. ## Cross-Case Synthesis Reading the three cases together produces a comparison that is more instructive than any one of them. @tbl-case-adv-summary records, for each, the construct it teaches, the strategy by which it builds a baseline, and the bias that would have contaminated the estimate had that baseline been missing. | Case | Construct taught | Baseline strategy | Bias absent the baseline | |------|------------------|-------------------|--------------------------| | Split-cable CPG [@lodish1995] | Small, decaying weight elasticities; wear-out [@tellis1987; @batra1986] | Randomized panels in-market | Targeting endogeneity inflates the effect | | eBay paid search [@blake2015] | Selection vs. causation in attribution | Randomized geo / shutdown holdout | Organic traffic credited to paid ads | | Public-health TV [@ghosh2023societal] | Incremental effect on a widened outcome | Cross-DMA border discontinuity | Local shocks confounded with exposure | : Cross-case synthesis of the three advertising cases: the construct each teaches, its baseline strategy, and the bias that would arise absent a credible baseline. {#tbl-case-adv-summary} The single thread is @Gordon_2019's: an advertising effect is a credibly constructed *increment above a baseline*, and the three cases differ only in how they build that baseline—by randomizing within a market, by withholding a random set of markets, or by exploiting an arbitrary advertising boundary. None relies on the sophistication of a regression; all rely on the design of a counterfactual. The cases also rehearse the **survivorship** caution of @sec-case-branding from the advertising side: campaigns that *appear* to have worked are over-represented in trade lore precisely because apparent success is what gets a campaign remembered, so a portfolio of celebrated campaigns is a sample drawn on the outcome. The corrective is the same one the split-cable program embodied at scale—measure against a control that was assembled *before* the result was known. A final note connects these cases back to the behavioral theory of @sec-advertising. The smallness of weight effects for mature brands (Case 1) is exactly what the persuasion chain of @eq-mcguire-chain predicts once a brand's consumers have already cleared its early stages; the dominance of selection in branded search (Case 2) is what one expects when the consumer has *already* yielded and is merely executing a known choice; and the mandate interaction in the public-health case (Case 3) is the behavior stage made visible—advertising moves behavior only where behavior is not already determined by another force. The econometrics and the psychology are not rival accounts. The identification design tells the analyst *how large* the effect is, and the behavioral model tells her *why it is that large, and where*. ## Key Takeaways - An advertising case is **evidence about an effect**, not proof that a campaign paid; its value is entirely in the credibility of the counterfactual $Y_i(0)$ it constructs (@eq-case-ate) [@Gordon_2019]. - Decades of randomized **split-cable** tests established that pure weight increases for established brands usually do not move sales, and that elasticities are small and decay with repetition—wear-out made visible at scale [@lodish1995; @tellis1987; @batra1986]. - Much of the measured return to **digital advertising is selection**: crediting observed conversions confounds customers the ad caused with customers who would have bought anyway, a bias that an experimental holdout dissolves [@blake2015]. - **Widening the dependent variable**—from own-brand sales to societal behavior—and exploiting a sharp geographic baseline can recover large, policy-relevant effects that own-sales elasticities miss [@ghosh2023societal]. - Across all three, the verdict turns on the **baseline, not the regression**; naïve before–after and last-click reads overstate effectiveness because firms and consumers both *select* exposure [@Gordon_2017; @Lewis_2015].