Lecture 24: Advertising

Main ideas and lessons from the lecture (Advertising, empirical evidence)

• Advertising is a highly empirical field, driven by:

  • Practitioner demand to measure advertising value/effectiveness.
  • Academic work focused on:
    • Mechanisms: How advertising works (e.g., changes in tastes, provides information, signals).
    • Welfare/market effects: whether mechanisms translate into different welfare outcomes.
    • General equilibrium impacts: how allowing advertising affects prices and markets.

• Methodological trend: because market-wide effects are hard to study cleanly in experiments, researchers increasingly use causal inference / quasi-experimental designs, such as:

  • difference-in-differences
  • border designs

• The lecture reviews three main empirical examples, progressing from:

  1. a pricing policy shock
  2. large-scale randomized ad targeting
  3. privacy regulation affecting tracking/targeted ads
  4. a border design estimating prescription-drug ad spillovers and dynamics

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Paper 1: Price advertising ban lifted → small retail price changes

Source described: M. Malo and Wald Fogle — “Effective Price Advertising on Prices: Evidence in the Wake of 44 Liquor Mart”

Background shock (policy & legal change)

• Rhode Island banned advertising alcohol prices from 1956 to 1996 (e.g., mailers/window signs listing prices were illegal).
• A lawsuit ended in 1996, when the U.S. Supreme Court overturned the ban.
• After May 13, 1996, alcohol price advertising became legal in Rhode Island.

Research question

• How did allowing alcohol price advertising affect liquor prices?

Methodology: Difference-in-differences (with a control group)

• Data collection gamble / pre-decision anticipation

  • Prices were collected beginning June 1995, before knowing precisely how/when the legal outcome would land.
  • Hand-entered prices for 33 beverages across 115 liquor stores (pre-period).

• Control group construction

  • Use Massachusetts stores as controls:
    • Rhode Island stores are affected by legalization.
    • Massachusetts stores (some near the border, some not) provide a comparison.

• Difference-in-differences structure

  • Compare:
    • Rhode Island price changes pre vs. post
    • vs.
    • Massachusetts price changes pre vs. post
  • Regression components include:
    • time fixed effects and state fixed effects
    • an interaction term such as Rhode Island × post (policy effect)

Additional data gathered (proxying quantity and advertising uptake)

• Wholesale price regulation exists in both states, helping interpret retail pricing.
• Collected whether stores used:
  • print advertising
  • window advertisements
• Quantity proxy:
  • Used lottery ticket sales at each store as a rough measure of alcohol traffic/quantity.
  • Rationale: more foot traffic implies more alcohol buying and potentially more lottery sales.

Key findings

• Advertising uptake was low

  • After the ban ended, <10% of sampled stores advertised.

• Retail price effects were tiny

  • Estimated retail prices fell by only about 0.5% to 1% within a year.

• Mechanism breakdown

  • Stores that advertised set lower prices on advertised items (about 20% lower vs non-advertising counterparts).
  • But non-advertised prices barely changed—no clear “raise everything else” loss-leader strategy.
  • Non-advertising rivals in Rhode Island showed very limited competitive reaction.

• Quantity / welfare implication

  • Advertising stores’ share of lottery sales increased (e.g., 16.4% → 18.4%).
  • Still, because price changes were small and only a limited portion of demand appears to shift, aggregate consumer impact remained modest.

Lesson emphasized

• In this setting—starting from an effectively suppressed baseline—advertising had very limited market-level price/welfare impact.

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Paper 2: Randomized online ads (Yahoo) → estimating ROI is statistically hard

Source described: Randall Lewis and David Riley — “Online Ads and Offline Sales” (as referenced in the lecture)

Context

• Around 2000, Yahoo dominated page views.
• Yahoo sold display ad formats, including:
  • LRE (“Large Rectangle”) ads
  • ads on news/inside pages

Research question

• Measure ad effectiveness not just in online clicks, but also in offline purchases.

Methodology: Randomized controlled trial with “intent-to-treat”

• Partnership

  • A large offline retailer (framed as Macy’s/Bloomingdale’s) ran the campaign on Yahoo and allowed evaluation.

• Targeting population

  • Retailer had ~1.5 million customers.
  • A matching process linked customer records (credit card/home address) to Yahoo accounts.

• Randomization (80/20 split)

  • 80% treatment: ads were served (subject to auction and targeting rules).
  • 20% control: ads were withheld.

• Key complication

  • Treatment does not guarantee ad display:
    • display depends on auctions and competing bids (e.g., retargeting, demographic bids).
  • Therefore the estimate is closer to intent-to-treat than a “seen ad” effect.

Measuring outcomes (online + offline)

• Purchases were trackable because:
  • customers used credit cards in-store
  • sales were linked back to who saw the ads
• Purchases were matched to earlier ad exposure days.

Reported scale (campaign magnitude)

• Two ad waves (early and late fall).
• Examples mentioned:
  • click-through: about 0.28%
  • among those seeing ≥1 ad: about 7.2% clicked at some point
  • tens of millions of ads shown (e.g., 32 million ads to ~814,000 people in one wave)

Key observations and lessons

1. Return-on-advertising estimation is extremely difficult

   • Purchase distributions are very noisy (many zeros + heavy upper tail).
   • Detecting small ROI differences requires unrealistically tight standard errors.

2. Naively regressing purchases on “ad viewed” is biased

   • Ad views are not random; ad delivery correlates with intent (analogous to paid search intent).

3. Intent-to-treat results are noisy

   • Treatment-group sales are higher by a small amount (cents),
   • but confidence intervals are wide (ROI estimate imprecise).
   • Pre-period imbalance corrections (e.g., difference-in-differences) remain noisy.

4. Possible longer-run effects

   • Some point estimates suggest post-campaign benefits,
   • but the lecturer highlights skepticism about some controls (e.g., individual fixed effects) given shifting behavior over time.

Lesson emphasized

• Even large randomized designs can yield imprecise ROI because purchase outcomes are low-signal and noisy.
• Causal identification must avoid bias from endogenous ad viewing/delivery.

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Paper 3: GDPR opt-in tracking rules → quasi-experimental effects on targeted advertising

Source described: Difference-in-differences study (“Tobias’s paper”)

Institutional setting

• GDPR
  • adopted April 2016
  • effective May 2018
  • requires explicit opt-in consent for tracking European consumers
• Lecture emphasis:
  • cookie pop-up environment
  • high friction, but many users click “accept” or default settings

Research question

What does GDPR change?

• the amount of trackable behavior (cookies/recorded searches)
• ad intermediary economics (clicks/revenue)
• bidding dynamics and the ad market equilibrium
• the intermediary’s predictive accuracy for targeting

Methodology: Difference-in-differences using an intermediary dataset

• Data from an intermediary contractor serving many major travel sites.

• Mechanism:

  • intermediary observes clickstream/search behavior via cookies
  • runs auctions based on predicted user likelihood to buy on the current site

• Treatment/control:

  • Treatment countries (EU): UK, France, Germany, Italy, Spain
  • Control countries (non-EU): US, Canada, Russia

• Regression includes:

  • website fixed effects
  • country fixed effects
  • time fixed effects

• Key outcomes include:

  • number of search events the intermediary is allowed to record
  • plus clicks/revenue proxies for auction participants

Key findings (with magnitudes)

• Recorded tracking falls sharply

  • log unique cookies down about 12%
  • log recorded searches down about 11%
  • the immediate drop lines up with GDPR timing, supporting causal interpretation.

• Who drops out

  • distribution shifts:
    • fewer users “seen exactly once”
    • more users “seen multiple times”
  • suggests cookie blockers/deleters and/or privacy tools change the composition of observed users.

• Advertising intermediary revenue declines, then partially rebounds

  • clicks down on impact; revenue down (about 16% on the effect day)
  • over subsequent weeks, bids rise gradually

• Two proposed explanations for higher bids over time:

  1. remaining users are more valuable
  2. improved information/auction learning from a “cleaner” sample increases willingness to pay

• Time dynamics and learning

  • initial decrease, then partial offset as the system adapts to new data composition.

• Machine learning performance

  • prediction mean-squared error worsens initially due to distribution shift,
  • then improves as models update and measurement noise from cookie deletion/blocking decreases.

Lesson emphasized

• Privacy regulation can meaningfully reduce tracking and short-run ad revenue, while markets adapt through:
  • reweighting toward remaining users
  • improved auction prediction
  • retraining models to match changed tracking composition

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Paper 4: Border discontinuity + structural model → spillovers from drug ads

Source described: Brad Shapiro (lecture discussion; antidepressant TV advertising and prescription data)

Research questions

• Do direct-to-consumer (DTC) ads increase prescriptions?
• Are there spillovers to rival brands?
• How quickly do effects decay?
• Do firms under-advertise relative to an optimal equilibrium?

Methodology: DMA border design + fixed effects

• Map physician addresses to counties, aggregate to county-month.
• Advertising data:
  • TV advertising expenditures by brand in 101 US DMAs (city markets)
  • Sept 1999–Dec 2003

• Local advertising measure:

  • apportion national spend to DMAs by population share
  • add local-only spending

• Border identification:

  • compare outcomes on either side of DMA borders (spatial discontinuity / border effect)
  • use fixed effects to remove time-invariant demand differences, including:
    • product-border-quarter fixed effects
    • product-border-DMA fixed effects

Key empirical results (reduced form)

• Own-brand effect (DTC advertising)

  • scaling implies spending 1 cent per person can increase sales by about 2.4%.

• Rival spillover

  • rival ad coefficient is about 2/3 of the own-brand effect.

• Decreasing returns

  • quadratic terms show diminishing marginal returns.

• Interaction effect

  • the return to your ads falls when rivals advertise more—consistent with being pushed toward diminishing returns.

Structural model for dynamics and optimization

• Nested logit with three levels:

  1. inside good vs outside good
  2. antidepressant category choice (driven by advertising within category)
  3. within-category brand choice (driven by advertising for specific molecules)

• Advertising decay modeled by discount factors Δ^s

  • decay happens quickly but at different speeds across levels
  • “90% decays” about:
    • ~3 months at the within-category level
    • ~6 months at the aggregate level

• Spillovers:

  • a large portion of prescription gains goes to other firms, not just the advertiser.

Optimal advertising and under-advertising

• Shapiro avoids imposing supply-side optimality (advertising is new; firms may not know marginal returns initially).
• Simulations:
  • firms appear to advertise less than implied by equilibrium returns.
  • “Advertising cooperative” scenario:
    • due to spillovers/free-riding, coordinated advertising would increase total advertising.
• Profit implications:
  • simulations suggest large advertising increases yield profit gains (about 15% mentioned).

Lesson emphasized

• Advertising effectiveness includes:
  • own effects
  • rival spillovers (free-riding)
  • rapid decay over months
• These features help explain why observed advertising may be far below socially/collectively optimal levels.

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Methodologies / instructional elements explicitly present

Difference-in-differences (policy shocks)

1. Define treatment region where policy changes (e.g., Rhode Island alcohol price advertising allowed).
2. Choose control region not directly affected (e.g., Massachusetts).
3. Collect comparable outcome data pre/post (retail prices, optionally quantity proxies like lottery sales).
4. Estimate with fixed effects and a treatment interaction (e.g., Rhode Island × post).

Randomized controlled trials with intent-to-treat

1. Construct target audience by linking advertiser lists to platform identifiers.
2. Randomize eligibility into treatment/control groups (ads eligible vs withheld).
3. Account for platform auction reality: being eligible doesn’t guarantee ad display.
4. Measure outcomes using linked transaction data (online + offline).
5. Analyze intent-to-treat differences; avoid treating “ad viewed” as exogenous.

Difference-in-differences (regulation affecting tracking/targeting)

1. Define treatment based on regulation effective dates; choose non-treatment controls.
2. Use panel regressions with fixed effects (website × country × time).
3. Measure intermediary observables (cookies/search counts, clicks/revenue proxies, bids).
4. Interpret mechanisms carefully: consent/opt-out changes user composition, affecting bidding and prediction over time.

Border designs (spatial discontinuity)

1. Define markets (e.g., DMAs) mapped to counties.
2. Compare near-identical conditions across DMA borders.
3. Use strong fixed effects (including product-border-quarter and product-border-DMA).
4. Estimate reduced forms for own effects, rival spillovers, and diminishing returns.
5. Optionally build a structural demand model (e.g., nested logit with time-decay).

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Speakers or sources featured (as named or referenced)

• Katherine Tucker (mentioned for a survey of recent work)
• Malo (co-author in the Rhode Island/44 Liquor Mart example)
• Wald Fogle (co-author in the Rhode Island/44 Liquor Mart example)
• Benam (earlier 1970s cross-sectional advertising/pricing study; “Advertising Eyeglasses”)
• Alan Sorenson (mentioned in relation to data collection constraints)
• Joel (informally referenced in liquor-price collection anecdotes)
• Randall Lewis (Yahoo ads/offline sales controlled experiment)
• David Riley (Yahoo ads/offline sales controlled experiment)
• Tobias (GDPR intermediary difference-in-differences paper credited in the lecture)
• Brad Shapiro (border design + antidepressant advertising structural model)
• Glenn Ellison (referenced in an anecdotal/example name; not a direct study author)
• Supreme Court of the United States (legal decision discussed; not a speaker)
• European Union / GDPR (institutional source; not a speaker)

Lecture presenter: not explicitly named in the subtitles, but delivers and summarizes the papers.