Toshin

Digital marketing platforms report the sales they touch, and firms increasingly allocate budgets by those reports. Yet a sale that follows an advertisement is not necessarily a sale the advertisement caused. A customer who already wants a brand may search for it, click a sponsored result and buy, and the last click receives credit for demand created earlier by other activity. This paper calls that distortion over-attribution and separates two quantities that reports blur: sales closure, where the advertisement completed a purchase the customer had already decided on, and incremental sales, where the purchase would not have happened without it.

The paper combines a structured synthesis of the evidence with a quantitative analysis. The evidence comes from randomised field experiments in search and social advertising, comparisons of observational methods with experiments, a large study of television advertising, the IPA databank analysis by Binet and Field, the WARC Multiplier Effect report, and the documented case of Adidas. The quantitative analysis applies formulas to published statistics and runs a computational experiment with stated assumptions. It reports no new field data.

Five conclusions follow. First, attributed return can overstate incremental return by a wide margin. Using published medians from 663 Facebook experiments, a lower-funnel lift of 6 per cent implies that at most 5.7 per cent of conversions among exposed users were caused by the advertisement, and in a simulation selection alone made an observational estimate about 64 times the true lift. Second, a reported return that looks healthy can be below break-even once margin is applied: at a 40 per cent margin the incremental return must exceed 2.5, and a reported return of 2.0 cannot pay even if every sale is incremental. Third, measuring small lifts needs hundreds of thousands to millions of users per group, so single small tests can mislead. Fourth, no form of advertising is exempt: economic theory and a study of 288 brands show that television at low elasticities cannot pay at typical spending levels. Fifth, brand strength and long-run effects are under-credited by last-touch reporting, and the WARC evidence suggests that brand strength raises the return on performance spend.

The paper turns these conclusions into a decision framework with six rules, a break-even test, a sample-size rule and a channel-by-channel starting plan for brands, and sets out the experimental programme designed to test and size its propositions.

Keywords: marketing attribution, incrementality, demand creation, demand capture, sales closure, marketing mix modelling, marketing effectiveness, brand and performance

Modern marketing is measured more closely than at any point in its history. A firm can see which advertisement a customer clicked, when they clicked it and what they bought afterwards. That visibility has moved budgets toward the channels that report the cleanest connection between spend and sales, in particular paid search and performance social. The assumption beneath this shift is that a measurable connection is a causal one.

It is not always. Consider a person who wants new trainers. They search the internet, and the results offer several varieties of an Adidas shoe with prices side by side. The internet is very good at this: it holds the buyer's hand from a list of options to the final purchase. When the sale is recorded, the paid search click receives the credit and is counted as an incremental sale. But the buyer had usually arrived already thinking about a shoe, or about Adidas itself, and many searches contain the brand name. The same is true of a showroom. Everyone who walks in does not create a sale by walking in, and the person at the till is closing a sale, not creating one.

There is also a time problem. Most of the effect of advertising arrives indirectly and later. Someone sees Adidas communication on another platform, or notices the product in a film, becomes interested in the brand, and some time afterwards goes online and searches. The search then receives the entire credit for a sale that was prepared elsewhere.

This is not a hypothetical worry. In October 2019 Simon Peel, Adidas's global media director, told the EffWeek conference that the company had focused on efficiency rather than effectiveness. He said Adidas believed digital advertising was driving e-commerce sales, "and as a consequence we were over-investing" (Marketing Week, 2019). If a brand of that size and sophistication made the error, smaller firms with fewer analysts are unlikely to be immune.

Research question. How much of the revenue that digital marketing attribution assigns to advertising is incremental, why do firms keep funding on attributed numbers, and what should a brand do about it?

Contribution. The paper makes four contributions. It defines the distinction between sales closure and incremental sales and the metrics that follow from it. It synthesises the experimental and practitioner evidence into a small set of propositions, with an honest account of how strong the evidence behind each is. It sizes the problem with formulas, published statistics and a computational experiment. And it converts the results into a practical framework brands can use, including a break-even rule, a sample-size rule, a channel plan and a measurement roadmap.

Structure. Section 2 sets out the concepts. Section 3 describes the method and the author's position. Section 4 reviews the evidence. Section 5 presents the quantitative analysis. Section 6 synthesises the results into propositions. Section 7 gives the recommendation for brands. Sections 8 to 11 cover implications for strategists, limitations, the research agenda and the conclusion.

2.1 Four quantities that reports blur

• Attributed sales: sales assigned to an advertisement or channel by a rule or model, regardless of causation.

• Sales closure: a purchase that an advertisement or channel completed, where the customer had already formed the intention to buy. A branded search click is the typical case. A closure is real revenue, but it is not evidence that the advertisement created the demand.

• Incremental sales: the difference between sales with the advertising and sales that would have occurred without it. In a holdout design with n people per group, if the exposed group buys at rate p1 and the control group at rate p0, incremental purchases equal n multiplied by (p1 minus p0). This is the potential-outcomes definition of a causal effect (Rubin, 1974).

• Incremental contribution profit: incremental revenue less cost of goods, returns, delivery and the advertising cost itself. An incremental return on ad spend above 1 is not sufficient unless margin is accounted for.

2.2 Demand creation and demand capture

Advertising performs two functional roles. Demand creation raises the probability that people will want the brand in future, and its effects are long-run and diffuse. Demand capture converts existing interest into a completed purchase, and its effects are immediate and easy to observe. The same channel can perform both roles, so the unit of analysis is the role within a campaign, not the channel label.

2.3 Two metrics

Over-attribution ratio is attributed return divided by incremental return for a given activity. A ratio of 1 means attribution is accurate. A ratio of 3 means the report is crediting the activity with three times what it caused.

Break-even incremental return is one divided by the contribution margin after cost of goods, returns and delivery. With a 40 per cent margin it is 1 divided by 0.4, or 2.5. Activity should scale only when its incremental return exceeds this line.

Figure 1 shows the logic with a hypothetical example. The platform reports a return of 4.0, which looks comfortably above break-even. A holdout test shows only 30 per cent of the attributed sales were incremental, so the incremental return is 1.2. The over-attribution ratio is 4.0 divided by 1.2, or 3.3, and the activity loses money on every pound spent.

Figure 1. Reported, incremental and break-even return (hypothetical figures for illustration)

3.1 Approach

The paper is a structured narrative synthesis, not a systematic review with meta-analysis. Sources were selected for relevance to one question: how far attributed returns can be trusted as a guide to what advertising causes. Searches were run in October 2026 across academic databases and the open web, and sources were included when they met at least one of three conditions: they report randomised field experiments in advertising; they benchmark non-experimental methods against experiments; or they are substantial, documented practitioner evidence on how brand and performance activity interact. Original abstracts and publisher pages were used where available. Where a finding is taken from a published summary and not from the full report, as with parts of the WARC report, this is stated.

The quantitative analysis in Section 5 uses three tools. First, closed-form formulas for break-even, incremental share and sample size, with the inputs taken from published statistics and stated assumptions. Second, simple arithmetic transformations of published medians, such as converting a reported lift into the share of conversions it implies were caused by the advertisement. Third, a Monte Carlo simulation written in Python (version 3, with NumPy and SciPy) with a fixed random seed, in which users are assigned to groups with stated purchase probabilities, targeting rates and a stated true effect, and the results of an observational comparison and a randomised holdout are compared over 2,000 repeated trials at each of three population sizes. These are computational experiments. They show what follows from stated assumptions, and they are not empirical findings about any firm.

3.2 Grading the evidence

Sources differ greatly in how far they can support a causal claim, so each is graded. Grade A is randomised field experiments. Grade B is large observational or quasi-experimental studies and benchmarking work. Grade C is modelling studies and practitioner databanks, which show association and are open to selection and commercial bias. Grade D is company statements and single cases, which illustrate but do not prove. The conclusions in Section 6 are worded to match the grade of the evidence behind them.

3.3 Position of the author

I am a brand strategist and creative director based in London, with a BBA in Marketing and an MA in International Fashion Business and Luxury Brand Management. My work has been in brand strategy across fashion, luxury, automotive and consumer categories, and I have written a book-length treatment of attribution (Tazdid, 2026). This matters for the reader because it is a source of both insight and bias. I have seen budgets defended with dashboards, and I begin from the view that over-attribution is real. To guard against confirmation, the paper includes evidence that cuts against a simple story, including a study finding low returns to television advertising, and it states what result would count against each proposition.

The title "strategist" covers several different jobs. Figure 2 places the main types on two questions: whether the work mainly creates or captures demand, and whether it is judged by craft or by numbers. My position is that of a brand strategist on the demand-creation side who is moving toward measurement, so that what demand creation earns can be shown in financial terms.

Figure 2. Where the author sits among strategist types

4.1 Randomised evidence on paid search and display

The most direct evidence comes from field experiments in which advertising is switched off for a random group. Blake, Nosko and Tadelis (2015) ran large-scale experiments at eBay. They found that brand keyword advertising showed no measurable short-term benefit. For non-brand keywords, new and infrequent users responded positively, but frequent users, whose purchases were not influenced by the ads, accounted for most of the spend, so average returns were negative. The pattern is exactly what the closure argument predicts: paying to reach people who already intend to buy purchases few extra sales.

Lewis and Rao (2015) analysed 25 large field experiments with major US retailers and brokerages covering about 2.8 million dollars of digital advertising. Their central finding concerns measurement itself. Individual-level sales are highly volatile compared with the per-person cost of advertising, so informative experiments can require more than 10 million person-weeks, and the median confidence interval on return on investment was over 100 percentage points wide. Observational methods face serious selection bias because advertising is targeted. Two lessons follow. The apparent precision of a dashboard return is illusory, and firms that want causal answers must plan for large tests.

4.2 Observational methods against experiments

Gordon et al. (2019) used 15 US advertising experiments at Facebook, covering hundreds of millions of user observations, to test the observational methods advertisers commonly use. They found that these methods often fail to reproduce the true effect found in the randomised tests. Estimates generally ran high, though in some cases they ran significantly low. A larger follow-up (Gordon, Moakler and Zettelmeyer, 2023) covered 663 Facebook experiments, each described by more than 5,000 user and experiment features. Double machine learning performed better than stratified propensity score matching, but the authors conclude that neither method performs well. Median randomised lifts were 28, 19 and 6 per cent at the upper, middle and lower funnel, and the median absolute difference between the non-experimental and experimental lift was 115, 107 and 62 percentage points respectively. Section 5.2 works through what these numbers imply. The conclusion is that better modelling of observational data does not replace running experiments.

4.3 No advertising is exempt: the television evidence

It would be easy to read the literature as an argument that performance advertising is bad and brand advertising is good. The evidence does not support that. Shapiro, Hitsch and Tuchman (2021) studied 288 established consumer packaged goods brands using retail sales data from about 12,000 stores and purchase data from more than 60,000 households. The median advertising elasticity for television was about 0.01, so doubling television advertising raised sales by only about 1 per cent. Marginal return on investment was negative for more than 80 per cent of brands, and the overall return on the observed advertising schedule was positive for only about one third of brands. The authors note that results cover established brands, exclude streaming, and depend on assumed margins, and that newer products may respond more. This result guards against a lazy conclusion. The case for brand investment must be tested like any other, and the central message of the paper is to measure, not to prefer one kind of spend.

4.4 Brand building, long-run effects and the multiplier

Binet and Field (2013) analysed 996 campaigns entered in the IPA Effectiveness Awards between 1980 and 2010. They report that the most effective balance on average is about 60 per cent of budget on brand building and 40 per cent on sales activation, that emotional campaigns were nearly twice as likely as rational ones to produce top-tier long-term profit growth, and that campaigns aimed at recruiting new customers produced about three times as many business effects as loyalty campaigns. This is Grade C evidence, since entries are self-selected award submissions, and the split is a benchmark that varies by category. Sharp (2010) argues similarly that growth comes mainly from reaching many light buyers, which is a demand-creation mechanism.

The WARC Multiplier Effect report (WARC, 2025), produced with Analytic Partners, BERA.ai, Prophet and System1, extends this argument. Its central idea is that brand and performance advertising do not add (brand plus performance) but multiply (brand times performance), because a stronger brand makes performance advertising work harder. Analytic Partners' modelling found that moving from a performance-only approach to a mixed approach raised total revenue return by 25 to 100 per cent, averaging about 90 per cent, while the reverse move cut return by about 40 per cent on average. System1 found that most strong equity-building ads also performed well in the short term, and a Prophet survey of 300 North American marketers found that most winning companies connected brand and demand activity. The report suggests a brand baseline of at least 30 per cent of budget, with 40 to 60 per cent typical of best practice, and treats search above about 25 per cent of budget as a warning. Its limits are that the evidence is mainly modelling rather than experiments, the partners are commercial, the research is centred on the United States, and the figures here come from reports about the study, not the full report. It is Grade C evidence and is best treated as a hypothesis to test.

4.5 The Adidas case

Adidas offers a documented example of the pattern at scale (Marketing Week, 2019). Spend was then about 77 per cent performance and 23 per cent brand. Econometric analysis indicated that 60 per cent of revenue came from first-time buyers, not the loyal customers the company had assumed, and that brand activity drove most sales across wholesale, retail and e-commerce. Video, television, outdoor and cinema, which had looked weak under last-click attribution, were found to drive e-commerce sales. In one market, stopping paid search spend caused no visible fall in traffic or revenue from organic search. Peel said the company was building an attribution model combining econometrics with test and learn. The article reports no measured business results from the changes, so this is Grade D evidence. It illustrates, and does not prove, the mechanism.

4.6 How the gap can be measured

Three methods recur. Randomised holdouts and ghost-ad designs give user-level causal answers where the platform allows them (Kohavi, Tang and Xu, 2020). Geo experiments compare matched regions, usually with time-based regression or synthetic controls, when user-level randomisation is not possible (Vaver and Koehler, 2011). Marketing mix models estimate channel contributions from aggregate data and can cover long-run and offline effects, but they depend on modelling choices and can mislead without outside anchors (Chan and Perry, 2017). Google's Meridian documentation recommends using geo experiments to set priors that calibrate marketing mix models, which is the logic of combining the methods.

4.7 Summary of the evidence

This section applies theory and formulas to published statistics, and runs a controlled computational experiment, to size the problem. It does not report new field data. Every input is either a published statistic, cited to its source, or a stated assumption, and the assumptions are listed so that a reader can change them. The methods are described in Section 3.1 and the results can be reproduced from the stated parameters.

5.1 Formulas

Let R be the reported (attributed) return on ad spend, s the share of attributed sales that are incremental, m the contribution margin, and L the lift, meaning the percentage increase in conversions among exposed users compared with a randomised control.

• F1. Incremental return: iROAS = R multiplied by s. The over-attribution ratio is R divided by iROAS, which equals 1 divided by s.

• F2. Break-even incremental return: 1 divided by m. The break-even share of attributed sales that must be incremental is 1 divided by (R multiplied by m).

• F3. Profit per pound of spend: (iROAS multiplied by m) minus 1.

• F4. Incremental share implied by a lift: s = L divided by (1 plus L). If every conversion among exposed users is credited to the advertisement, the over-attribution ratio is (1 plus L) divided by L.

• F5. Sample size per group for a two-group test: n = 2 multiplied by (z for significance plus z for power) squared multiplied by CV squared, divided by L squared, where CV is the coefficient of variation of the outcome. For a conversion outcome with base rate p, CV squared is (1 minus p) divided by p. The values used are 5 per cent two-sided significance and 80 per cent power, so the sum of the two z values is 2.80.

• F6. Dorfman and Steiner condition: with advertising elasticity e and contribution margin m, the profit-maximising advertising-to-sales ratio is e multiplied by m, and the marginal profit return per pound of advertising is (m multiplied by e) divided by the advertising-to-sales ratio (Dorfman and Steiner, 1954).

5.2 What published statistics imply

Gordon, Moakler and Zettelmeyer (2023) report, for 663 Facebook experiments, median randomised lifts of 28, 19 and 6 per cent at the upper, middle and lower funnel, and median absolute differences between non-experimental and experimental lift estimates of 115, 107 and 62 percentage points. Applying F4 and simple division gives Table 1.

Table 1. Calculations from published medians (Gordon, Moakler and Zettelmeyer, 2023)

Two results stand out. First, the error of non-experimental methods grows relative to the true lift as the funnel narrows: the median error is about 4 times the lift at the upper funnel and about 10 times at the lower funnel, where the purchase is closest and the true lift is smallest. Second, at a 6 per cent median lift only 5.7 per cent of the conversions that follow exposure were caused by it. A rule that credits every conversion following exposure would therefore over-attribute by a factor of about 17.7 at the median lower-funnel outcome. Real attribution windows and rules are narrower than this extreme case, so 17.7 should be read as an upper bound on the logic and not as a typical dashboard error.

5.3 Break-even and sensitivity

Table 2 applies F1 to F3 to a reported return of 4.0 and a 40 per cent margin, so that break-even is an incremental return of 2.5 and a break-even incremental share of 62.5 per cent.

Table 2. Reported return of 4.0 at a 40 per cent margin

Figure 3. Profit per pound of spend by incremental share, at three margins

The break-even share depends on both the reported return and the margin (Table 3). A reported return of 4.0 needs at least 62 per cent of attributed sales to be incremental at a 40 per cent margin. A reported return of 2.0 at a 40 per cent margin needs more than 100 per cent, which is impossible, so that spend loses money even if every attributed sale is incremental. Reported returns that look healthy are often below break-even once margin is applied, before any question of incrementality is asked.

Table 3. Share of attributed sales that must be incremental for spend to break even

5.4 Can the gap be measured? Power analysis

Because incremental lifts at the lower funnel are small, tests need very large samples. Table 4 applies F5 for two outcomes: a conversion outcome with a 2 per cent base rate, and revenue per person with a coefficient of variation of 10, the order of magnitude reported by Lewis and Rao (2015) for individual-level sales.

Table 4. Users needed per group for 80 per cent power at 5 per cent significance

Figure 4. Required sample size against the lift to be detected

The minimum detectable lift for a revenue outcome with CV of 10 is about 12.5 per cent with 100,000 users per group, 4.0 per cent with one million and 1.25 per cent with ten million. Expressed as a return, suppose mean revenue per person is 50 pounds, so the standard deviation is 500 pounds, and the advertising costs 0.50 pounds per exposed person. The 95 per cent confidence interval on incremental return is then about 17.5 return points wide with 100,000 users per group, 5.5 points wide with one million and 1.75 points wide with ten million. This agrees in kind with Lewis and Rao's finding that the median confidence interval on return was over 100 percentage points wide. A single small test can therefore fail to separate a profitable return from an unprofitable one, which is a reason to plan sample size in advance, use geo designs and pooled evidence, and treat a dashboard return with no interval as an unsupported number.

5.5 A computational experiment on selection bias

To show how a reported return can diverge from an incremental one when exposure is targeted, a simulation was run with stated parameters. Users are of two types. A high-intent group (10 per cent of users, such as people searching for the brand) buys with probability 20 per cent without advertising. The remaining 90 per cent buy with probability 1 per cent. Advertising is targeted: 60 per cent of high-intent users and 10 per cent of other users are eligible to see it. Ten per cent of all users are held out at random and never exposed. The true effect of exposure is a 6 per cent relative increase in purchase probability, the median lower-funnel lift in Table 1. Three estimates were compared: the true lift; a randomised holdout among eligible users; and a comparison of exposed users with users who were never eligible, which is a common observational method.

Table 5. Expected results of the selection-bias simulation

The observational comparison finds a lift of 381 per cent where the true lift is 6 per cent. Nothing in the setup makes the advertising more powerful. The entire gap comes from who is targeted, which is the selection mechanism described by Lewis and Rao (2015) and Gordon et al. (2019). The randomised holdout recovers the truth on average, but a single test is noisy. Repeating the holdout 2,000 times at three population sizes gave Table 6.

Table 6. Results of 2,000 repeated holdout tests (10 per cent holdout)

Figure 5. Selection-bias simulation: expected estimates (left) and spread of repeated holdout tests (right)

Two lessons follow. An observational comparison can be wrong by an order of magnitude even when advertising works exactly as assumed, and a randomised test fixes the bias but needs enough users. At 200,000 users the holdout had only an 18 per cent chance of detecting a real 6 per cent lift, and the 95 per cent range of estimates ran from about minus 6 to plus 21 per cent. This is a stylised setting with assumed parameters, so the figures illustrate mechanisms and are not estimates of any firm's performance.

5.6 An economic theory check

Dorfman and Steiner's (1954) condition gives a second, independent check on whether a given level of advertising can pay. Table 7 applies F6 at a 40 per cent margin. It shows the marginal profit return per pound of advertising for different advertising elasticities and advertising-to-sales ratios. A value below 1 means that the next pound spent returns less than a pound.

Table 7. Marginal profit return per pound of advertising at a 40 per cent margin (Dorfman and Steiner, 1954)

Shapiro, Hitsch and Tuchman (2021) report a median television advertising elasticity of about 0.01 across 288 brands. At that elasticity the profit-maximising advertising-to-sales ratio is 0.4 per cent, and a brand spending 5 per cent of sales on advertising earns only about 8 pence of margin per extra pound. This is consistent with their finding that marginal return on investment was negative for more than 80 per cent of brands. The theory also shows the way out. At an elasticity of 0.10, spending up to 4 per cent of sales pays. Elasticities differ greatly by brand, channel and context, so the conclusion is not that advertising should be cut but that its elasticity has to be measured before the budget is set.

5.7 Consistency check on the Multiplier Effect

WARC (2025) reports that moving from performance-only to a mixed approach raised revenue return by 25 to 100 per cent, averaging about 90 per cent, and that the reverse move cut return by about 40 per cent on average. These figures can be checked against each other. If a change multiplies return by 1.9, reversing it divides by 1.9, a fall of 47 per cent. An uplift range of 25 to 100 per cent implies a reverse fall of 20 to 50 per cent. A 40 per cent fall corresponds to an uplift of about 67 per cent, inside the reported range. The figures are therefore mutually consistent, although this says nothing about whether the underlying models are right, which only experiments can show.

5.8 Summary of the quantitative findings

1. Reported returns must be compared with break-even, not with 1. A reported return below 1 divided by the margin, which is 2.5 at a 40 per cent margin, loses money even if every attributed sale is incremental.

2. If lifts at the lower funnel are as small as the published median of 6 per cent, then at most about 6 per cent of conversions among exposed users were caused by the advertising, and credit rules that award all such conversions overstate by up to 17.7 times.

3. Selection alone, with no advertising effect beyond the assumed 6 per cent, produced an observational lift estimate about 64 times too high.

4. Measuring small lifts needs hundreds of thousands to millions of users per group, so tests must be planned with a power calculation, and single underpowered tests should not decide budgets.

5. Economic theory agrees with the empirical studies: at low advertising elasticities, typical advertising-to-sales ratios cannot pay, and the elasticity is the quantity to measure.

6.1 Why over-attribution happens

Five mechanisms appear across the evidence. The first three are well supported. The last two are interpretations that need more direct testing.

1. Selection. Advertising is targeted at people likely to buy, so exposed users differ from unexposed users even without any advertising effect (Lewis and Rao, 2015; Gordon et al., 2019).

2. Intent capture. Channels placed at the moment of purchase, such as branded search, are reached by people who have already decided (Blake, Nosko and Tadelis, 2015).

3. Delay and indirectness. Brand effects arrive late and through other channels, so last-touch rules assign them to whatever came last (Binet and Field, 2013; Marketing Week, 2019).

4. Measurability bias. Budgets drift toward what can be measured quickly, which favours capture over creation. Adidas described focusing on the wrong, short-term metrics.

5. Organisational incentives. Speed, apparent precision and the need to show accountability make dashboard numbers attractive even to teams who doubt them. Evidence here is mostly anecdotal and is a priority for research.

6.2 The doom loop

The mechanisms combine into a loop. Attributed return makes performance look efficient and brand look unprovable, so budget moves to performance. The brand weakens, performance spend becomes more expensive per sale, and the response is more performance spend. WARC describes this as a doom loop. If the multiplier is real, the loop damages both halves of the plan, which is why it is worth testing directly.

6.3 Propositions

6.4 What the evidence cannot yet say

The evidence does not give a reliable typical value of the over-attribution ratio by channel, because published experiments are few, differ in design, and may suffer from publication bias. It does not establish the size of the multiplier, since the main source is modelling. It says little about how organisations actually make allocation decisions. These are the gaps the research agenda in Section 10 addresses, and they are the reason the recommendation below uses tests and not fixed benchmarks wherever possible.

In one sentence: fund what creates sales, not what closes them. Treat attributed return as a report of where sales were closed, use controlled tests to find what marketing actually created, and allocate budget by incremental contribution profit.

7.1 Six rules

1. Separate creation from closure. Label every campaign as mainly demand creation or demand capture, and report closed sales separately from incremental sales. Do not describe a closure as an acquisition.

2. Treat capture channels as unproven until tested. Branded search, retargeting and last-click-heavy activity should start with a low assumed incrementality. Test the largest of these first with a holdout, ghost-ad or geo test, since that is where the most money is likely to be wasted.

3. Change the metric. Judge activity by incremental contribution profit, not reported return on ad spend. Scale only when incremental return exceeds the break-even return of one divided by contribution margin.

4. Calibrate the models with experiments. Use marketing mix modelling for long-run, brand and offline effects, and feed experimental results into it. Where methods disagree, investigate before moving budget.

5. Rebalance in steps and protect the brand. Use the Binet and Field 60:40 split and the WARC guides (a brand baseline of at least 30 per cent, and caution when search exceeds about 25 per cent) as starting references only. Move budget in steps of perhaps 10 to 20 per cent and re-test. Do not cut brand because its effect is hard to trace, and do not cut capture without a test, since defending branded search against competitors can sometimes be worth paying for. Because television showed low average returns in Shapiro et al. (2021), brand spend must also earn its place through measurement.

6. Put finance and marketing in the same room. Make them jointly own the measurement plan. Test each major channel at least once a year, reward teams on incremental results, and record what each test changed.

Planning the test. Before running any test, compute the sample size with F5 and decide in advance what result will change the budget. Detecting a 6 per cent lift on a 2 per cent conversion rate needs about 214,000 users per group, and detecting a 1 per cent lift needs about 7.7 million (Table 4). If a channel is too small to power a user-level test, use a geo test, a longer test window or pooled results across campaigns, and report the confidence interval with every result.

7.2 Where to start, by channel

7.3 Twelve-month roadmap

7.4 What the recommendation does not say

It does not say digital advertising does not work, and it does not say brand advertising always does. A platform lift test measures only that platform's effect, some decisions cannot be randomised, and attribution can also under-credit a channel. Platforms that publish studies on this have an interest in the answer. The recommendation is that value must be measured with controlled evidence, and that every claimed return, from performance or from brand, should be asked the same question: what would have happened without it?

For strategists on the demand-creation side, the findings change the argument they need to make. Brand work is often defended with language of meaning and reputation, which finance teams discount because it cannot be traced. The evidence suggests a stronger approach. Strategists can show that the dashboard understates, and sometimes overstates, what a channel earns, propose a test that gives a causal answer, and express the result in contribution profit. The test also protects strategists from their own bias, because television and brand spend can fail it. A strategist who can both argue for demand creation and show its measured return is more credible than one who can only do the first.

For agencies, the implication is that reporting attributed return alone is a risk. A client who later learns that a large share of reported sales were closures may reasonably question the whole account. Offering incrementality testing as part of the service turns a threat into an advantage.

• The paper is a synthesis and reports no new experimental data. Its propositions are supported to different degrees, as the grades show.

• Parts of the WARC evidence are taken from published summaries and not from the full report, which is behind a registration page.

• The quantitative analysis in Section 5 uses stated assumptions. The simulation is stylised, its parameters were chosen to illustrate mechanisms, and its numbers are not estimates for any firm. The power calculations use a normal approximation and a coefficient of variation taken from one published source.

• Published experiments may over-represent large firms and platforms that allow testing, and may suffer from publication bias.

• The Binet and Field data are self-selected award entries, and the WARC evidence is mostly modelling from commercial partners.

• The Adidas case reports no measured outcomes of the changes. It illustrates the mechanism and does not prove it.

• The author's background in brand strategy is a source of potential bias, addressed in Section 3.3 by including contrary evidence and stating what would count against each proposition.

• Experiments identify short-run effects well and long-run brand effects poorly. Holdouts understate the value of demand creation, so mix modelling and brand tracking are needed alongside them.

The propositions in Section 6 are the basis of a doctoral programme of five linked studies. Each hypothesis is paired with a result that would support it and one that would refute it, to be preregistered before data are analysed. The thresholds are provisional.

The studies are: a systematic review and meta-analysis of published field experiments (Study 1); holdout and geo experiments with two to four partner firms, with branded and non-branded search as the central case (Study 2); a marketing mix modelling comparison calibrated with the experiments (Study 3); a qualitative study of how marketing and finance teams make allocation decisions (Study 4); and the development and validation of the contribution-profit decision framework (Study 5). A result that refutes these hypotheses is still an outcome, because it would show where attribution can be trusted.

The simulation in Section 5.5 would be replaced in Study 2 by real exposure and outcome data, and the assumed parameters by estimates. Study 3 should also test the multiplier directly, for example by asking whether the incremental return of the same search campaign changes with brand strength, using a geo design that varies brand and performance levels in different regions.

The ability to measure a sale is not the ability to explain why it happened. The evidence reviewed here shows that attributed returns can overstate what advertising caused, that dashboard methods often fail to recover true effects, and that brand and long-run effects are under-credited in a way that can push budgets into a loop of rising spend and falling returns. It also shows that no channel is exempt from the question of whether it earns its cost.

The calculations make the stakes concrete. At a 6 per cent lift only about 6 per cent of conversions after exposure are caused by the advertisement, observational comparisons can overstate lift by an order of magnitude through selection alone, a reported return below 1 divided by the margin (2.5 at a 40 per cent margin) loses money even if every sale is incremental, and measuring small lifts takes hundreds of thousands to millions of users. The practical answer is a discipline and not a preference. Separate sales that advertising created from sales it closed. Test the largest capture channels first. Judge activity by incremental contribution profit against a break-even line. Calibrate models with experiments. Move money in steps. Make finance a partner. Brands that follow it will fund the marketing that grows the business, not the marketing that merely reports it. The research programme in Section 10 is designed to replace the default assumptions in this paper with measured bounds.

Binet, L. and Field, P. (2013) The Long and the Short of It: Balancing Short and Long-Term Marketing Strategies. London: Institute of Practitioners in Advertising.

Blake, T., Nosko, C. and Tadelis, S. (2015) 'Consumer heterogeneity and paid search effectiveness: a large-scale field experiment', Econometrica, 83(1), pp. 155-174.

Chan, D. and Perry, M. (2017) Challenges and Opportunities in Media Mix Modeling. Google Inc. Research report.

Gordon, B.R., Zettelmeyer, F., Bhargava, N. and Chapsky, D. (2019) 'A comparison of approaches to advertising measurement: evidence from big field experiments at Facebook', Marketing Science, 38(2), pp. 193-225.

Gordon, B.R., Moakler, R. and Zettelmeyer, F. (2023) 'Close enough? A large-scale exploration of non-experimental approaches to advertising measurement', Marketing Science, 42(4), pp. 768-793.

Dorfman, R. and Steiner, P.O. (1954) 'Optimal advertising and optimal quality', The American Economic Review, 44(5), pp. 826-836.

Google (n.d.) Meridian GeoX: geo experiments for incrementality and MMM calibration. Available at: https://developers.google.com/meridian/geox

Kohavi, R., Tang, D. and Xu, Y. (2020) Trustworthy Online Controlled Experiments: A Practical Guide to A/B Testing. Cambridge: Cambridge University Press.

Lewis, R.A. and Rao, J.M. (2015) 'The unfavorable economics of measuring the returns to advertising', The Quarterly Journal of Economics, 130(4), pp. 1941-1973.

Marketing Week (2019) 'Adidas: We over-invested in digital advertising', 17 October. Available at: https://www.marketingweek.com/adidas-marketing-effectiveness/

Rubin, D.B. (1974) 'Estimating causal effects of treatments in randomized and nonrandomized studies', Journal of Educational Psychology, 66(5), pp. 688-701.

Shapiro, B.T., Hitsch, G.J. and Tuchman, A.E. (2021) 'TV advertising effectiveness and profitability: generalizable results from 288 brands', Econometrica, 89(4), pp. 1855-1879.

Sharp, B. (2010) How Brands Grow: What Marketers Don't Know. Melbourne: Oxford University Press.

Tazdid, T.H. (2026) Attribution Nightmare. Unpublished manuscript.

Vaver, J. and Koehler, J. (2011) Measuring Ad Effectiveness Using Geo Experiments. Google Inc. Research report.

WARC (2025) The Multiplier Effect: A CMO's guide to brand building in the performance era. London: WARC, with Analytic Partners, BERA.ai, Prophet and System1. Available at: https://page.warc.com/the-multiplier-effect-report