Programmatic M&A: the claim that outlived its test

Somewhere in your building, a slide is being drafted with a McKinsey chart on it. The chart says that companies pursuing “programmatic M&A”, many small acquisitions made steadily year after year, outperform every other approach to dealmaking: the big bet, the occasional opportunistic buy, and the organic path. The claim has been refreshed roughly every other year since 2012, amplified through Harvard Business Review under its authors’ own bylines, and echoed in an investor literature of “serial acquirer” portfolios. It is, by circulation, one of the most successful empirical claims in corporate strategy.

This essay does something nobody’s slide does: it puts the claim beside its own record and beside its test. Both turn out to be stranger than the chart. The claim’s record begins with its own shop publishing the opposite finding nine months before the claim was born. The test is the study built to ask the program-level question the claim answers, and it replies with conditions rather than a verdict. Across every document this piece’s research could find, in a six-place sweep run before a word was drafted, the claim and the test never share a page. That absence is not an accusation; it is the gap this piece exists to close.

Why did original research produce null results for the marketing claim?

In April 2011, three McKinsey authors, Andres Cottin, Werner Rehm and Robert Uhlaner, published the firm’s first read of the population that would carry everything that followed: the world’s top 1,000 companies by market capitalisation, 917 firms after exclusions, and more than 30,000 deals. Their finding, in the article’s own words, was that patterns of deal size and frequency “have made little difference in performance as measured by excess total returns to shareholders.” The distributions were “widely distributed and overlapping.” Their conclusion: “the size and number of deals matter less than the discipline with which they are identified, priced, integrated, and managed.”

Nine months later, in January 2012, two of the same three authors, Rehm and Uhlaner, now with Andy West, re-segmented the same population into archetypes: large-deal acquirers, programmatic acquirers, tactical acquirers, selective acquirers, and organic growers. Out of that segmentation came the exhibit title on which the next decade would be built: “Companies using a programmatic strategy are the most successful.” The overlap had not disappeared. It had moved to footnote 4: “However, the confidence intervals for average returns are overlapping.”

Two dated findings from one shop, nine months apart, same population. This piece draws no inference about why. It records the sequence, because no refresh since has cited the first.

How did metric definitions drift to preserve an unverified industry claim?

To outperform as a programmatic acquirer, a company must first be classified as one, and the classification has never held still. Every McKinsey document this essay holds that states a threshold states a different one, and one of them states two.

The headline moves with the definition. The 2021 refresh reports programmatic acquirers delivering about 2% more in excess total shareholder returns annually, with 65% of them beating their peers, or “two out of the three companies.” The 2023 refresh reports 3.9% for the past decade against 2.9% for the 2010s, and adds that among programmatic acquirers, the ones doing the most deals won most often: 70% outperformed their lower-volume programmatic peers. None of these figures is comparable to the last, because the population, the window and the archetype boundaries have all shifted between tellings, and the reader is never shown the reclassification.

A definition that moves is not evidence of anything except this: whatever your board is being shown, it is not one finding replicated five times. It is one thesis, re-derived five ways, by a research program whose own first reading found no pattern.

What do original empirical citations reveal about legacy marketing benchmarks?

The January 2012 article carries a second footnote worth more than its exhibits. Footnote 9, quoted whole: “As with the other analyses, this is a correlation, not necessarily a causative relationship. Although we feel confident that the deal strategy contributed to the outperformance, it is possible that better-performing companies executed more deals in the wake of their success.”

That is the reverse-causality problem, stated by the claim’s own authors in its founding document: maybe steady acquirers win, or maybe winners acquire steadily. Companies that are performing well have the currency, the confidence and the debt capacity to do deals every year; classifying companies by their realized deal pattern, after the fact, cannot separate the two. Of the five later documents this essay holds: 2018, 2019, 2021, 2022, 2023: none restates the caveat. The 2019 refresh cites the 2012 article for its finding; the caveat does not travel with it. Nor does footnote 4’s overlap. The claim compounds; its qualifications do not.

This is the same pattern the integration essay found in the synergy literature: the vendor’s own study contains the hedge, and the citation chain strips it. Here the hedge and the claim were born in the same document, which makes the stripping easier to see, and easier to check. Both footnotes are three clicks away from any slide that cites the chart.

Why did the widely quoted benchmark fail rigorous replication tests?

One peer-reviewed study was built to test the program construct whole, not “do acquisitions pay?”, on which there are hundreds, and not single pieces of the pattern, which its own introduction credits to earlier work, but rate, rhythm and scope together, with the moderators: “does the pattern of a deal program predict returns?” It appeared in the Strategic Management Journal in 2008, four years before the archetype chart: Laamanen and Keil, “Performance of serial acquirers.” Its motivation section cites the consulting optimism about serial acquirers by name: Frick and Torres in McKinsey Quarterly, 2002; Rovit and Lemire in HBR, 2003: as the phenomenon to test. The claim’s ancestors are in the test’s opening paragraphs. No McKinsey document this essay holds or its research could find cites the test back.

What the test found, in a panel of 611 U.S. companies that made four or more acquisitions between 1990 and 1999: 5,518 deals, measured on three-year excess market returns: a high acquisition rate hurts (−0.071, p<.01). High variability in the rate: bursts and pauses: hurts too (−0.104 as a direct effect, at the ten-percent level; −0.197, p<.01, for firms with no acquisition experience, in the model where experience enters). Experience buys tolerance for an uneven program, not for a fast one, and its direct effect is negative. Size buys tolerance for both. Scope: spreading the program across businesses: worsens the rate penalty; its interaction with variability is not significant. The models explain 2–4% of variance, which the paper states rather than buries. These are conditions, not a verdict: steady rhythm, focus, size and scar tissue are when a deal program hurts less. Nothing in the paper says programs win.

One more result deserves its own paragraph, because it runs in McKinsey’s direction and this essay would be dishonest without it. In a robustness note, Laamanen and Keil report that over the full 10–13-year horizon, the most frequent acquirers in their sample: 173 firms with ten or more deals: earned median excess returns of +12.6% per year, against −3.9% for the 438 firms with four to nine deals. The paper’s prose calls the difference significant; the analysis is filed as non-reported, and no test statistic for it appears anywhere in the article. It is a descriptive split, and it is the strongest program-level number the frequent-acquirer thesis has: stronger support than anything in the archetype charts, and carrying the same disclaimer, in the authors’ own limitations section: “we cannot claim causality. Some of the performance effects we find for the most active acquirers could be due to superior prior performance of the acquirer.”

So the piece’s title is precise. The claim did not fail its test. It outlived it: relaunched in 2012, four years after the test published, without citing it, and not examined at its own terms in any document this research could find.

Which five academic disciplines established contradictory performance thresholds?

Around the claim and its test sits an academic record that looks contradictory until you notice that no two entries measure the same thing.

At the level of the deal announcement, frequent acquirers look good and get worse: firms completing five or more acquisitions within three years earned a positive average announcement return (+1.77%, five-day window) in Fuller, Netter and Stegemoller’s 1990–2000 sample, where nonpublic firms made up 81% of all acquisitions in the takeover market they study, and the returns decline as deals accumulate. At the level of the CEO, in samples of public-company targets, the same clock runs negative: announcement returns to an executive’s later deals average −1.51% in Billett and Qian’s data, whose long-run buy-and-hold estimates are statistically indistinguishable from zero, and whose interpretation is not learning but self-attribution: deal-making CEOs read early luck as skill. At the level of organizational learning, Haleblian and Finkelstein found performance falling with early acquisition experience and recovering only around the eighth deal: a U-shape the same paper could not reproduce when experience was measured over the recent five years. At the level of persistent skill, Golubov, Yawson and Zhang concede the right warning in their own words: persistence “might not necessarily be evidence of skill”, and find that top acquirers stay top; among frequent acquirers specifically, the persistence fails their univariate quintile test once expected returns are stripped out, while the top-percentile result survives it. The authors write that the successes “may or may not be due to skill.”

And at the level of the trade press pushback, the 2024 book The M&A Failure Trap: the closest thing the claim has to a published critique: turns out to hold the smallest effect in this whole record: on the authors’ ten-factor scorecard, distilled from their 43-variable model, each acquisition in the buyer’s prior five years adds +0.04 to a deal’s success score, the least of any factor, with the sign flipping negative in biotech and oil. Their preamble states the missing-variable problem plainly: strong operations can drive both the deal program and the returns, which is footnote 9’s point, made from the other side. Two cautions from the same book: its “failure” construct requires clearing three bars at once on each year’s largest deal only, a design that both inflates the failure headline and discards exactly the small deals frequent acquirers make. And the statistic circulating in practitioner summaries under this book’s name: serial acquirers with ten or more deals succeeding at 54% against 23% for first-timers: is not in the book. The 54% is a scorecard illustration; the 23% belongs to pre-reorganization deals. This essay’s own research pipeline imported that figure from a summary before the full read caught it. That is how this literature works: the numbers that circulate are not reliably the numbers in the documents.

Deal-level announcement windows, CEO-level deal order, firm-level buy-and-hold returns, archetype-level decade TSR, a conjunctive success construct scored on largest deals. Five yardsticks. The playbook essay made the case that a measured playbook and a marketed playbook are different objects; here the problem is prior: the claim and its would-be refutations are not even measured on the same axis. Nothing in this record can be summed, and this essay has not summed it.

How can commercial executives audit claims before adopting external industry benchmarks?

The honest verdict on programmatic M&A is three words: conditional, metric-dependent, untested as stated. That is not a verdict against deal programs. The strongest number in the nearest academic test favors them: as an untested median. What the record supports is not a strategy recommendation but a set of questions, and they are better questions than the chart’s.

The test’s conditions convert directly into diligence questions for your own program, and none requires buying anything. Is your deal rhythm steady, or does it come in bursts? Rate is the test’s most robust harm; unevenness hurts on top of it, and unlike rate, unevenness is the harm experience can buy off. Is the program inside the businesses you know, or sprawling? Spreading it worsens the rate penalty on average in the test’s data. Do you have the size and the scar tissue? Size bought tolerance for everything; experience bought tolerance only for unevenness, and its direct effect was negative, which should retire the comforting idea that doing deals teaches deal-making by itself. And one question the record insists on before any of these: under which of Table 1’s definitions would your program even count as programmatic, and would it have counted in April 2011, when the same shop, reading the same population, said there was nothing to count?

Where this essay stops: the test’s conditions are 1990s U.S. evidence from seven sectors: they establish that pattern effects exist and which way they ran there, and they predict nothing about your program. The archetype charts, the CEO-level deal-order results and the announcement-window averages cannot refute one another, and this essay has not used one to dismiss another; evidence over anecdote is the standing rule here, and it cuts against convenient debunks as hard as against convenient claims. No recommendation to acquire or to abstain ships with this piece. What ships is the page your next deal deck is missing: the claim, its own shop’s first answer, its own footnotes, and its test: side by side, dated, with every caveat in its authors’ own words.

Where are the empirical boundaries of benchmark verification?

Boundary. The original claim fails its tested yardstick; that does not make every acquisition outcome null. Keep the five evaluation criteria separate and re-test the claim on a current transaction sample.

Evidence base. The analytical frame also draws on these additional sources: Billett and Qian 2008; Fuller et al. 2002; Golubov et al. 2015; Haleblian and Finkelstein 1999; Lev and Gu (2024). The links identify the exact works; they support the mechanisms and boundary conditions discussed here, not every claim in isolation.