How to Tell a Deal Effect from a Selection Effect
The subject here is the measured effect of acquiring an innovative start-up: did the deal change what the target and its parent did, or did the target merely look different because it was the kind of firm an acquiror would choose? This chapter explains the outcomes and counterfactuals used to answer that question. The practical value is simple but important: a large before-and-after decline is suggestive, while a decline relative to a credible comparison is evidence about the acquisition itself.
The outcomes are windows onto innovation, not innovation itself
A start-up’s innovation is not a single observable number. Research can produce a patent, a secret process, a product improvement, a scientific capability, or an idea that another team later develops. The OECD study therefore uses several measures, each with a different meaning, and the BSE study adds a separate implementation proxy. Reading them correctly is the first safeguard against both exaggerating and minimizing the effect of an acquisition.
The broadest OECD measure is the annual flow of DOCDB patent families. A patent family groups applications in different offices that cover the same invention, using the earliest filing date as the invention’s starting point. The study standardises yearly filing counts by patent authority, technology class, and year before aggregating them at the firm level. That adjustment matters because a raw count would mix differences in patenting traditions, technological fields, countries, and time with differences in inventive activity. The result is a comparable trajectory: whether a target’s measured flow rises or falls relative to the innovation environment around it.
The same information can be viewed as a stock. A stock summarises a firm’s accumulated inventive history, with older inventions depreciated over time. It is useful for describing whether a target or acquiror entered a deal with an established technical base. It is less suitable for detecting a sudden post-deal change, because a large pre-existing portfolio can remain in place even if new work stops. That is why a post-acquisition analysis focuses heavily on flows rather than only on the number of patents a firm owns.
Citation-weighted patenting adds a quality or influence dimension. The OECD weights inventions by the citations they receive during the first five years, excluding self-citations, and then standardises the result. A newly filed patent that later receives attention from other patents contributes differently from one that receives none. The measure is still indirect. Citations can reflect field conventions, examination practices, and the visibility of an invention rather than its social or commercial value. Some citations are supplied by examiners, especially in the European system, which limits the extent to which the acquiring firm can directly manipulate them. Even so, citations are best read as evidence about subsequent technological influence, not as a universal score for an idea.
Radicalness asks a different question. It measures the share of technological classes cited by a patent that are not classes in which the patent itself is classified. In effect, it captures whether an invention recombines existing knowledge in a way that reaches into a different technological field. A fall in radicalness among the patents that continue to be filed would suggest a shift toward less far-reaching work, but a stable radicalness measure would not prove that innovation is healthy. A start-up can stop filing altogether, or produce valuable non-patented work, without changing the radicalness of its remaining portfolio.
The study also uses trademarks and total factor productivity as supporting indicators. Trademarks can signal movement toward market entry, while productivity is intended to capture how efficiently a firm turns inputs into output. They are not substitutes for patent data. Trademark registration depends on an intellectual-property office and sectoral practices, and the productivity estimates require balance-sheet information available only for a restricted group of firms. These measures can test whether the post-deal story looks like a shift into commercialisation or operational integration, but they cannot identify that shift on their own.
The BSE paper uses future citations to patents held by the start-up before acquisition as a proxy for implementation. If other patents cite an old start-up patent more after the deal, the authors interpret that increase as evidence that the idea was developed or used. A decrease is interpreted as evidence that it was shelved. To reduce the risk that acquired patents were unusual before the deal, each is matched to similar control patents on application year, technology class, number of inventors, the firm’s state and founding year, and a measure of textual similarity to previous work. This is a careful way to compare like with like, but the outcome remains a proxy: more citations can indicate diffusion, while no additional citations do not prove that an idea was abandoned.
These distinctions explain why a measured decline must be stated precisely. “The target filed fewer patents” is a claim about an observable flow. “The target innovated less” is a broader interpretation that becomes more credible when patent quality, trademarks, productivity, or implementation measures move in the same direction. “The acquiror killed the idea” is a claim about motive and intent that requires still different evidence.
The counterfactual is built in stages
The basic problem is selection. Suppose acquired start-ups were already closer to commercialisation than other young firms. Their patenting might have fallen even without an acquisition because the research phase was ending. Or suppose acquirors chose firms with unusually strong technologies that were entering a natural period of transition. A simple comparison of each target with itself before and after the deal would attribute every subsequent change to ownership, including changes that were already on the way.
Difference-in-differences addresses this problem by comparing changes, not levels. Researchers first observe how the treated target’s outcome changes from a pre-deal period to a post-deal period. They then compare that change with the change for a control group. The acquisition effect is the extra movement in the target relative to the control. The key assumption is parallel trends: in the absence of acquisition, the two groups would have continued to evolve in sufficiently similar ways.
A simple example shows what this comparison does and does not accomplish. Imagine that patenting falls by two units for an acquired target and by one unit for a comparable firm during the same period. The relevant difference is not the target’s two-unit fall; it is the additional one-unit fall relative to the comparison. If both firms were already moving apart before the deal, the extra fall cannot safely be assigned to acquisition. Conversely, similar pre-event movement does not prove that every unobserved factor is balanced. It makes the counterfactual more credible, not certain.
Event-study estimates make this reasoning visible across time. The year before the announcement is used as a reference point, and each later coefficient describes how the gap between treated and comparison firms changes relative to that point. Pre-event coefficients are a diagnostic for whether the groups were already diverging; post-event coefficients show when the extra movement appears and whether it persists. The estimates are often standardised by an unconditional average flow, so a statement such as “one and a half times the average flow” describes a relative scale, not a literal claim that every target lost one and a half patents. Keeping the unit of the coefficient attached to the claim prevents a visually dramatic event-study line from being mistaken for a raw count.
The choice of control group is consequential. The OECD’s main design uses start-ups that will be acquired later but have not yet been acquired as controls. These firms are more comparable to eventual targets than firms that are never acquired, because they have demonstrated enough relevance to enter the acquisition market at some point. As each acquisition occurs in a different year, the method must handle staggered treatment. It also allows the effect to vary across firms and over time rather than forcing every acquisition to have the same impact.
A not-yet-acquired firm is a useful control only while it remains untreated for the comparison being made. Once its own acquisition occurs, it can no longer stand in for an untreated trajectory at later event times. This is one reason conventional two-way fixed-effects averages can be misleading: an early-treated firm may be compared with a later-treated firm, and a less-exposed acquiror with a more-exposed one, even though treatment is already changing the comparison. The OECD’s chosen estimator is designed for this staggered and heterogeneous setting. The method does not eliminate the need for judgment; it prevents a particular kind of timing mistake from being hidden inside one average coefficient.
The design includes firm fixed effects, which remove stable differences between firms, and industry–country-specific trends, which absorb broad changes shared by firms in the same economic setting. It uses the announcement date rather than only the legal completion date. That choice recognises anticipation: founders, researchers, and managers may change behaviour as soon as a deal becomes public or credible. If filings fall between announcement and completion, assigning treatment only at completion would place part of the effect in the wrong period.
The parent is harder to analyse than the target. A start-up is generally treated once, but an established acquiror can buy several start-ups, sometimes in the same period. The OECD therefore represents the parent’s treatment as cumulative acquisition intensity and compares firms exposed to different numbers of acquisitions. It also controls for acquisitions of non-start-ups and uses a burn-in period to reduce contamination from deals that occurred before the observed data. The resulting estimate asks whether greater exposure to start-up acquisition is followed by a different innovation trajectory; it is not a simplistic one-deal experiment for every incumbent.
The OECD adds a stronger counterfactual using withdrawn bids. Some start-ups received an acquisition offer that did not close. A failed bid is useful only if its failure was unrelated to the target’s innovation. If a buyer withdrew because the technology deteriorated, the failed target would not represent what would have happened to a successful target without acquisition. The study therefore surveys the reasons for withdrawal. From 457 withdrawn bids, it retains 122 linked to competing bids that did not lead to another acquisition, adverse macroeconomic conditions, or regulatory objections. It excludes cases involving valuation disputes, disagreements about growth strategy or ownership, negative developments involving a party, and unclear reasons because those events could be related to innovation prospects.
The comparison then has three relevant paths. A successful target is observed before and after acquisition. A target whose bid was exogenously withdrawn is observed before and after withdrawal. Both are compared with never-acquired firms in the same country–industry settings. The difference between the successful-target change and the withdrawn-target change is a triple difference: it asks whether completion, rather than merely receiving an acquisition bid, is associated with the additional post-event decline.
The withdrawn-bid strategy is not a magic word that removes every concern. Its causal interpretation depends on the classification of reasons and on the assumption that the retained withdrawals are unrelated to unobserved innovation changes. The retained sample spans only 14 countries and 46 industries, and it is much smaller than the full population. Similar pre-event patent flows and observable characteristics support the comparison, but they cannot demonstrate equality on every unmeasured dimension. The design strengthens the inference about a target outcome; it does not reveal the acquiror’s intention.
The BSE study’s patent-level matching makes a related point from a different angle. It finds no statistically significant average effect of acquisition on citations to pre-existing startup patents, then finds a positive effect for unrelated acquisitions and a negative effect for related acquisitions. That result is not a contradiction of a target-patenting decline in another study. One analysis follows the target firm’s new patent flow across a global sample; the other uses US patent citations to estimate whether old ideas are implemented. Different estimands can reveal different parts of the same transaction.
The limits of the proxies remain active even after the counterfactual improves. If the target moves research into secrecy, patents may fall while invention continues. If the parent incorporates an idea into a product without assigning new patents to the target, the target measure can fall while some value is realised elsewhere. If integration consumes researchers’ time, the decline may be real but temporary. If a project is shelved because it threatens an existing product, the measured decline may be both an outcome and a clue about motive. Patent, citation, trademark, and productivity evidence can narrow these possibilities, but none alone can close them.
The purpose of careful identification is therefore not to manufacture certainty. It is to separate the questions. Selection methods tell us which firms entered the deal. Difference-in-differences asks how their trajectory changed relative to a plausible counterfactual. Withdrawn bids make that counterfactual more demanding. Multiple outcomes test whether the result is confined to filing behaviour. Only after those distinctions are in place can the post-deal innovation ledger be read: what happened to the target, what happened to the parent, and what remains unexplained.