How Do We Know? The Counterfactual Behind the Patent Effect
For PIPE applicants, the key evidence question is not whether recipients patented more after receiving money. That raw comparison would mix the effect of funding with whatever already distinguished funded and non-funded firms. The more useful question is whether the study’s design creates a credible estimate of what funded applicants would have experienced without the grant, and what that estimate can—and cannot—say before grant size enters the picture.
The comparison is designed before the result
The study’s control group is made up of firms that applied to the same PIPE calls as funded firms but were not selected. This choice matters because an applicant has already crossed several thresholds that a non-applicant has not. They have decided to seek public R&D support, prepared a proposal, and entered an evaluation process under the same broad rules. A firm that never applied might have had less interest in research, less information about the program, a different project, or no expectation of meeting the eligibility conditions. Comparing that firm with a recipient would make the grant carry the weight of all those differences.
Same-call applicants provide a narrower counterfactual frame. The calls give applicants a common institutional environment: the broad eligibility rules, information conditions, evaluation criteria, and budget constraints are shared. Within that frame, some eligible proposals are funded and others are not. The non-funded applicant therefore helps answer a specific question: how did an applicant’s later patenting differ from the path of a comparable applicant who did not receive PIPE support?
This is a stronger comparison than a simple winner-versus-everyone-else design, but it is not a guarantee of identical firms. Selection is based on technical merit and project feasibility. The study’s available pre-treatment records may not capture every feature that evaluators saw in a proposal, such as the precise quality of the research idea or the team’s unrecorded expertise. If those features influence both the funding decision and later patenting, a residual selection concern remains. The same-call design narrows the problem; it does not make the problem disappear.
The distinction between a level comparison and a change comparison is useful here. Imagine that recipients have a higher patent count in the year of selection. That difference could reflect a stronger pre-existing innovation trajectory, not the grant. If both groups then gain the same amount, recipients would still have more patents but the grant would not explain the gap. Conversely, if their levels begin close together but recipients’ outcomes rise faster after funding, the change in the gap is more informative. Difference-in-Differences formalizes that second comparison while still relying on the idea that, absent the grant, the groups would have continued on sufficiently comparable paths.
The analysis addresses that concern in several connected ways. It excludes proposals deemed ex ante ineligible and observations without the pre-treatment covariates needed for comparison. It uses information measured before treatment—firm size, industry, region, and year—rather than variables that may have been changed by the grant. Those characteristics do not explain the entire innovation process. They help place applicants on a common baseline so that the post-treatment difference is less likely to be a simple reflection of observable starting conditions.
The study then combines propensity-score weighting or matching with a Difference-in-Differences estimator. The first part uses observed pre-treatment characteristics to give greater comparison weight to non-funded applicants who resemble funded firms on those characteristics. The second part asks how outcomes change over time for the funded group relative to the change for the comparison group. This is different from comparing their patent levels at one point. If funded applicants already had more patents before the decision, a level difference alone could be misleading. Difference-in-Differences focuses on the divergence in trajectories after the funding event.
The “doubly robust” label describes the estimator’s use of two complementary components: a treatment model for the weighting and an outcome model for the change in patents. In practical terms, the design does not ask one statistical adjustment to carry the entire burden. It uses the observed probability of entering the funded state and a model of outcomes together, while also including firm and time fixed effects. The paper reports that covariate balance improves substantially after weighting, with standardized mean differences below conventional thresholds. That improvement is evidence that the reweighted groups look more alike on the measured characteristics; it is not evidence that the weighting has balanced characteristics that were never recorded. A statistical adjustment can only work on the information supplied to it. The distinction is especially important when a proposal’s technical merit or a research team’s practical competence is only partly visible in the administrative data.
Fixed effects perform a different job from matching. Matching and weighting reshape the comparison using observed pre-treatment characteristics. Firm effects use repeated observations to account for stable differences that may be present across the panel, while time effects account for changes shared across firms in a given period. These tools operate at different parts of the problem, but they should not be counted as independent proof. If the missing selection factor varies over time or is tied to the project itself, fixed effects may not remove it.
The design also avoids a tempting but dangerous shortcut: controlling for everything that happens after the grant. Employment, spending, team composition, and organizational behavior may be pathways through which funding produces innovation. Treating them as ordinary baseline controls could obscure part of the effect. Restricting the main adjustment to lagged, pre-treatment information keeps the timing of the causal question intact. Firm effects account for stable differences across firms that are captured by the panel structure, while time effects account for changes shared across years. Industry, region, and size information further locates firms within the comparison. None of these devices observes every project-level difference. They make the comparison more disciplined under the study’s assumptions; they do not turn observational program data into a randomized experiment.
The most important identifying assumption is therefore conditional. For the dose–response part of the analysis, grant intensity must be independent of potential outcomes once the relevant pre-treatment characteristics are taken into account. Put plainly, after the design has accounted for what it can observe before treatment, the remaining reason one funded firm received a larger award rather than a smaller one cannot also be an unmeasured reason that determines its later patenting. The program’s rules make that assumption more plausible because prior patent history is not part of the evaluation score and project selection is based on technical merit and feasibility. But plausibility is not proof. Nor is the dose assumption identical to the parallel-trends assumption. Similar pre-treatment patent trajectories help with the funded-versus-non-funded comparison; they do not, by themselves, show that the amount assigned among funded projects was unrelated to unobserved future patenting potential. The average effect and the dose curve therefore rest on related but distinct credibility questions.
The study’s use of lagged covariates is also consequential. A grant can change employment, spending, or organizational behavior. If those post-treatment variables were used as if they were pre-existing controls, the adjustment could remove part of the effect being estimated or create a new bias. By relying on characteristics measured before treatment and allowing time for innovation to emerge, the design keeps the comparison closer to the question it intends to answer: what did funding change relative to the applicants’ prior position?
The diagram separates three ideas that are often collapsed. The common call creates the comparison frame. The pre-treatment trajectory check examines whether the groups were already moving differently before funding. The post-treatment outcome supplies the difference that the estimator summarizes. A successful rendering of this logic does not prove causality; it simply makes clear where the assumptions enter.
What the average effect says—and when it arrives
Against this comparison, the baseline estimate is positive. Three years after the grant, beneficiary SMEs register an average increase of 0.155 patents relative to matched non-funded applicants. The reported standard error is 0.050, and the estimate is statistically significant at the 1% level. In the descriptive data, the control group’s mean is 0.016 patents, so the estimated additionality is large relative to that baseline even though the absolute number of patents remains modest. The standard error matters alongside the estimate: 0.050 indicates that the study is not presenting 0.155 as a number known without sampling uncertainty. Statistical significance makes the estimate less compatible with a zero difference under the model’s assumptions; it does not measure the social value of a patent, guarantee that the effect will recur in another program, or settle the grant-size question.
The comparison base should stay attached to the number. The estimate is not “each recipient produced 0.155 patents.” It is an average difference in the study’s patent measure across the matched applicant sample. Some firms may have produced no additional patent, some may have produced more, and fractional counting means the outcome can summarize partial firm contributions rather than only whole patent events. The estimate describes the mean result under the study’s design; it is not an individual forecast.
The result is also specific to the measured outcome. The study uses firm-level fractional patent applications, not a complete index of innovation. It does not establish that the same grant increased sales, productivity, employment, patent quality, or total social value by the same amount. A patent is evidence that a particular kind of technological output was additional relative to the comparison, not a complete accounting of the return on public money.
Alternative specifications strengthen the average finding without making it universal. The estimate is 0.097 in a selected-industry sample, 0.149 when patents and utility models are used as the outcome, and 0.105 when observations with the top 1% of patents are excluded. The estimates remain positive, although statistical significance varies. This pattern makes it less likely that the baseline result is driven solely by one narrow sample choice or a few very high patent holders. It does not remove the measurement boundary or identify the mechanism that produced the difference.
The event-study evidence adds a temporal test. Before treatment, the estimated coefficients are statistically indistinguishable from zero. That supports the view that funded and non-funded applicants followed similar innovation trajectories before the funding decision, at least in the measured pre-treatment period. It is not evidence that the firms were identical in every unobserved respect. A pre-trend test can show that the available outcome histories do not reveal differential movement; it cannot show that no hidden difference exists.
After the decision, the estimated effect does not appear as an immediate jump. Effects emerge gradually and become statistically significant from the second year onward. The paper describes the difference as stabilizing between roughly 0.15 and 0.25 additional patents after four years. The main outcome window remains three years after the grant, while the longer horizon helps show that the timing is consistent with an R&D process whose results take time to become observable.
This lag changes how a program should be evaluated. A grant may be paid at the beginning of a project, but the relevant output can require recruitment, experimentation, technical development, testing, and preparation of an application. The dataset does not allow every one of those steps to be separately measured, but the timing pattern warns against treating the first months after a grant as a complete performance verdict. An evaluation conducted too early could mistake “not yet visible in patents” for “no innovation effect.” That is an absence-of-evidence problem, not evidence that no research activity occurred.
The estimate also carries selection risk in a way that matters for interpretation. PIPE applicants chose to enter the program, and funding decisions reflect project evaluation. The study’s same-call comparison and pre-treatment adjustments make the resulting estimate more credible than a raw cross-sectional difference, but the interpretation still depends on the conditional independence assumption. New evidence could change the conclusion if, for example, detailed proposal-quality measures showed that larger awards went systematically to projects with greater unobserved patent potential, or if a different credible design produced a materially different effect.
At this stage, the evidence supports a careful statement: within the PIPE applicant setting, receiving a grant is associated with additional patenting over a multi-year horizon, and the event-study pattern is consistent with comparable pre-treatment trajectories followed by gradual post-treatment divergence. It does not yet support the stronger statement that every grant amount works equally well. The 0.155 average combines recipients who received different doses and firms with different capacities to deploy them.
That is why the average effect is a starting point rather than the final allocation answer. An average tells us that the funded state improved the measured outcome in this setting. It does not tell us whether moving from a smaller award to a larger one produces a proportionate gain, whether the next dollar is more valuable at the lower or middle end of the distribution, or whether a high award is being used efficiently. Those are questions about treatment intensity, and they require a different lens from the one used to estimate the average recipient effect.
The next step is therefore not to abandon the positive result but to disaggregate it. The same PIPE data that support the funded-versus-non-funded comparison also contain variation in grant amounts. Reading that variation will reveal whether the average effect conceals a rising, flattening, or declining response as the dose changes.