Reanalysis of "Competition and Innovation: An Inverted-U Relationship"

1. Focus the report on the three problems that the report actually aims to solve and drop unsubstantiated criticism (e.g., patent counts are commonly used in the economics literature as a proxy for innovation; see Bloom et al., 2020, American Economic Review, and the literature referenced therein). It seems unfair to set out to do 3 analyses to address a subset of issues, and when these yield qualitatively similar conclusions to the original paper, attack the paper on other dimensions in the conclusion (e.g., measurement issues).
2. Find a different way to address the concern of using Poisson for non-count data
3. Provide more information on the multilevel model used and the choices underlying the hinge model; in particular explain why the hinge model is preferable to a fully flexible non-parametric specification.

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The target article DOI should refer to the published version of the article, 10.1093/qje/120.2.701, rather than its NBER working paper.

You raise concerns about the lag specification, but do not run any robustness checks on the lag order. Please do so.

It is natural that quantitative analyses of diffuse concepts such as innovation and competitiveness need to be measured with quantifiable proxies, and no better alternative measures are proposed. Patents are an extremely common innovation measure, and citation-weighted patents are a refinement over simple patent counts, which captures the innovative value of each patent. The Lerner index is known to have interpretability issues as a measure of competitiveness (industries can have high profit margins because their market is uncompetitive or precisely because its firms competitively seek cost and revenue edges over their competitors; see Elzinga & Mills 2011, doi:10.1257/aer.101.3.558), but you propose no alternative. If you want to examine whether the specific parameterizations of innovation and competition matter, then propose alternative measures and re-run the analyses on those. E.g., you could replace the Lerner index with a Herfindahl-Hirschman index and reanalyze the relationship (though if you do so, please address the original author's comments on pg. 704).

Poisson quasi-maximum likelihood models are often used on non-count data. They also have useful properties, allowing for asymptotically consistent estimation of percentage average treatment effects even with zeros in the data (Santos Silva & Tenreyro 2006, doi:10.1162/rest.88.4.641; Chen & Roth 2024, doi:10.1093/qje/qjad054). If you want to justify an alternative model, you either need to (1) justify why another parameter is preferable or (2) show that your alternative model estimates the same parameter.

"The quadratic is a poor fit to data, and the nonparametric curve in Figure 1B looks even worse." Justification for this claim is unclear, especially as the nonparametric curve is not plotted directly onto data points. If you want to say something concrete about the data fit, there should be some quantitative backup. One potential solution here would be to compare the parametric quadratic and spline fits with a simple binscatter to assess how these models compare with more descriptive nonparametric fits of the data (see Cattaneo et al. 2024, doi:10.1257/aer.20221576).

It is well-documented that log(Z + 1) specifications produce scale-variant estimates which misidentify interpretable parameters (Aihounton & Henningsen 2021, doi:10.1093/ectj/utaa032; Cohn, Liu, & Wardlaw 2022, doi:10.1016/j.jfineco.2022.08.004; Chen & Roth 2024). This issue also effects your hinge specifications, for which the primary coefficient of interest is on a log(Z + c) variable (where both the Z and c are rescaled by user-specified features, namely xdiff and delta, which do not have any clear data-driven justification). These are not reasonable robustness checks for (quasi-)Poisson regression, as log(Z + 1) specifications have almost universally worse properties. If you want to run robustness checks, you should find alternative models that can capture the sort of percentage ATE estimates Poisson provides with zeros in the data; see Chen & Roth (2024) and Thakral & To (2025, https://neilthakral.github.io/files/papers/transformations.pdf) for recommendations.

The report makes reference to a U-shaped criterion of b_1 < 0 < b_1 for the hinge models; please revise (of course, this point is immaterial if the hinge models are removed).

Using multilevel models rather than fixed effects models does not seem to be an improvement in methods. The reason you specify fixed effects over random effects is because you are concerned about the potential bias that arises when group effects are correlated with predictors of interest. You raise this point yourself in your accompanying blog post:
"In general when fitting a multilevel model, it’s a good idea to adjust for the group-level mean of the predictor–in this case, the average value of x within each industry. Otherwise you have to worry about correlations between x and the varying intercepts. In this case, adding this group-level predictor doesn’t change much. I won’t share the result here just because I’ve already done a lot of work to write this up and there are enough other concerns with the analysis, but, yeah, it’s a good idea to include this predictor too."
This is effectively handled by fixed effects models. To switch these out for random effects multilevel models unnecessarily opens bias pathways.

Reanalyses of influential work are useful and necessary. But meaningful robustness checks must arise from specifications with equivalent or better credibility than those in the original paper. I would be open to reviewing a new version of the manuscript whose robustness checks rise to this standard.

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