Productivity, Place, and Plants

THE sources and consequences of spatial differences in productivity are a frequent focus in urban economics, starting with the state-level analysis of Ciccone and Hall (1996). Spatial differences in productivity contribute to regional dispersion in wages and employment (Caliendo et al., 2018; Hornbeck & Moretti, 2018), and drive location choices of plants (Ellison et al., 2010; Gaubert, 2018) and of people and hence the city size distribution (Desmet & Rossi-Hansberg, 2013). These differences are also testable implications of core urban economics models (e.g., Gaubert, 2018; Davis & Dingel, 2020). Furthermore, these differences motivate studies of spatial misallocation and the design of spatial policies (Moretti, 2012; Boeri et al., 2019; Fajgelbaum et al., 2019; Hsieh & Moretti, 2019; Fajgelbaum & Gaubert, 2020).

Our paper revisits a central—but untested—assumption in these literatures: that measured spatial productivity differences reflect systematic differences between places, such as from agglomeration forces, sorting, or exogenous productivity shifters. Instead, we permit, and quantify, the role of spurious productivity differences, unrelated to systematic sources. We are motivated by two facts. First, there is substantial heterogeneity in productivity across individual plants (Syverson, 2004, 2011), dominant even within narrowly defined industries (Cunningham et al., 2020). Second, there are often few plants per industry in a location. For instance, in the United States, among the 118 locations with some auto manufacturing, the median plant count is two (and the mean is just 2.4); Detroit, which has the highest number of plants and employment total, has just 22 plants, with at least 87% of their employment concentrated in the largest six (source: County Business Patterns, NAICS 3361, Metropolitan Statistical Areas, for 2012, our reference year in the rest of the paper). As a result, the average productivity of a finite sample of plants conflates idiosyncratic heterogeneity with systematic productivity differences. We call this spurious source of productivity differences “granularity bias,” as individual plants’ productivities do not wash out in the calculation of local averages.

The share of measured productivity differences that reflects granularity bias rather than systematic differences has important implications. At one extreme—with only systematic differences across place and no role for plant idiosyncracies—labor and capital moving across locations should be expected to fully inherit the productivity of existing plants. This view guides existing spatial modeling, counterfactual analyses, and assessments of spatial misallocation of resources—both its policy sources and remedies. At the other extreme, measured productivity differences would reflect simply the “luck of the draw” of idiosyncratically heterogeneous plants—with no role for place. In this case, counterfactual reallocation of resources would not inherit existing measured productivity, and there is no point in tracing measured differences to deep causes.¹

Our task amounts to stripping out the potentially large, spurious contribution of idiosyncratic, granular plants from place-level average productivities, and thereby isolating the dispersion of true place effects, which capture systematic differences only. We define a true place effect as the expected productivity of a randomly drawn plant from a potentially place-specific distribution. This statistical definition of place effects is agnostic to their sources, encompassing exogenous or endogenous causal effects, sorting—the economic sources that are the object of much research in urban economics—and even spatially correlated mismeasurement. In our framework, true place effects stand in contrast to raw averages of productivity of finite populations of plants, which are draws from the latent productivity distribution of each location’s infinite superpopulation of plants.

In the data, we find that granularity bias accounts for two-thirds to four-fifths of the spatial raw differences in productivity. We reach this conclusion in several steps. We start by documenting large dispersion in the raw variance of average productivity across U.S. cities (metropolitan statistical areas, MSAs) demeaned within the national 4-digit industry (which nets out mechanical productivity differences working through industry composition). Our main measure of plant-level productivity is log of revenue total factor productivity (TFPr), although we also study log value added per worker and log revenue per worker. Our headline number of the raw variance of average-based location effects is 0.026—the dissection of which is the focus of the paper. That is, a city one standard deviation above the mean has about a 16 log points (17%) higher average productivity. Manufacturing plants in the top 10% most productive MSAs are on average 48 log points (61%) more productive than plants in the bottom 10%. While MSA-level results involve averages across many plants (the average plant count per MSA is around 300 in our sample), we also construct finer industry-specific location effects, which exhibit four times the variance, at 0.110.²

We then assess the scope of, and ultimately strip out, granularity bias in three complementary strategies. First, we provide a nonparametric permutation test, calculating the probability that the observed level of spatial dispersion would emerge if plant-level productivity were independent of place. We simulate 1,000 U.S. economies that randomly reassign the empirical plants across MSAs, so that by construction, all place effects reflect granularity only.³ The resulting average simulated variance is high, but less than the empirical one, making clear that granularity can generate substantial spurious variation. Yet, the empirical U.S. economy falls into the top of those sampling distributions, and hence does exhibit a statistically significant degree of dispersion in true place effects.

Second, we constructively estimate the bias-corrected variance of true place effects. We employ a split-sample approach. In every MSA-industry cell, we randomly split plants into two equally sized groups. We then estimate average-based place effects for each of the two resulting economies. The covariance between the average-based place effects of these paired cities is an unbiased estimator of the variance of the true place effects, which, by definition, are the common components of both split samples. This bias-correction shrinks the variance substantially, from 0.110 to 0.023 for the industry-specific location effects (by more than three-quarters), and even for the MSA-level location effects, from 0.026 to 0.008 (by more than two-thirds). In sum, when identifying the variance of true place effects, places are much more similar than the raw variance of average productivity levels suggests, and the majority of spatial differences in realized productivity largely reflect the luck of the draw from highly dispersed plant distributions.

Third, we assess the role of three sources of granularity bias: idiosyncratic plant-level heterogeneity in productivity, finite plant counts, and plant size (as our baseline specification weights by plant employment). To assess the role of idiosyncratic variance, we remove outliers by winsorizing plant-level TFP by 0% and 2.5% rather than our baseline of 1%, and find similar results. To gauge the role of large, influential plants, we also provide unweighted results, which imply smaller raw variances that nonetheless continue to overstate the variance of true place effects considerably. To trace the role of finite plant counts, we raise the minimum plant count for each location-industry cell incrementally from two (our baseline) to 150. The raw and bias-adjusted variance fall in tandem. As we select larger, more similar places, we also reduce the true variance of the sample, throwing the baby out with the bath water.

Our paper contains three additional extensions. First, we zoom in on the dispersion in place effects for new plants. Raw productivity averages of new plants are more dispersed across places than those of old, existing plants, but true place effects are similarly dispersed, such that granularity bias is even more pronounced for new plants. This split of our sample into new and incumbent plants also crystallizes a specific facet of granularity bias (and makes tangible the draws of new plants from the distribution of a location’s superpopulation): new plants’ productivity has only a very loose link to that of incumbent plants, inheriting only about 12% of their average productivity. This loose link highlights the fact that naive extrapolations, such as place-based policies or entry and location decisions of businesses hoping to replicate prevailing successes one to one, would succumb to a gambler’s fallacy by ignoring the granularity bias we document. Second, we show robustness to studying log value added per worker (labor productivity) and revenue per worker in the manufacturing sector, as well as broadening this analysis to industries beyond manufacturing to all tradable industries. Third, we show that the role of granularity bias extends to the within-country regional dispersion of 15 European countries, drawing on Bureau van Dijk firm-level data.

Our findings raise several implications. Most basically, our paper highlights a new, quantitatively dominant source of productivity differences across places: the luck of the draw. This large role for granularity diminishes the share of productivity differences attributable to systematic sources, which have been the focus of the literature we cited in the beginning of our introduction.⁴ Furthermore, our findings have implications for quantitative urban models. A long literature has estimated local productivity shifters on the basis of quantitative models that are calibrated to exactly match raw productivity differences (directly or indirectly). These models attribute all productivity differences to be of the systematic kind and hence hold those productivity factors fixed across general-equilibrium counterfactuals (e.g., Desmet & Rossi-Hansberg, 2013; Allen & Arkolakis, 2014; Hsieh & Moretti, 2019). Our findings suggest that the counterfactual reallocation of inputs across places differentiated by average productivity would have muted effects when accounting for granularity, unless inputs are only absorbed proportionately by existing plants (which drive the observed raw productivity), with particularly large attenuation at the entry margin. Our results suggest analogous implications for analyses of spatial misallocation and place-based policies, which risk conflating misallocation across plants (Hsieh & Klenow, 2009) with misallocation across space (Hsieh & Moretti, 2019). To our knowledge, no currently employed spatial model can capture the role of granularity, the development of which our descriptive empirical paper leaves for future work.⁵

Section II defines the conceptual and statistical framework of our analysis. Section III presents the data, and the sample and variable construction. Section IV presents the main results, covering the United States, TFP, and all plants in a place. Section V presents the analysis of new plants. Section VI presents the results for labor productivity, revenue per worker, and the broader set of industries beyond manufacturing. Section VII presents the analysis for 15 European countries.

We start by defining true place effects, then clarify the pitfalls of estimating the dispersion of place effects, and present our strategies to overcome these measurement challenges.

We formulate a statistical definition of true place effects of productivity—the expected value of productivity of a randomly drawn plant from a potentially place-specific distribution—and we clarify how those relate to measured raw averages of finite counts of idiosyncratically heterogeneous plants.

The economy is characterized by a set $L$ of count $NL$ locations indexed by $l∈L$⁠. Each location has a count of $NPl$ plants, which are indexed by $p∈Pl$⁠, where $Pl$ denotes the population of location-$l$ plants; we will also consider subsets $Sl⊆Pl$ of size $NSl$⁠.

Plant $p$ in location $l$ has log total factor productivity $apl=lnApl$—but our derivations below would also apply to, for example, average labor productivity and alternative productivity concepts. In fact, while we refer to $apl$ as plant productivity, we also leave open the possibility that it also reflects mismeasurement.

Plants are heterogeneous in productivity in ways that potentially depend on their location $l$⁠. We agnostically describe this property in the statistical form of a latent data-generating process $a∼Fla(a)$⁠, of plant-level productivity in a location $l$⁠.

Importantly, this latent data-generating process does not describe the given finite population of existing plants (as in the real economy, or our census data). In statistical terms, $Fla(a)$ describes the location’s infinite superpopulation of plants, from which the finite observed population is drawn. The draws from $Fla(a)$ give the plans that would, if drawn, be active (unlike the potential-entrants distribution that include nonviable plants as in plant selection models such as in Melitz, 2003), and hence the distribution may reflect a host of underlying economic forces—for example, selection on entry and exit, and sorting.

In addition, a plant is characterized by size $ep$ (e.g., employment); the exposition below starts with unweighted (or equally sized) plants within locations, and no weighting across locations. We discuss the extension to weighting and heterogeneity in size in section IIF.

Our goal is to characterize the dispersion of true place effects $τl$ across locations $l∈L$⁠. We now contrast the true place effect defined in equation (1) with the average productivity level of a finite set of plants in a place.

However, even the population average defined in equation (4) generally differs from our object of interest, namely the expected value $E[apl|l]$ defined in equation (1). That expectation is taken over the latent data-generating process $Fla(a)$ of plant productivities, from which the real economy and the census data draw a finite set of plants. We next discuss the pitfalls of estimating the true place effects on the basis of average productivities taken over finite sets of plants, and then our identification strategy stripping out the associated measurement error, which we characterize as granularity bias below.

While each place effect $τ^l$ is estimated without bias, dispersion measures based on averages $τ^l$ are upward-biased estimates of the dispersion of true place effects $τl$⁠, for reasons we jointly label as “granularity.” We formalize this bias with the example of our leading dispersion statistic, namely the variance.

In the second line, the first term is the variance of true place effects. The second term is a term that biases upward the raw variance of productivity averages as an estimate of the variance of true place effects due to the granular nature of plants in places. We call this term “granularity bias,” and we characterize it below.

While the variance of the place averages $τ^l$ is a consistent estimator of the variance of true place effects $τl$⁠, with finite populations of plants within locations it is biased upward by the second term in the second line of equation (6): the weighted average of within-location variances divided by location count of plants. This term reflects ”granularity” in the sense that a given plant need not wash out in the average. It arises under finite cell counts of plants $Nl$ combined with large idiosyncratic variance $σl(u)2$ within a cell $l$⁠, so it is present even when $Sl=Pl$ as the populations of existing plants are finite. Intuitively, these factors generate realized deviations of sample averages from expected values $τl$⁠, raising the observed variance of place averages above the variance of true place effects. Below we dissect each source of granularity and discuss the potential empirical relevance of each.

First, to gauge the empirical range of cell sizes (plant counts) $Nl$⁠, we plot the CDF of cell sizes from public-use data on manufacturing plants in the U.S. County Business Patterns in appendix figure A1. Panel a plots the CDF of plant counts for cells defined as MSAs (pooling all industries); Panel b does so for MSA-industry cells, at the level of the 86 4-digit NAICS manufacturing industries. While small cells are an obvious issue in measuring variance across location-industries, for which 60% have fewer than 5 plants, there are more plant observations at the MSA level when pooling all industries. Our empirical implementation will exclude varying degrees of small cells.

Second, equation (6) clarifies that even for larger $Nl$⁠, granularity bias can be large if plants exhibit large idiosyncratic variance in at least some locations. In the national data, within-industry dispersion of productivity across manufacturing plants is indeed tremendous. Cunningham et al. (2020) report standard deviations of 0.460 and 0.684 for log TFP and log labor productivity (revenue per hour worked), respectively, covering 1997–2016 and the U.S. manufacturing sector, using U.S. Census data similar to ours, and studying 4-digit NAICS industries (with equal weights across industries and years). The 90th percentile of plants in a 4-digit NAICS industry are, nationally, 193% (1.078 in logs) or 490% (1.773 in logs) more productive than the 10th percentile, for TFP and labor productivity, respectively.⁶ Syverson (2004) reports similar statistics for an earlier period.

A third source of granularity arises in the common specification in which plants are weighted by size, such as employment, as we will do in our empirical implementation [although our theoretical exposition above is written in terms of unweighted (or equally sized) plants]. Then, large plants can dominate plant averages. (We additionally discuss weighting in section IIF.) In appendix figure A2, we present Lorenz curves and Gini coefficients of employment-plant concentration at the MSA and MSA-industry (4-digit NAICS) cells. We do so for the p10, p25, p50, p75, and p90 of cells in terms of their Gini coefficient. We drop MSAs and MSA-industry cells with fewer than ten plants, which zooms into the cells least likely to be subject to granularity bias (and for the Lorenz curve to have a clear interpretation). This restriction does not bind when we define cells as MSAs. Again we draw on public-use CBP data, with further details on the construction of the indices contained in the figure note.

In manufacturing, the typical (median) MSA and MSA-industry cell are tremendously concentrated. Pooling all industries, the Gini coefficient for the median MSA is 0.76 and ranges from 0.70 to 0.82 for the 10th and 90th percentile MSAs. In the median MSA, the top 5% of plants employ 46% of manufacturing workers. The top 20% of plants account for 80% of manufacturing employees. For the MSA-industries, where the restriction of at least ten plants drops 75% of cells and hence selects cells least subject to granularity, the median Gini coefficient is 0.63, and the 10th and 90th percentile Gini coefficients are 0.49 and 0.77. In the MSA-industry cell with the median Gini coefficient among even these remaining cells, the top 5% of plants account for 24% of employment, and the top 20% account for 64%. But even in the bottom 10th percentile of the MSAs and MSA-industries in terms of concentration (Gini coefficient), 72% and 44% of employment are accounted for by the largest 20% of plants.

To assess the scope for granularity bias in the data, our first strategy is to consider an extreme benchmark for the distribution of place effects: that all locations $l∈L$ have the same data-generating process for plant productivity $Fla(a)=Fa(a)∀l∈L$⁠. We test a more specific version, namely that all places have the same expected value $τl=τ∀l∈L$⁠, so that the variance of true place effects is zero. Then, dispersion in measured place averages arises solely as an artifact of grouping heterogeneous plants, that is, from granularity bias.

We implement a nonparametric (or randomization), exact test of this hypothesis in the spirit of permutation tests.⁷ We construct the sampling distribution of our test statistic of interest under the following procedure: plants are randomly distributed across space into places. Specifically, we preserve the count of plants in each place (in practice in each location-industry cell). Under this procedure, the rank of a given empirical dispersion static in the CDF of those of the random economies gives the nonparametric $p$-value corresponding to that null hypothesis.

Broadly, by referencing a random-location benchmark, our test of productivity place effects is in the spirit of Ellison & Glaeser (1997), who study whether the observed geographical concentration is statistically different from randomly located plants, Bartelme and Ziv (2020, 2023), who do so focusing on the role of multiplant firms, and Armenter and Koren (2014), who study the distribution of exporters.

Hence, the covariance of averages of randomly chosen subsamples is an unbiased estimator of the variance of the true place effects, eliminating granularity bias. This method is a standard tool in labor economics to remove measurement error (e.g., Gerard et al., 2018; Drenik et al., 2023; Silver, 2020; Kline et al., 2020).

There are two ways in which weighting might enter and affect the above exposition. First, the exposition above does not weight locations differently when constructing the cross-regional variance. That is, the bias term is the unweighted average over all location-specific bias terms. Consistent with this specification, in our empirical implementation, we weight MSAs equally (rather than giving larger MSAs a larger weight).

Second, the expressions above have presented the case in which place effects $τl$ equally weight (or consider equally sized) plants within a location. In practice, we weight plants by plant employment $epl$ when constructing cell-level averages. The true place effect then takes the weighted expectation of productivity over the joint distribution of plant productivity and size, $Fl(a,e)$⁠. The main implication is that the bias from granularity now also encompasses the potential dominance of large plants. Importantly, the covariance remains the unbiased estimator of the variance of true place effects also in the weighted case. (For the permutation tests, we do not reassign plants based on size.) We additionally present specifications without weighting by plant size.

Finally, the above exposition sidesteps industry differences, being written as if only one industry existed. We account for differences between industries in two ways. First, we implement our approach within industries, and we report our results as averages across industries. Second, we define plant productivity as deviation from industry average, and we pool across industries. These measures are presented in section III.

We now describe our empirical implementation of the framework in section II.

Our primary data set is the U.S. Census of Manufactures (CMF), plant-level data on production and plant characteristics for the universe of U.S. manufacturing. We use the most recently available wave, 2012 (but we do not exploit the panel dimension across Censuses or compare our findings to previous Censuses). As our location measure, we use plants’ MSA (dropping plants outside of MSAs). While the data contain 6-digit NAICS industry codes (we use industry definitions from Fort & Klimek, 2018), we will coarsen the definition to 4-digit for most purposes.

The CMF contains information on revenue, employment and payroll (separately for production and nonproduction workers), production worker hours, material and energy expenditures, and capital expenditures. Value added is revenue minus nonlabor/capital inputs. Since we include an extension studying place effects for new and old plants in section V, we also construct plant age as the difference between 2012 and the first time the plant enters the Longitudinal Business Database (LBD), which we merge onto the CMF for this purpose. We use LBD employment when constructing value added per worker (see below) and when weighting plants.

Our sample requires plants to have an industry code, be located in an MSA, and have positive value added as well as TFP, described below, and remove administrative records.

In our primary specifications, we winsorize the final plant-level productivity measures at 1% and 99%. We also probe robustness to no as well as 2.5% levels.

Our primary definition of places are location-industry cells, by MSA and 4-digit NAICS industry. We also probe robustness to 6-digit industry classification. We keep location-industry cells with at least two plants, the minimum number required for our split-sample strategy described in section IIE while maximizing the number of cells. We will probe robustness to varying this cutoff between 2 and 150 plants in section IVD. Our main sample consists of around 120,000 plants in around 11,500 cells. (Plant, MSA, and cell counts must be rounded to meet Census disclosure requirements.) There are 384 U.S. MSAs and 86 4-digit NAICS manufacturing industries.

Since the place effects are demeaned by industry, we can pool all industries’ place effects and report the resulting variances across all industries, corresponding to the average of within-industry variances, as our headline number. Whenever we refer to dispersion statistics or plot distributions of location-industry effects, we do so weighted by the share of the industry in total employment within its respective location, for comparability with the location effects that pool all industries in a location, described below.

Hence, location effects $ξ^l$ can be thought of as the common location component across all industries in a given location, whereas the industry-specific location effects $τ^l,i$ essentially treat location-industries as independent entities with no connection to neighboring industries. When place effects are not perfectly correlated across industries, the dispersion of location-industry effects will be larger than that of location effects.

As a complement, we draw on Bureau van Dijk (BvD) firm-level data covering 15 European countries, again in manufacturing. On a country-by-country basis, we replicate our analysis using NUTS-2 within-country regional divisions, which most closely resemble U.S. MSAs, with each containing between 800,000 and 3 million inhabitants. We construct TFP measures for the manufacturing sector, at the 2-digit NACE industry level (due to the lower number of observations in BvD rather than census data), which gives us 23 industries. We obtain the industry-country-specific labor share by dividing the sum of payroll at the industry level of all sample firms by the corresponding sum of value added for firms with nonmissing observations on both variables. We then construct firm-specific TFP by assuming a Cobb-Douglas production function, and subtracting from log value added labor-share-weighted employment and one-minus-labor-share-weighted log capital. We use fixed tangible assets as the capital stock measure. We winsorize the resulting TFP measures at 1% and 99%. We again keep all location-industry cells with at least 2 firms. Appendix table A2 lists the number of regions, cells, and firm counts in each country.

These data have several drawbacks for our purposes compared to the U.S. plant census. For instance, coverage is imperfect, and data quality varies across countries specifically regarding value added (see, e.g., Gopinath et al., 2017). To maximize coverage and mimic a census, we keep each firm’s most recent observation, implying that most observations come from the late 2010s. The capital stock measure is based on book value of assets. We do not apply industry-specific input price indices (industry fixed effects absorb national output price indices). Since BvD is at the firm rather than plant level, all production units of multiplant firms are assigned to a single industry and headquarter location.

We first measure the raw geographic dispersion in productivity across U.S. cities. We then implement our permutation test of the null hypothesis that this empirical variance is entirely spurious and would arise even if plants were randomly allocated across places. We implement our split-sample strategy to cleanse the dispersion of granularity bias and provide the unbiased estimate of the variance of true place effects. Finally, we run a series of robustness checks dissecting the sources of the granularity bias. Table 1 reports the key numbers cited here. In all of our figures and dispersion statistics, we weight MSAs equally, and MSA-industries by local employment share, as discussed in section IIF.

Figure 1 plots the distribution of average-based productivity place effects for locations, $ξ^l$⁠, and for location-industries, $τ^l,i$⁠. In accordance with Census disclosure requirements, the graphs present kernel densities rather than histograms, censored at the 5th and 95th percentiles. Hence, tails and potential skewness are not depicted (so the mode need not be centered at zero, although we have centered place effects at zero over the full support).

Figure 1 panel a plots the distribution of location-specific effects based on averages, $ξ^l$⁠. The focus of this section is the solid line, representing the raw distribution of average-based place effects. The location effects $ξ^l$ trace out a bell-shaped distribution. (The censoring by the Census disclosure process masks potential skewness.) As printed into figure 1, the variance is 0.026. This statistic is our headline number reported in the introduction in section 1. That is, plants in MSAs with location averages one standard deviation above the mean have on average around $0.026=0.16$ higher productivity (log TFP) than plants in their peer industries nationally.

While our main dispersion statistic is the variance, we also provide the productivity difference between the 90th and 10th percentiles in the second row of table 1.¹⁰ This difference in log TFP is 0.47 (61%)—on average, plants in the 90th percentile MSA are 61% more productive than plants in the MSA at the 10th percentile.

Panel b replicates this analysis for the location-industry effects $τ^l,i$⁠, which permit place effects to vary by industry. Recall that, when plotting the variance and constructing dispersion statistics, we weight each location-industry effect by the share of the industry in total employment within its respective location, for comparability with the location effects $ξ^l$ plotted in Panel a, which at the MSA level weighted industries by employment shares.

As a benchmark, if all industries in a location deviated by the same percent from their national industry benchmark, then the location and location-industry effects would exhibit the same dispersion. If productivity premia are imperfectly correlated across industry within a location, then industry-specific location effects may exhibit more dispersion than location effects. We find a considerably more dispersed distribution of the industry-specific location effects, with a variance of 0.110. The difference in log TFP between the 90th and 10th percentile is 0.98 (i.e., 166%).

Section IVA has quantified the differences in average productivity across places. However, some of this dispersion could be spurious, reflecting dispersion in idiosyncratic productivity levels of heterogeneous plants rather than true place effects. We now test the extreme hypothesis that there is no variation in place effects, and that the raw variance of the measured average-based place effects reflects idiosyncratic plant heterogeneity only.

Implementing the general methodology in section IID, we randomly relabel each plant’s location $l(p)$ while preserving the empirical plant-count distribution in each location-industry $l∈L$⁠, ensuring MSAs’ industry structures are unaltered in terms of plant counts. Since we draw without replacement, all plants are used exactly once per randomization. We generate 1,000 randomized economies. We treat each randomized economy as we did the empirical one, calculating place averages of productivity and their raw variance. We also construct 95% “confidence intervals” by extracting the 25th and 975th ranked observations in this sampling distribution; the position of the empirical raw variance in this sampling distribution gives the $p$-value, which we also report.

Across the 1,000 randomized U.S. economies, the mean variances are 0.017 for the location effects and 0.096 for the location-industry effects, compared to 0.026 and 0.110 for the empirical raw variances calculated and discussed above in section IVA. That is, granularity on its own already generates tremendous—purely spurious—variation in average-based place effects.

For illustration, figure 1 also includes, as dot-dashed lines, the distribution of place effects in the specific randomized economy most closely matching the mean permuted variance. Intuitively, the closer that dot-dashed line is to the line representing the actual U.S. economy, the more similar the random economies are to the empirical distribution, and the more granularity alone could account for the observed dispersion.

In figure 2, we present the distribution of raw variances of the 1,000 randomized U.S. economies, the mean of which we reported above. (Here, Census disclosure guidelines do permit us to release the uncensored distribution.) This distribution is the nonparametric sampling distribution of the variance of place averages under the assumption of no place effects. The vertical dashed line denotes the level of the empirical variance. For location effects, panel a clarifies that the empirical variance is above 991 of the 1,000 permutation values given the sampling distribution; the location-industry effects in panel b puts the data above the 985th observation of the 1,000 permutation values. These values imply one-sided $p$-values of 0.010 and 0.016. That is, the empirical variance is statistically more dispersed than would be expected from a null hypothesis of no place effects, even though such economies would generate substantial purely spurious variance.

This test provides a nonparametric statistical rejection of the absence of true place effects, which hence contribute to the observed variance of place averages of productivity. But to obtain an estimate of the variance of true place effects, we cannot simply subtract the raw variance from the counterfactual mean variance of the random economies, for instance, as, in the permutation test, plants’ productivity levels $apli$ take with them their potential true place effects $τl$⁠. Instead, we next implement our split-sample correction to constructively quantify the variance of true place effects.

We now implement our split-sample procedure in order to constructively quantify the variance of true place effects by removing the granularity bias.

The concrete implementation of the methodology laid out in section IIE takes the following steps. While the covariance is an unbiased and consistent estimator of the variance, granularity—the very reason we draw on this method—may still imply substantial error in one given random sample split. We therefore implement 1,000 random sample splits, and we extract the resulting distribution of covariances. We report the mean as our preferred statistic, but additionally provide information on the distribution. Specifically, we extract the, informal, nonparametric 95% “confidence intervals” implied by the sampling distribution of the resulting 1,000 covariances. When constructing location-industry effects and computing covariances, we weight by the location-industry employment share of the industry in the MSA of the full rather than split sample employment shares. (As before, we do not weight across MSAs.)

The bias correction dramatically reduces the variance of productivity across U.S. regions by more than two-thirds for location effects, from 0.026 to 0.008, with 95% of our draws falling in the range of 0.006–0.010. For industry-specific location effects, the variance is reduced by four-fifths, from 0.110 to 0.023, with 95% of the draws falling in the range of 0.019–0.027. Figure 1 illustrates the effect of the bias-correction on the distribution of place effects as a dashed line, drawing on a simple mean-preserving linear transformation of the raw distribution to match the bias-corrected variance.¹¹ That is, this distribution corresponds to one that matches the variance of true place effects, which is dramatically more compressed than the raw distributions. Hence, on the one hand, two-thirds to four-fifths of the cross-regional variation in productivity reflects the bias arising from granularity unrelated to true place effects. On the other hand, and consistent with our permutation test, the remaining variation constitutes the still economically and statistically significant variance in true place effects.

We visualize the bias correction in figure 3. The binned scatter plot depicts one specific split-sample economy, selected among the 1,000 randomizations to have its covariance-to-variance ratio be closest to the corresponding mean value of our 1,000 split-sample economies’ coefficients, as described below. Panel a reports on the location effects, panel b on the industry-specific location effects. The panels are scatter plots, juxtaposing, for each place, its pair of place effects computed separately on the basis of the samples split in half within each place. The graph summarizes the underlying observations into 25 equally sized bins, but the regressions are run on the underlying individual place effects. The x-axis captures the means of each bin from one split sample, and hence traces out the raw dispersion of average-based place effects (in the half sample). As throughout, we do not weight across MSAs, although, for industry-MSA effects, we weight by the industry’s employment share in the MSA (here again, as above, weights are constructed off the pooled sample, rather than on the basis of a specific sample).

The figure also includes two extreme benchmarks. Intuitively, if there were no relationship in productivity between the two split samples $A$ and $B$ within a place, each split sample average would reflect idiosyncratic effects only, and a line fitted to the scatter plot would have a slope of 0 through the origin. As another benchmark, in the absence of idiosyncratic effects, place effects, common to both split samples, would dominate the split samples’ averages, generating a 45 degree line.

The empirical effects fall somewhere in between these two extremes, providing a striking visual clarification that the empirical economy is characterized by a large degree of granularity in productivity differences across places. We estimate a slope of 0.275 for the location effects, and a slope of 0.166 for industry-specific location effects.¹² The linear regression coefficient corresponds to $γ=Cov(ξ^lA,ξ^lB)Var(ξ^lA)$ for the location effects, and analogously for the location-industry effects. Since $Cov(ξ^lA,ξ^lB)$ is our bias-corrected estimate of the (full sample $A∪B$⁠) variance $Var(ξlA∪B)$⁠, the regression coefficient represents the share of the raw variance (of the half sample making up the variation traced out on the x-axis) that survives bias correction. These positive slopes therefore confirm the attenuated, yet existent, presence of true place effects we have discussed above by comparing the mean covariance of the split samples with the population raw variance. Of course, the slope actually implies a slightly smaller fraction because the split-sample variance (i.e., the denominator corresponding to the estimated coefficient, $Var(ξ^lA)$⁠) is slightly larger exactly due to heightened granularity from halving the sample size.¹³

We now provide a series of alternative specifications with the goal of tracing out the sources of granularity bias, and we explore, but ultimately dismiss, potential alternative strategies to reduce it. Mirroring the discussion in section IIC and guided by our core equation (6), we dissect the three potential sources: finite plant counts per place, large idiosyncratic dispersion in plant-level productivity unrelated to place, and heterogeneity in plant size. Our main exhibits for these checks are table 1 and figure 4.

As a direct way to gauge the role of cell counts, we vary the minimum (location-industry) cell size cutoff. Table 1 column 1 reports the baseline specification with minimum size requirement of two plants. Column 2 reports the statistics when requiring at least ten plants. In figure 4, we vary this restriction incrementally from 2 to 150 (with spacing determined by Census disclosure rules).

Consistent with a decline in granularity bias, the raw variance falls when we raise the minimum cell count. Column 2 of table 1 clarifies that moving to ten rather than two plants per cell, the raw variance falls from 0.026 to 0.021 for location effects, and, more dramatically, from 0.110 to 0.045 for location-industry effects. As depicted with the line with solid circles in the figure, the raw variance falls as the minimum plant count per cell increases, and more so for the industry-specific location effects (panel B in the table, and panel b in the figure) than for the location effects (panel A and panel a).

Yet, inevitably, restricting the sample to larger and larger cells has compositional effects beyond granularity bias. It is possible that the remaining places have place effects that are more and more similar. As shown in table 1 column 2 panel A, starting from the threshold two and moving to ten, the covariance for location effects is essentially unchanged. Figure 4 panel a, which plots the (mean) covariance (line with solid triangles), reveals a stable covariance until a threshold of around 40 plants, and then it starts dropping gradually, reaching zero at around 100 plants. For industry-specific location effects, table 1 column 2 panel B reports a drop in the covariance to 0.014 with at least ten plants compared to 0.023 with at least two plants; figure 4 panel b reports the corresponding moderately steeper gradient of the covariance to the minimum cell count.

The $p$-values of the permutation tests for the specification with at least ten plants, reported in table 1 column 2, continue to indicate that even with more firms per cell, the empirical variance is squarely statistically different from random allocations of plants across places. This fact is indicated by the line with hollow diamonds and the associated 95% confident intervals, making clear that the empirical raw variance only crosses these confidence bands at around 100 plants, for both location and location-industry effects.

The figure also makes clear the catch-22 that granularity bias provides: the easiest “solution” to reduce granularity bias is to restrict one’s analysis sample to cells that are less subject to it—throwing the baby out with the bath water. Comparing column 1 (our baseline specification with at least two plants per cell) with column 2 (where we require at least ten plants) in table 1 illustrates this tradeoff: only about 250 out of our initial set of MSAs remain, 2,800 out of the 11,500 MSA-industry cells, and around 86,000 out of the 120,000 plants (where Census disclosure requirements force us to round all counts). The dotted line in figure 4 reports on the steep sample count (number of cells) tradeoff for the interval between 2 and 150 plants, which is most dramatic when going from 2 to around 20–30, and then continues more gradually. At a cell-size cutoff of 100, the remaining sample features only 10% of MSAs (and a much lower fraction of industry-MSA cells), fails the permutation test, and features a bias-corrected variance of zero.

Another way to adjust plant cell counts is to redefine cells. Our results for location effects $ξl$ as aggregates of industry-specific location effects $τl,i$ already speak to the impact of aggregating industry cells. Alternatively, we now redefine industry cells from 4-digit to 6-digit NAICS, reporting results in column 3 of table 1. There are 359 6-digit NAICS manufacturing industries nested in the 86 4-digit industries, and indeed, column 3 reveals that the number of plants per location-industry cell falls while the number of location-industry cells increase. A pure granularity perspective, holding the composition of place effects constant, would predict an increase in raw variances. Yet, there is a composition shift as well, as some 6-digit cells do not have at least two plants at the 6-digit industry-location level, as indicated by the lower plant count. Indeed, the remaining cells appear more homogeneous: though the raw variance falls by less than half, the covariance falls by around two-thirds. Moreover, this sample and specification fails the permutation test, with average permuted variances being close to the empirical raw variance. Overall, we conclude that the composition changes that accompany stricter cell definitions prevent us from isolating the true variance of place effects and the role of finite plant counts in granularity bias.

Besides the limitation that the above exercises inevitably change the underlying fundamentals of the remaining cells in the analysis sample, they do not address the other two dimensions of the bias, namely the degree of idiosyncratic plant heterogeneity and plant size differences, which we study separately next.

As described in equation (6), granularity can also reflect large plant-level, idiosyncratic within-location variance, even if cells have relatively many plants. Our first lever to study this source of granularity bias is to vary the winsorization of plant-level TFP, at 0% and 2.5% rather than, as in our baseline, 1% (at the national level). The results are reported in column 4 of table 1 for 0%, and in column 5 for 2.5%. While indeed winsorization and hence extreme values of plant-level productivity play a role in the dispersion measures, it is limited. Studying variances, abandoning winsorization leads to a small increase from 0.026 to 0.029 for location effects, and 0.011 to 0.012 for industry-specific location effects; raising the threshold to a symmetric 2.5% leads to a modest attenuation to 0.022 for location effects and 0.094 for location-specific industry effects. The 90th–10th percentile difference is also quite robust to winsorization.

Turning to the permutation tests, the $p$-values remain clearly below the 5% threshold, although, if anything, winsorization boosts the statistical significance of the empirical raw variance compared to the randomization benchmark, consistent with granularity bias.

A priori, winsorization should probably lower the bias-corrected variance, if extreme plant values are clustered in specific places and reflect true place-specific effects. Indeed, the covariances are 0.009, 0.008, and 0.006 for the location effects for the 0%, 1%, and 2.5% winsorizations, and, respectively, 0.026, 0.023, and 0.019 for the location-industry effects. In sum, granularity bias withstands our attenuation strategy of adjusting tails in the national data, even as this strategy itself alters the sample and erodes the true variance.

The third source of granularity bias is heterogeneity in plant size, by which place effects are weighted. (For exposition, equation (6) is written with equal plant weights.) Large plants will dominate average-based raw place effects, and may generate much of the spurious dispersion in the permutation tests. To gauge the role of large plants, we also present results that weight each plant equally, with results reported in column 6 of table 1. Consistent with the role of large plants in granularity bias, the raw variances fall by around four-fifths for the location effects, and slightly more than half for the location-industry effects. The permutation test reveals a tantamount decline (in percent terms) for the mean raw variance of the randomized economies. But the $p$-values of the empirical raw variance become even lower, falling below 1%, indicating if anything that the role of granularity has not declined. Congruently, a similar scaling down occurs for the bias-corrected variance of true place effects, which falls by three-quarters for location effects and by less than two-thirds for industry-location effects, compared to the weighted specifications in column 1. Hence, we conclude that the unweighted specifications yield a similar picture for the share of the raw variance reflecting granularity bias, while scaling down the overall level of dispersion. Again, we caution that this specification check inevitably entails a substantive redefinition of productivity place effects and the underlying (weighted) sample, so that, even if granularity bias had been less pronounced in the unweighted specification, equal weights naturally do not provide a solution if the preferred specification is weighted (for it to be consistent with aggregation, for instance).

Overall, we conclude that granularity bias is a robust feature of the data, which dominates the raw variances of average-based place effects, and that potential alternatives to our covariance-split-sample strategy that build on adjusting the core dispersion-relevant fundamentals of the data run the risk of throwing out the baby with the bath water.

Our main findings have revealed that due to plant idiosyncracies, systematic place effects are considerably less pronounced than raw averages suggest. An interesting specific question is the degree to which new plants inherit the place effects of the old, incumbent plants. For instance, a common assumption is that spatial TFP differences across places are a fixed property of the place-specific production function that would also determine productivity “at the margin” for counterfactual input reallocations (e.g., Desmet & Rossi-Hansberg, 2013; Hsieh & Moretti, 2019). To the degree that the extensive margin (new plants) absorb reallocated inputs (rather than incumbent plants scaling up or down), our strategy can quantify the degree to which TFP effects indeed carry over to new plants. As one extreme, if new plants’ productivity is considerably more compressed across places, or unrelated to that of incumbent plants, such counterfactual reallocation would not generate the gains from reallocation implied by the productivity average of existing plants.

A priori, older and larger incumbent plants dominate the pooled averages constructed in section IV, leaving room for the place effects for new plants to differ. In 2012, plants older than five years made up 78% of manufacturing plants, and 91% of total employment in the manufacturing sector (source: U.S. Census Business Dynamics Statistics). On the theoretical side, in models of embodied technological change (as in, e.g., Sakellaris & Wilson, 2004) new projects reflect the frontier technology while incumbent, old projects reflect legacy technologies, so that measured place averages may reflect age composition, or place effects would show up among new plants. Some models (e.g., Duranton and Puga, 2001) specifically predict that some cities are better environments for entrepreneurship than others. The entry and location choices of new plants can also be considered revealed-preference proxies for productivity differences (Henderson, 1994).

We partition the population of plants into new plants aged five years and younger (superscript $Y$ for “young,” not $N$⁠, which we use for counts), and old plants (⁠$O$⁠) aged six years and older. To implement our split-sample method, we now require at least two plants per age group per location-industry cell, rather than two plants of any age, as before. This restriction has limited effects on dispersion statistics for the pooled (i.e., not age-specific) sample, which we report in table 1 column 8. Compared to the baseline sample requiring two plants of any age (column 1), the new restrictions leave the raw variance of the location effects (panel A) fairly stable and essentially leaves the covariance unaffected, despite dropping around a quarter of MSAs. For the industry-specific location effects in panel B, the restriction drops around three quarters of cells. The raw variance drops by around 40%, but with a much smaller drop (a quarter) in the covariance, suggesting that the restriction drops particularly small and noisy location-industry cells.

Figure 5 panels a and b plot, in thick lines, the distribution of raw location effects for new plants, $ξ^lY$⁠, and, respectively, location-industry effects, $τ^l,iY$⁠. Table 1 reports the full set of dispersion statistics for the new plants only (column 9). In thinner lines, the figure plots the distributions of old plants’ place effects (reported in table 1 column 10). We now weight location-industry effects by the industry’s employment share in total local employment, separately computed for the old and new plants. We continue to not weight across locations.

At $Var(ξ^lY)=0.084$⁠, location effects of new plants are two-and-a-half times as as dispersed as the old place location effects (⁠$Var(ξ^lO)=0.033$⁠), which in turn appear to dominate the pooled sample’s raw variance (0.032, see table 1 column 8 panel A, which reports dispersion statistics for the pooled sample). The new plants’ location-industry effects are also two-and-a-half times more dispersed at $Var(τ^l,iY)=0.152$ compared to the (pooled) raw variance of 0.064, in turn again close to those for the old plants’ place effects (⁠$Var(τ^l,iO)=0.066$⁠). For the new plants, table 1 column 9 also reveal that the top 90th to 10th spread of location effects is 0.744, and 1.11 for location-industry effects.

Hence, taking the raw variances at face value, new plants appear dramatically more dispersed in their productivity than old plants or as would be suggested when pooling all plants. This increased dispersion would imply, for instance, that place matters much more for the productivity of marginal projects, or entrepreneurship, than would be suggested by a standard pooled measure, and that, potentially, forces leading to this dispersion, such as sorting or agglomeration forces, might be even more pronounced for such new projects.

However, much of this higher variance of the new plants’ place effects may simply reflect heightened granularity bias, due to smaller populations and potentially even higher idiosyncratic dispersion in true or measured TFP. Our split-sample strategy permits us to again remove this bias, and to isolate the variance of true place effects for new plants. Indeed, the bias-corrected variances of the new plants drop dramatically to $0.015$ for location effects and to $0.019$ for location-industry effects. These corrections for new plants’ place effects entail much larger reductions from the corresponding raw variances than for the pooled samples’ place effects, while still leaving the dispersion of true place effects higher than that of the old plants (which exhibit bias-corrected variances of 0.008 and 0.016 for location and industry-specific effects, respectively).¹⁴

True place effects for new and old plants may be distinct. For example, in a nursery cities view (Duranton & Puga, 2001), some cities favor entrepreneurship, in ways that need not carry over to incumbent, large production units. Alternatively, place-based productivity differences could be entirely cohort-specific.

Augmenting our split sample method, we investigate this question. In figure 5 panels c (location effects) and d (location-industry effects), we juxtapose the new-plants place effect of a given place with the corresponding place effect of old plants only.¹⁵ As one benchmark, we plot a slope of 1: place effects would show up for both new and old projects identically. As another benchmark, we plot a slope of 0, which would indicate no relationship between new and old plants’ respective place effects.

The hollow scatter points trace out the empirical relationship between the new and old place effects. They suggest that the place effects for new plants are much closer to a no-correlation benchmark than the 45 degree line. We also include, as a solid line, the estimated linear regression slope $γRF$⁠, which is the reduced-form effect in the IV interpretation of the split-sample method we describe below. The slopes reveal a small (and imprecisely estimated) elasticity of 0.121 (SE 0.119) and 0.125 (SE 0.066) for location and location-industry effects of new plants’ to old plants’ place effects.

However, the unity benchmark is inappropriate due to granularity bias, which shows up as attenuation bias in the regression estimate. To construct a bias-corrected benchmark, we implement a formal instrumental variables (IV) approach. We estimate a first stage using the split samples, regressing the place averages of a random half sample of old plants indexed by $(O,B)$ (y-axis) on those on the other sample of old plants $(O,A)$ (x-axis). (In fact, the aforementioned slope between new and old plants used that half sample on the x-axis rather than all old plants.) The line plots the resulting first-stage regression slope $γFS$⁠, which provides benchmarks of 0.194 (SE 0.074) for location effects and 0.184 (SE 0.049) for industry-specific location effects, hence far from 1.¹⁶ This first-stage relationship is analogous to the visualization of the overall bias correction in the full sample in figure 3. With this bias-corrected benchmark, the new plants appear to inherit a larger—but far from perfect—share of the place effects of the old. The formal IV effect $γIV=γRF/γFS$ is 0.620 (SE 0.686) for the location effects and 0.683 (SE 0.376) for location-industry effects. Intuitively, the IV effect measures the distance of the reduced form effect from the first stage, that is, the corrected benchmark of full sharing.

To generate the figure, we generate 1,000 split-sample economies, and then we select, for visualization in the scatter plot, the two economies with first-stage and reduced-form coefficients closest to the mean coefficients (putting twice as high a penalty on the error in the first-stage coefficients). The mean estimated first-stage, reduced-form, and IV coefficients are, respectively, 0.194, 0.113, and 0.681 for the location effects, and 0.183, 0.127, and 0.716 for the location-industry effects.

We conclude that while place effects for new plants comove by about 62%–68% (using the point estimates) with those of old plants, there is a substantial degree of independent variation in the new plants’ place effect, with estimates having wide confidence intervals.

We complement our primary productivity measure, log TFP, with log value added per worker (labor productivity). This measure is less demanding, requiring neither specifying a production function nor comprehensive input measures. As a benchmark, with Cobb-Douglas production, the dispersion of log labor productivity corresponds to that of the log marginal product of labor (i.e., the log labor share—netted out by the industry fixed effects—plus the plant’s log value added per worker). Between-firm dispersion in marginal products can reflect standard misallocation (Hsieh & Klenow, 2009), analogously for spatial misallocation (Hsieh & Moretti, 2019).

Column 7 of table 1 replicates our main specification using labor productivity in place of TFP. Appendix B contains replications of other main exhibits. In contrast to the prediction that marginal products are more compressed than TFP, we find that raw variances increase compared to those of TFP, by about 150%, from 0.026 to 0.063 and from 0.110 to 0.290 for location and location-industry effects. Given the tantamount increase in permutation variances, $p$-values remain similar. Finally, the bias-corrected variance estimates increase by about 100%, from 0.008 to 0.016 for location effects and from 0.023 to 0.041 for location-industry effects.

We conclude that the dispersion in true place effects is if anything more pronounced for marginal products than for TFP. Moreover, the relative share of the raw variance that reflects granularity bias is in fact somewhat higher: three-quarters (rather than two-thirds) for location effects, and six-sevenths (rather than four-fifths) for location-industry effects.

Finally, in appendix D, we show robustness to using log revenue (rather than value added) per worker for our baseline manufacturing sample. Additionally, this appendix shows robustness to studying a broader set of industries, namely all tradable industries (including those beyond manufacturing), since tradables avoid local output price indices as a standard source of spurious differences in the revenue per worker measure. (In this broader industry sample, we can only study revenue per worker, as the input measures required to construct TFP and value added per worker are not available.) We find broadly similar results for both manufacturers and all tradables using this measure.¹⁷

We close our empirical study by applying our analysis to the within-country, cross-regional dispersion of 15 European countries. We draw on internationally comparable firm-level data from Bureau van Dijk (BvD), construct TFP measures for manufacturing firms, as described in section III, and, separately for each country, study regional dispersion among the NUTS-2 regions, which most closely correspond to U.S. MSAs.

Figure 6 and appendix table A2 report three dispersion statistics country by country, including the United States: the raw variance (solid circles), the mean raw variance implied by 1,000 random allocations of plants across places (hollow diamonds) along with the 95% confidence intervals (dashed lines) taken from the sampling distribution given by the 1,000 randomizations, and the mean covariance (triangles)—the bias-corrected estimate of the variance—of the 1,000 randomly split samples along with 2.5% and 97.5% confidence intervals implied by the sampling distribution (solid lines).

Consistent with the U.S. findings, the European applications exhibit large—and quite heterogeneous—raw variances of average-based place effects. The raw variance of the location effects ranges from 0.005 for Austria to around 0.024, 0.029, 0.037, and 0.053 for Norway, the United Kingdom, Italy, and Germany. It is tempting to ascribe these high raw variances to intuitive regional divergences in those countries (the high-unemployment regions in the North in Norway, the productive urban centers in the United Kingdom, the South-North gap in Italy, the East-West division in Germany). Yet, in the United Kingdom, random allocations would have yielded similar dispersion, in fact in 7 countries (Austria, Denmark, France, Hungary, Spain, Sweden, and the United Kingdom). However, that null hypothesis of no-more-than-random productivity dispersion can be rejected at the 5% level in many but not all of those aforementioned countries with anecdotal divergences and high raw variances (the full list is Bulgaria, the Czech Republic, Germany, Italy, Norway, Portugal, and Romania, while Poland is marginally significant with a $p$-value of 0.058).

The biased-corrected variances are lower than the raw variances in all cases, but their ratios vary substantially. The bias correction shrinks the raw variance by less than a quarter for Bulgaria, Norway, Romania, Portugal, and Italy, but by over 70% for Austria, France, and the United Kingdom.

For the industry-specific location effects, granularity bias is amplified, as with the U.S. data. As with the U.S. data, the raw variances are dramatically larger, by an order of magnitude, but the bias-corrected estimates using the split-sample covariances settle in at quite similar (but generally slightly higher) levels to the location effects. However, reflecting the heightened granularity bias, the $p$-values of the permutation tests reveal that the industry-specific location effects are insignificantly different from the random allocation benchmark in all countries but Germany and Romania.

We end our assessment of the cross-country context by noting the small amount of locations (NUTS-2 regions), which range between 5 and 42, industry-location cells, ranging from 132 to 717, and firms, ranging from 1678 to 116,918 (reported in appendix table A2). Appendix table A3 and appendix figure A4 report the results for value added per worker; as in the United States, the dispersion statistics increase, with considerable heterogeneity.

We tentatively conclude that granularity leads to large—if anything more dramatic—upward bias in productivity differences across place in the 15 European countries we can study in internationally comparable firm-level microdata. Obvious challenges are the lower cell-level firm observation counts and other data quality issues associated with the BvD data, which we have discussed in section III.

We have dissected the dispersion in productivity across cities, a major motivation of research in urban economics, and traced much of it to the “luck of the draw” of tremendously heterogeneous plants that happen to be located in a given location. The share of variance due to this spurious source is especially pronounced when zooming into fine-grained industries.¹⁸ Randomly allocating plants across places would generate only slightly less dispersion than the empirical economy. Two-thirds to four-fifths of the raw variation is an artifact of granular data. This broad pattern holds when measuring productivity as TFP as well as value added per worker, in U.S. plant-level data and in firm-level data from 15 European countries, and it extends to all tradable industries. Furthermore, we uncover substantially more, and independent, variation in location effects measured from new plants, implying that place effects may not perfectly carry over to new plants.

In short, in our analysis, idiosyncratic plant heterogeneity appears to drive much of place heterogeneity. The remaining share of dispersion our method attributes to systematic place effects may reflect a combination of causal effects of place on productivity (such as agglomeration forces), as well as sorting, or spatially correlated measurement error.

We close by reiterating that our contribution remains a descriptive analysis. Plausible implications of our findings concern the modeling of spatial equilibria and counterfactuals, where places are often assumed to exhibit heterogeneous productivities due to systematic sources, rather than granularity bias. We leave it for future research to develop a spatial model of heterogeneous granular plants. We speculate that permitting granularity as a source of productivity differences in such a model would reduce the relevance of alternative, systematic sources, such as those we discussed in the Introduction.