The total tonnage of fertilizer applied to corn increases by 484.45 tons, an 26.6 percent increase, statistically significant at the 1 percent level. The impact congregational mergers have on corn fertilizer use is not only statistically significant, but also represents an economically meaningful change. In sum, the information in Table 2.3, Table 2.4, and Table 2.5, demonstrates that congregational mergers increase fertilizer use, in keeping with Proposition 2. Next, we test Proposition 3: that congregational mergers will not affect technology adoption when all potential adopters are fully informed. Strip cropping, irrigation, and orchards are technologies for which we expect no effect. Table 2.6 demonstrates the impact congregational mergers have on the number of farms using strip cropping and the acres under strip cropping; the number of farms reporting irrigation use and the total number of irrigated acres; and the total number of acres in fruit orchards, groves, vineyards, and nut trees. Table 2.6 confirms our hypothesis: we see no statistically significant impacts of congrega- tional mergers on strip cropping, irrigation, or orchard acreage. Furthermore, the magnitudes of the coefficients we do see are small, and in the case of irrigation, have negative signs. The absence of results in this table further supports the fact that congregational mergers are driving the changes in input uses observed above, because mergers are affecting farmers on the dimensions we would expect, but we are not seeing impacts on agriculture that should not be affected by mergers.With any regression analysis,blueberries in containers growing it is important to ensure that the results are robust. We use three pieces of evidence to demonstrate that the results we present in this paper hold up to robustness checks. First, we saw impacts of congregational mergers where we expected them: on fertilizer and lime use and on corn. We did not see impacts where we expected them not to be: on strip cropping, irrigation, and orchards, as presented above.
In addition, our results are robust to a variety of different land use variables provided in the census of agriculture data: the outcomes measured in number of farms do not change significantly if instead of total farms, we use commercial farms or cash-grain farms; the outcomes measured in acreage and tonnage do not change if we use acres in the county or acres harvested rather than acres in farms. In this section of the paper, we perform a placebo test. We also investigate channels other than information through which congregational mergers might be driving fertilizer adoption, and provide evidence against these other possible explanations.Table 2.7 has the placebo analysis. We run this check in order to see whether mergers that occurred from 1964 to 1967 impact our outcomes in 1964, before these mergers actually occurred. We use the time period 1964 to 1967 because it includes the same number of years as our actual treatment period. Column looks at farms using fertilizer; at acres fertilized; at tons of fertilizer used; at corn acres fertilized; at farms using lime; and at acres limed. We expect to see no statistically significant impacts of “future” congregational mergers on these outcomes. Indeed, Table 2.7 shows that, with the exception of the number of farms using lime, there is no statistically significant effect of future congregational mergers on 1964 input outcomes. In addition, comparing these effects to those in Tables 2.3, 2.4, and 2.5, the magnitudes of the coefficients are quite small. This helps confirm that the effects we are observing above are real and driven by the congregational mergers we observe, rather than by something unobserved. To assuage concerns about small-sample inference, we also run a permutation test, in which we randomly assign 39 counties to treatment 10,000 times. Using each of these treatment assignment vectors as a placebo treatment, we find our actual effect on farms using fertilizer is larger than all but 4 percent of the randomly drawn treatment vectors. Figure 2.7 displays the results of this procedure. It is still possible that our results are being driven by something other than a congregational merger driven information effect. Here, we explore two other possible explanations for our results. The first is the presence of agricultural extension.
Agricultural extension, formally introduced in the United States by the Smith-Lever Act of 1914, plays a major role in information dissemination in agriculture. There is a large literature on the effect of agricultural extension, both in the United States and elsewhere, on agricultural productivity and technology adoption ; Huffman ; Birkhaeuser et al. ; Dercon et al.. Despite the importance of extension, we argue that it is in fact congregational mergers and not extension services that generate the results we find in this paper: because of the fixed effects strategy, in order for agricultural extension to be driving these results, we would need to see agricultural extension services changing differently over time in treatment counties than in control counties, having removed the state time trend, only over the 1959 to 1964 time period. This is potentially plausible, but seems unlikely, especially because extension funding and the number of extension agents allowed is governed by state laws, which do not change often. For example, the Minnesota statutes outlining extension were first passed in 1923, updated in 1953, and were not revised again until 1969. The law allows for “the formation of one county corporation in each county in [Minnesota]” to act as an extension agency, with in most cases one extension agent and a specified budget, based on the number of townships in the county. While county extension offices documented their activities for mandatory state reports, these reports were inconsistent across different counties and years. Also, many of the variables measured were endogenous, such as the number of phone calls received or the number of attendees at extension events. As a result, it is impossible to credibly measure the intensity and efficacy of extension efforts over our sample period.Another plausible explanation would be that the mergers also facilitated increased access to capital. In order to provide evidence against this possibility, we estimate Equation again, this time with the number of farms with each of a variety of capital-intensive technologies as outcome variables. Table 2.8 shows the impact congregational mergers have on the number of farms with cars, trucks, tractors, bailers, and freezers.
As expected, we find no statistically or economically significant effect of congregational mergers on capital-intensive inputs: the standard errors are quite wide, and the effect sizes small: the coefficient on cars, for example, is only a 0.01 percent increase relative to the control group mean, and the standard error is almost one hundred times the size of the coefficient. This suggests that congregational mergers did not substantially increase access to capital, and provides additional evidence that information is the main channel through which congregational mergers impacted technology adoption. Finally, one might worry that by only using TALC congregational mergers in our analysis, we are understating the true treatment effect. We argue above that the TALC mergers are exogenous, and, due to the heavily Lutheran populations in these regions, the mergers where we would expect to see an effect. Indeed, the congregations that are merging in these data have, on average, 492 baptized members, so seeing an additional 35 farms begin to use fertilizer is an entirely reasonable effect size. There is another major Lutheran church branch, the Lutheran Church – Missouri Synod ,planting blueberries in containers that was not directly involved in the TALC merger, but whose mergers could be attributed to increased discussion about merger surrounding TALC. We collected data from Concordia Historical Institute, the LCMS seminary, on congregational mergers between LCMS churches during the sample period. There is only one merger that occurs in a non-metropolitan county during this time period, and the inclusion of said merger does not produce a statistically distinguishable result from using only the TALC mergers. Ultimately, given the range of tests that we perform, we have confidence that our results are robust and that we are correctly attributing them to the information effect of congregational mergers. Since the early 2000s, US ethanol production has exploded in response to federal policies incentivizing the production of renewable fuels. In 2005, Congress passed the Energy Policy Act introducing a Renewable Fuel Standard mandating that 2.78% of gasoline sold in the US be from renewable sources. In 2007, Congress passed the Energy Independence and Security Act setting annual renewable fuel mandates for US production with an ultimate goal of 36 billion gallons by 2022. Of these 36 billion gallons, 15 billion are to be conventional bio-fuels – corn-based ethanol in particular. The US ethanol industry has clearly responded to the Renewable Fuel Standards established in the EPAct and EISA. Between 2002 and 2014, US ethanol production has increased from just over 2 billion gallons per year to over 14 billion gallons per year . In order to produce such quantities of ethanol, the number of corn ethanol refineries in the US has increased from 62 in 2002 to 204 in 2014 . The striking increase in US corn ethanol production has raised several important questions about its unintended consequences. One strand of research has explored how increased demand for ethanol has affected land use in the US corn belt as aggregate demand for corn increases . Another strand of research has been more concerned about the environmental externalities of changing agricultural patterns, particularly focused on nitrate runoff and water pollution . In this chapter, I explore both the land use change effects and environmental effects of expanding ethanol production. In particular, I study the geospatial effect of ethanol re- fineries’ placement on nearby land use change and use my results to estimate environmental consequences. I am specifically interested in how the location of ethanol refineries spatially affects agricultural land, and I do not attempt to identify the full general equilibrium effect of the 14 billion gallon US corn ethanol industry. Put another way, I study how the distribution of ethanol refineries differentially affects different agricultural areas net of the ethanol industry’s aggregate effect on corn prices. I find that within a population of almost 114 million acres of agricultural land in Illinois, Indiana, Iowa, and Nebraska, nearly 300,000 more acres of corn were grown in 2014 than in 2002 due merely to ethanol refinery location effects.
This represents approximately 21,000 tons of nitrogen applied as fertilizer. Almost all the 300,000 acres of increased corn acreage exist within 30 miles of an ethanol refinery, suggesting that these refineries have strong local effects on land use change and nitrogen use. There is clear economic intuition for why ethanol refineries would differentially affect nearby and faraway agricultural land. When a corn-fed ethanol refinery is built, it represents a new terminal market for corn. Since refineries operate continuously, they have an inelastic demand for this input. And since transportation costs are significant for grains, one would expect an ethanol refinery to source its corn from the nearest producers. Thus, by reducing transportation costs for nearby producers , ethanol refineries essentially subsidize corn production for nearby farmers. On the margin, this subsidy incentivizes farmers to grow more corn – or grow corn more often – than they otherwise would. As corn production increases, so will nitrogen fertilizer use. Corn requires higher levels of nitrogen fertilizer than other Corn Belt crops, and particularly high levels of fertilizer when grown successively corn-after-corn. Thus, economic intuition suggests ethanol refineries would have a localized effect increasing corn production and nitrogen fertilizer use. Consequently, these refineries would also have an effect on localized nitrate runoff due to the increased nitrogen fertilizer use. Researchers have previously addressed different components of the ethanol industry’s effects on land use change and nitrate runoff. One line of research has explored whether the hypothesized local corn subsidy provided by nearby ethanol refineries actually exists. In a frequently cited paper, McNew and Griffith find that corn prices at an ethanol refinery are 12.5¢ higher than average, that the effect is slightly stronger for “upstream” refineries than for “downstream” refineries, and that price effects can be detected up to 68 miles from a refinery. However, Katchova and O’Brien both fail to find such a subsidy. Gallagher et al. highlight that locally-owned and non-locally-owned refineries have different effects on corn prices: the authors find that corn prices are increased by proximity to a non-locally-owned refinery, but not by proximity to a locally-owned refinery. Finally, Lewis finds different results in different states: ethanol refineries in Michigan and Kansas affect local corn prices, but refineries in Iowa and Indiana do not.