Maize revenues and quantity sold are also positively correlated with propensity to adopt Kudu, though not significantly so. It seems, therefore, that larger, better off farmers are more likely to use Kudu. Looking at the interaction term between treatment and the propensity score, we see the that positive revenue effects are concentrated among likely adopters, significantly so when we look specifically at maize revenues finding. Likely adopters also see significantly larger maize quantities sold finding. We see no significant difference in price for likely adopters, perhaps because prices are determined in general equilibrium in the village, and are therefore not distinct between adopters and non-adopters. Finally, Figure 5 presents heterogeneity in treatment effects based on baseline levels of the outcome, as measure in the baseline survey. Similar to Figure 4, the top panels plot Fan regression estimates of the outcome at endline on baseline levels separately by treatment and control, while the bottom panel presents the difference, along with the 90% and 95% confidence intervals. Density in the baseline measure is again presented in red. Consistent with the results from Table 7, we see null effects for the vast majority of farmers, who tend to lie to the left-hand side of the distribution in total revenues, maize revenues, and quantifies sold. This is unsurprising given the low adoption rates among these farmers. However, for the minority of farmers who lie to the right-hand side of the distribution – who are more likely to adopt Kudu – we see significant increases in total revenues and maize revenues specifically. Though not significant, point estimates on quantity sold are also large and positive for farmers who already sold large volumes at baseline. Perhaps surprisingly, we see a negative and significant effect on prices for those farmers in the far-right side of the distribution of baseline prices. This may reflect some of the broader convergence in prices observed upon introduction of this marketplace. Consistent with this,dutch bucket for tomatoes the top right-most panel suggests that prices are higher for those with initially low prices finding and lower for those with initially higher prices.
The control group for this sub-experiment are farmers in treatment villages who may already be experiencing general equilibrium changes from prices as well as indirect information effects from the treated farmers around them. Second, to exploit the power from the panel nature of the market survey, we then further randomly rolled tranches of control markets into the SMS Blast treatment. In each of the 12 market survey rounds between October 21, 2016 and March 24, 2017 we rolled in three control markets to the SMS Blast, treating all study traders and farmers with the Blast. Then, subsequent to the household and trader endline surveys, we rolled in an additional 36 control trading markets to the SMS Blast and so observe four final rounds of market surveys with this system in place. We begin by investigating the nature of the farmer-level SMS Blast experiment by looking at the extent to which farmer-level uptake of the components of the experiment differs between the SMS Blast treatment and the within-village controls. Table A.11 shows that the treatment-village control group has uptake rates that are in general about three-quarters of the way between the pure control group and the SMS Blast treatment finding. This suggests that there was fairly widespread dissemination of information about the intervention in treatment villages. Given this, it is perhaps not surprising that when we examine the first row of Table A.12 there are few strong differences in outcomes between the SMS Blast treatment and control. While the point estimates generally suggest a positive effect of being treated, only for the variable ‘know better’ finding do we see significant differences. The third row of this table provides a test of the roll-in to control villages, including a dummy for those farmers that as of the endline survey had already started to receive the Blast. Here, we see much smaller point estimates and no evidence that simply including control farmers in the Blast had any influence on outcomes at endline. This impression is confirmed by looking at Tables A.13 finding and Table A.14 finding. To exploit the panel nature of this treatment, we analyze these impacts using market and round-level data with two-way fixed effects and standard errors clustered at the sub-county level. In all cases effects on market-level outcomes appear very limited. The general lack of significance is confirmed visually in Figure B.11.
Overall, then, we conform with the broader literature in finding no large improvements stemming from information-only market price interventions, whether these are implemented individually within villages otherwise generally treated, or rolled in over time to untreated markets. We have a number of windows into the effects of the transport guarantees, because they were randomized both at the individual and at the contract finding level. First, we can look at the cross-buyer experiment, asking whether those buyers who were permanently assigned to receive the Basic or Comprehensive guarantee transact more business on the platform. Table A.15 shows that they do not. Next, within the original control group who were assigned no permanent guarantee, we can examine the effect of the random fraction of bids they post assigned to each guarantee group on the overall amount of business conducted. Table A.16 shows that increasing the fraction guaranteed does not increase business transacted. Finally, at the bid level we can ask whether having a specific bid assigned to a guaranteed increases the chance of doing business, both among the original experimental control group as well as among other buyers entering the platform subsequent to the experiment. Table A.17 examines the bid-level data and shows that for the original control, having a specific bid guaranteed increases the number of successful deals, the amount transacted, and the value transacted. Unfortunately, this pattern of results appears most consistent with a general lack of significance of the guarantees at generating new business, with the control group having come to understand the system well enough to game it finding. While we certainly do not take these results as suggesting that transport and contractual risk are unimportant in anonymous technological marketplaces, it does not appear that these guarantees, backed by AgriNet, were effective at removing them. We have provided a number of pieces of evidence suggesting that this intervention may have generated meaningful spillovers onto the control group. Most basically, the summary statistics on adoption and usage show that there was some uptake of the intervention, and an increase in receipt of SMS price information, even in control villages. Second, the evidence of convergence at the market level indicates that prices move in general equilibrium. If the spatial boundaries of these impacts do not satisfy SUTVA across sub-counties, spillovers to the control will exist. Finally, the “one treated” result in the dyadic data is a direct indication of the fact that trade flows increase between dyads in which only one of the markets is treated, indicating that trade patterns are affected even in markets that are not themselves treated. What does the presence of these positive spillovers mean for the accuracy of our overall treatment effects? They suggest that our market integration effects and farmer treatment effects may, if anything, be an underestimate on the true gains for the platform. For traders, for whom the platform seems to generate competitive pressures that squeeze profits, the implications of spillovers may be more complicated.
To examine the effects of spillovers on traders, we follow Hildebrant et al. finding in using baseline data to map the trading linkages between study clusters, and then exploiting the incidental randomized variation in the intensity of treatment within these trading networks to measure spillovers. The average sub-county is connected to 1.8 other sub-counties by baseline buying networks, and the average number of treated connections is .9. Given stratification-block FE αj , β1 measures the effect of the treatment in a village with no baseline trading connections finding, β2 gives the finding slope coefficient on number of total trading partners, β3 gives the spillover effect of treatment in the trading network for control markets finding, β4 gives the treatment heterogeneity by number of total trading partners finding, and β5 gives the additional spillover effect of having treated trading partners for markets that are themselves treated finding. Given the complexity of estimating standard errors in this data structure, we use Randomization Inference to randomly reassign the sub-county-level experiment 1000 times, re-calculating the network treatment intensity and the regression above for each iteration. In Appendix Table A.18, we perform a balance test by pointing this same specification finding at the baseline data.Table A.19 shows the results of looking at the first year of implementation. These short term effects indicate quite strong and heterogeneous spillovers. The overall effect of treatment is negative finding,blueberry grow pot and exposure to the treatment for control markets is also bad for traders. The SNT in the third row of this table shows that as control traders become more exposed to the treatment – perhaps facing greater competition in their buying markets, which are treated – they pay higher buying prices, achieve lower markups, and as a result see lower profits despite their quantities traded not changing much. Relative to this, the differential ST – SNT in the first row shows that treated traders are able to offset these spillover-related losses, perhaps due to greater access themselves to other markets when both are plugged into the Kudu network. We see a significant negative coefficient on buying price and a significant positive coefficient on markups that offset the spillover-related erosion of markups observed among the control group. Moreover, we see large and significant effects on both purchases and sales, suggesting that treated traders benefit in terms of sales volumes from exposure to a greater number of treated markets. These effects results in a differential ST – SNT profit effect that is positive, significant, and of a similar magnitude finding to that of the SNT effect. This suggests the for treated traders, the negative effect of being more exposed to treatment is offset by the positive effect of being able to access other markets that are within the Kudu network, resulting in limited total spillover effects finding for this group.
Given that the net treatment effect on trader profits is negative and exposure to the treatment is mostly negative for the controls, this suggests that the negative Intention to Treat finding estimates on traders presented throughout the rest of the paper are if anything biased towards zero by the presence of spillovers. Looking over the longer term, we can pool across midline and endline as is done in the rest of the paper for the trader and farmer outcomes finding. We find that, over the longer term, the negative SNT effects are moderated finding. The differential spillover on treated traders remains significant for the volume of purchases and the signs remain positive for revenues and profits, but are no longer significant. We therefore find that spillover effects for traders are strongest immediately after the introduction of the platform; over the longer run, most of the spatial inequalities created may have been arbitraged away. Overall, then, our study suggests that we experienced spillover effects that are in the direction of treatment effects finding, and hence we may be underestimating the gains from the platform in terms of increases in trade flows, price convergence, and impacts on traders. This is an inherent challenge for any randomized experiment designed to increase trade flows in an environment in which markets are not in perfect autarky. Short of randomizing at the country level, avoiding spillovers due to spatial and trade-network based connections may be impossible.What the randomization at scale buys us is the ability to detect any differences in GE outcomes – trade flows, prices, etc.– which may be impossible to detect with an experiment randomized at the individual or village level. However, it does not necessarily provide the full treatment effect. In future work, we therefore intend to combine these results with a structural model, as well as with data on the geography and trading networks observe in our survey data, to estimate the full treatment effects on trade flows and market integration.