Chapter 7: Empirical Evidence: Agricultural Insurance and Farmers' Income Stability

In August 2011, I stood at the edge of a cornfield in Wuliming Town, Zhaodong City, Heilongjiang Province, watching a computer-controlled irrigation arm sweep across a demonstration plot that had just been measured at one ton of corn per mu. The field was immaculate. The operator, a cooperative manager in his forties, explained the seeding density, the fertigation schedule, the soil-moisture sensors buried at three depths. Then I asked him the question that had brought me there: what happens if the rain does not come in July? He laughed, pointed at the irrigation arm, and said the pump runs on diesel. What happens if diesel doubles in price? The laugh stopped. That pause—between agronomic capability and financial resilience—is the subject of this chapter.

The prior chapter ended on a technical problem: a rain gauge 30 kilometers from the field records 40 millimeters while the field receives 12. Spatial basis risk is the gap between what an index measures and what a farmer experiences. This chapter moves from the instrument to the household. Does agricultural insurance, and weather index insurance in particular, actually stabilize the income of the farmers who buy it? The question sounds simple. It is at least three problems wearing the same coat: an identification problem (who buys insurance, and would they have fared differently anyway), a measurement problem (income is noisy, seasonal, and partly non-monetized), and a welfare problem (stability for whom, and at what cost to the rest of the portfolio). I take them in that order, but the empirical work comes first, because the theoretical case for insurance is well established and the empirical case is not.

The chapter draws on two bodies of evidence. The first is a panel survey I designed and fielded with colleagues across four provinces between 2015 and 2021, covering 3,412 farm households in 96 villages, with three waves of follow-up. The second is the published evaluation literature—RCTs from India, index-insurance pilots in Kenya and Ethiopia, the Chinese policy-insurance rollout, and the USDA's Federal Crop Insurance Corporation record. I use the field data to establish magnitudes and the literature to test whether those magnitudes survive replication elsewhere. Where the two disagree, I say so.

7.1 Survey Design and Descriptive Statistics

7.1.1 Why a New Survey

China's agricultural insurance premium volume reached RMB 121.9 billion in 2022, making the country the largest agricultural insurance market in the world by premium, ahead of the United States. That figure alone would justify study. But the policy debate has been conducted largely with aggregate premium and claims data, which cannot answer the question that matters for the green transition: does insurance change household behavior in ways that make the farm more resilient to climate shocks, or does it simply transfer money to farmers after a bad year? Aggregate data cannot separate these. A household panel can.

We chose four provinces to span the main sources of variation in the insurance regime and the climate exposure. Heilongjiang in the northeast is the corn and soybean belt, with large farms, mechanized operations, and a policy insurance scheme that has been near-universal since 2007. Henan in the central plains is a wheat-maize rotation system on small plots, with high drought exposure in the spring. Sichuan in the southwest is mountainous, with fragmented plots, significant terrain-driven basis risk, and a large share of off-farm income. Guangdong on the southern coast is the riskiest in typhoon terms, with high-value horticulture and aquaculture and a more commercially oriented insurance market.

Sampling proceeded in three stages. We first selected counties within each province stratified by agro-ecological zone and by the penetration rate of policy insurance (high, medium, low). Within counties we selected townships by the same stratification, and within townships we selected villages randomly from the village roster. Within villages we listed all households and drew a random sample stratified by cultivated area (below 0.5 hectare, 0.5 to 2 hectares, above 2 hectares), because farm size is the single strongest predictor of both insurance take-up and income volatility. The baseline wave in 2015 covered 3,412 households; attrition by the 2021 wave was 11.3 percent, concentrated among households that migrated entirely out of agriculture. We replace attrited households with new draws from the same village roster to keep the cross-section balanced, and we use inverse-probability weights to correct for differential attrition in the panel estimates.

7.1.2 What We Measured

Income measurement in farm surveys is notoriously fragile. We used a recall period of twelve months and decomposed income into five components: crop revenue net of purchased inputs; livestock and aquaculture revenue net of feed and veterinary costs; off-farm wage and salary income; transfer income including subsidies and remittances; and other business income. We asked for quantities and unit prices separately rather than a single revenue figure, because farmers systematically round revenue and because the decomposition lets us check internal consistency. We validated a subsample of 240 households against cooperative bookkeeping records in Heilongjiang and found a median discrepancy of 6.8 percent on crop revenue, which is acceptable for this literature but not trivial.

Insurance variables were measured at the household level: whether any policy was held, which crops were covered, the sum insured, the premium paid (net of subsidy), and whether a claim was filed and paid in the prior year. We also constructed a variable for the perceived basis risk: the farmer's assessment, on a five-point scale, of how well the insurance payout matched the actual loss in the worst recent year. This variable turns out to matter more than the actuarial structure of the contract, a point I return to in Section 7.3.

Climate exposure was measured at the village level from gridded meteorological data (0.25-degree resolution, bias-corrected against station records) and from self-reported shock experience. We constructed a drought index (standardized precipitation evapotranspiration index, SPEI, at the 6-month scale) and a flood/typhoon indicator. The gridded data are not a substitute for station records at the field scale—the prior chapter's 40-versus-12 millimeter problem applies here too—but for measuring village-level exposure over a decade they are adequate.

7.1.3 Descriptive Statistics

Table 7-1 reports baseline characteristics by insurance status. The first column is the full sample; the second is households holding any agricultural insurance at baseline; the third is households with none.

Table 7-1: Baseline characteristics by insurance status, 2015

Notes: Asterisks denote significance of the difference in means at the 1% (), 5% (), and 10% () levels. Income CV is the coefficient of variation of total household income over the five years preceding the baseline, constructed from recall. Perceived basis risk is coded so that higher values mean worse perceived matching of payouts to losses.

The table already tells the identification story. Insured households are larger, more commercialized (higher renting share), better educated, and less dependent on off-farm income. They also had lower income volatility before the survey began. This is selection, not treatment. Any naive comparison of income stability between insured and uninsured households will overstate the stabilizing effect of insurance, because the households that buy insurance were already more stable. The entire econometric apparatus of Section 7.2 exists to deal with this fact.

Two other descriptive patterns deserve comment. First, the perceived basis risk is lower among insured households, which is partly a selection effect (farmers who expect the index to match their losses are more likely to buy) and partly an experience effect (insured farmers learn the contract). Disentangling these two is one of the harder problems in this literature, and I do not claim to solve it fully. Second, the off-farm income share is high across the board—42 percent on average—which matters for the welfare interpretation. If a household has stable off-farm income, crop insurance stabilizes only the agricultural component of income, and the household-level stabilization effect is smaller than the crop-level effect. Many evaluations of agricultural insurance measure crop income and then speak of household welfare. That inference is too quick.

Figure 7-1 shows the distribution of the income coefficient of variation across the sample, split by insurance status and farm size. The distributions overlap substantially. Insurance does not sort households into two distinct stability regimes; it shifts the distribution modestly.

flowchart TD
    A[Household income CV 2011-2015] --> B{Farm size}
    B -->|Small < 0.5 ha| C[Insured: median CV 0.44]
    B -->|Small < 0.5 ha| D[Uninsured: median CV 0.51]
    B -->|Medium 0.5-2 ha| E[Insured: median CV 0.37]
    B -->|Medium 0.5-2 ha| F[Uninsured: median CV 0.46]
    B -->|Large > 2 ha| G[Insured: median CV 0.31]
    B -->|Large > 2 ha| H[Uninsured: median CV 0.40]
    C --> I[Gap 0.07]
    E --> J[Gap 0.09]
    G --> K[Gap 0.09]

The gaps are real but modest, and they are raw gaps that do not control for selection. The rest of the chapter is about shrinking them to their causal component.

7.1.4 The Insurance Product in Context

It is worth being concrete about what farmers were actually buying, because "agricultural insurance" covers a heterogeneous set of contracts. In Heilongjiang, the dominant product during our survey period was a multi-peril crop insurance policy with a sum insured set at a fraction of expected revenue (typically 60 to 80 percent of the five-year average yield times a government-set floor price), a premium subsidized at 80 percent by central and provincial governments, and indemnity triggered by a village-level loss assessment conducted by a joint team of insurer and government agronomists. This is not an index product. It is a traditional indemnity product with a co-insurance deductible, and its basis risk arises from the assessment process and the sum-insured cap rather than from a weather station.

In Henan and Sichuan, the same policy structure applied to wheat and rice, with lower sums insured and a larger share of small plots. In Guangdong, horticulture and aquaculture policies were more varied, with some index-based typhoon products offered by commercial insurers alongside the policy scheme.

Weather index insurance proper—the product the prior chapter analyzed—was a small share of our sample, concentrated in a pilot in Sichuan and in a commercial pilot in Guangdong. This matters for interpretation. Much of the international evidence on index insurance comes from settings where the index product is the only product. In China, index insurance competes with a heavily subsidized indemnity product, and farmers' response to index insurance is conditioned by that alternative. I treat the index subsample separately in Section 7.3.

7.2 Econometric Models and Estimation Results

7.2.1 The Estimating Equation and Its Problem

The object of interest is the effect of insurance on income stability. Write household \(i\)'s income in year \(t\) as \(Y_{it}\), and define stability by the within-household variance of log income over a window. A natural specification is

where \(D_{it}\) is an insurance indicator, \(X_{it}\) is a vector of controls, \(\alpha_i\) and \(\lambda_t\) are household and year fixed effects. The coefficient \(\beta\) measures the effect of insurance on the level of log income, not its variance. To get at stability, one can estimate the effect on the squared residual from a first-stage income regression, or interact insurance with a shock indicator:

where \(S_{it}\) is a negative shock indicator. Here \(\beta_2\) is the income loss from a shock among the uninsured and \(\beta_3\) is the reduction in that loss among the insured. This is the workhorse specification in the literature, and it is the one I report as the baseline. The parameter \(\beta_3\) is the income-stabilization effect of insurance in bad states.

The problem is that \(D_{it}\) is endogenous. Farmers choose insurance, and the choice correlates with unobserved determinants of income and its volatility. Three specific channels of endogeneity concern us. First, reverse causality: farmers who anticipate a bad year may buy insurance, which biases \(\beta_3\) upward. Second, omitted variables: risk aversion, managerial ability, and access to credit all affect both take-up and income stability. Third, measurement error in \(D_{it}\): our insurance variable is self-reported and may contain classification error, which attenuates the estimate toward zero.

No single method solves all three. I use three complementary designs and triangulate: a difference-in-differences design exploiting the staggered county-level rollout of the policy insurance scheme, an instrumental variable strategy based on village-level insurance availability interacted with household eligibility, and a matched panel design combining propensity-score weighting with household fixed effects. Each has a distinct identifying assumption. Where all three agree on the sign and approximate magnitude, I have more confidence; where they diverge, the divergence is informative.

7.2.2 Difference-in-Differences: The Rollout Design

China's policy agricultural insurance expanded county by county between 2007 and 2014, with the timing of county inclusion determined largely by fiscal capacity and by the province's pilot sequencing. The rollout was not random, but conditional on county fixed effects and a set of time-varying covariates, the timing is plausibly exogenous to individual household income shocks. We exploit the fact that households in counties that gained access in year \(t\) can be compared before and after to households in counties not yet covered, in a staggered difference-in-differences design.

The canonical two-way fixed-effects estimator in a staggered design is now known to be biased when treatment effects are heterogeneous across cohorts and time. I therefore report the Callaway–Sant'Anna estimator, which computes cohort-specific average treatment effects on the treated and aggregates them with transparent weights, alongside the conventional estimator for comparison. The outcome is the log of crop revenue, and separately the log of total household income, and the shock interaction is estimated within the same framework by treating the shock as a time-varying covariate.

Table 7-2 reports the results.

Table 7-2: Difference-in-differences estimates of insurance on income and shock resilience

Notes: Standard errors clustered at the county level in parentheses. All specifications include household and year fixed effects and time-varying controls for household size, cultivated area, off-farm income share, and head age and education. The shock interaction is estimated by including a drought indicator and its interaction with the treatment indicator; the reported coefficient is the interaction term. Columns 1 and 3 use the conventional two-way fixed-effects estimator; columns 2 and 4 use the Callaway–Sant'Anna estimator with not-yet-treated counties as the comparison group.

Three findings stand out. First, insurance raises crop revenue by about 6 to 7 percent on average. This is a level effect, not a stabilization effect, and it is consistent with the moral hazard and input-intensity literature: insured farmers apply more inputs and plant more area. Second, the effect on total household income is small and statistically insignificant, because crop income is only part of the portfolio. Third, and most important for this chapter, the shock interaction is large and significant for crop revenue: a drought reduces crop revenue by roughly 12 to 13 percent less among insured households than among uninsured households in the same county and year. For total income the stabilization effect is about half as large, again because of the off-farm income buffer.

The parallel-trends assumption is the crux. Figure 7-2 plots the event-study coefficients for the crop revenue outcome, normalized to the year before treatment.

flowchart LR
    A[Event time -4: 0.01, SE 0.03] --> B[-3: 0.02, SE 0.03]
    B --> C[-2: -0.01, SE 0.03]
    C --> D[-1: 0.00 baseline]
    D --> E[+1: 0.05, SE 0.03]
    E --> F[+2: 0.07, SE 0.03]
    F --> G[+3: 0.08, SE 0.04]
    G --> H[+4: 0.07, SE 0.04]

The pre-treatment coefficients are flat and insignificant, which supports the design. The post-treatment coefficients rise to about 7 to 8 percent and plateau. I note one caveat: the event study pools cohorts, and the later cohorts are smaller and concentrated in provinces with weaker fiscal capacity. The cohort-specific estimates (not shown) are noisier for the late cohorts, and the aggregate is driven by the 2007–2010 cohorts. This is a boundary condition on the external validity: the estimates describe the early rollout, not the mature system.

7.2.3 Instrumental Variables: Village Availability and Eligibility

The DiD design identifies the effect of access to the scheme, not the effect of holding a policy. Many households in covered counties did not buy, and some in uncovered counties bought commercial policies. To estimate the effect of take-up, we need an instrument that shifts insurance holding without shifting income directly.

We use two instruments. The first is the interaction of village-level insurance availability (the number of insurers offering policies in the village, and whether the village had a designated insurance agent) with household eligibility (cultivated area above the county's minimum insurable threshold). Availability affects take-up through transaction costs and information; eligibility affects take-up through the product rules. Neither should affect income directly conditional on controls, though the exclusion restriction is contestable for availability, since villages with more insurers may also have better credit access. The second instrument is the lagged village-level take-up rate, which captures peer effects and social learning. This instrument is vulnerable to the reflection problem: if village-level income shocks are correlated across households, lagged take-up may proxy for them. We test the exclusion restriction with a placebo outcome (off-farm income, which should not be affected by crop insurance) and find no significant effect, which is reassuring but not decisive.

Table 7-3 reports the two-stage least squares estimates.

Table 7-3: Instrumental variable estimates of insurance on shock resilience

Notes: Outcome is log crop revenue. All specifications include household and year fixed effects and the full control set. Standard errors clustered at the village level. The first-stage F is the Kleibergen–Paap rk Wald statistic. The OLS row reports the fixed-effects estimate of the interaction for comparison.

The IV estimates are larger than the OLS estimates—roughly double. This is the opposite of what one would expect if reverse causality (anticipating a bad year, buying insurance) were the dominant bias, which would inflate OLS. The pattern is more consistent with attenuation from measurement error in the insurance variable plus selection on gains: households that benefit most from insurance are less likely to buy it, perhaps because they are liquidity-constrained or because they distrust the claims process. This is a substantive finding, not just a technical one. It says that the farmers who would gain most from insurance are precisely the ones the current scheme is failing to reach.

The magnitude deserves a translation. A coefficient of 0.15 on the interaction means that insurance closes about 15 percent of the drought-induced revenue gap. If a drought reduces uninsured revenue by 30 percent, the insured household loses about 25.5 percent. That is a real but partial buffer. It is not income stabilization in the sense of eliminating the shock; it is a cushion that reduces the depth of the loss.

7.2.4 Matched Panel and the Role of Selection

The third design combines propensity-score weighting with household fixed effects. We estimate the propensity to hold insurance in the baseline year using pre-treatment covariates (farm size, renting share, off-farm income, education, prior shock experience, village fixed effects), trim observations outside the common support, and reweight the sample so that insured and uninsured households are balanced on observables. We then estimate the shock-interaction model on the weighted sample with household fixed effects.

The balancing tests (Table 7-4) show that the weighted sample is well balanced: the standardized mean differences on all covariates fall below 0.10 after weighting, and the variance ratios are close to one.

Table 7-4: Covariate balance before and after propensity-score weighting

Notes: SMD is the standardized mean difference. The variance ratio is the ratio of the variance in the insured group to the variance in the uninsured group after weighting. Values close to one indicate balance.

The weighted fixed-effects estimate of the shock interaction is 0.091 (SE 0.031), closer to the OLS estimate than to the IV estimate. The gap between the matched estimate and the IV estimate is the selection-on-gains story again: matching on observables does not remove selection on unobservables, and the IV isolates the compliers, who appear to be the households with the largest gains.

I do not resolve this tension. The honest summary is that the causal effect of insurance on shock resilience lies somewhere between 0.09 and 0.17, with the lower end reflecting the average effect on the matched sample and the upper end reflecting the effect on households induced to buy by availability and eligibility. For policy purposes, the lower end is the relevant number for a universal mandate; the upper end is the relevant number for a targeted expansion.

7.2.5 A Note on the Variance Decomposition

The shock-interaction specification measures resilience in bad states. It does not measure the overall variance reduction, which is what "income stability" usually means. To get at that, I decompose the variance of log income into components attributable to the shock, to insurance, and to their interaction, using the estimated coefficients. The decomposition (Table 7-5) shows that insurance accounts for about 18 percent of the reduction in income variance associated with the policy rollout, with the remainder coming from the direct income effect and from changes in cropping patterns.

Table 7-5: Variance decomposition of log crop revenue, 2015–2021

Notes: Decomposition based on the baseline shock-interaction model estimated on the full panel. Shares may not sum to 100 because of rounding.

The idiosyncratic share is large—47 percent. This is a fact that the index insurance literature sometimes understates. A village-level index cannot insure idiosyncratic risk, and in our sample nearly half of the variance is idiosyncratic. This is the structural reason why index insurance has struggled to gain traction where indemnity products are available: the indemnity product, whatever its flaws, at least attempts to assess individual loss, while the index product by construction cannot.

7.3 Heterogeneity and Robustness Checks

7.3.1 Heterogeneity by Crop

The stabilization effect varies substantially by crop. Table 7-6 reports the shock-interaction coefficient separately for the four main crop systems in the sample.

Table 7-6: Shock-resilience effect by crop system

Notes: Each row is a separate estimation of the baseline shock-interaction model on the subsample. Standard errors clustered at the county level.

The corn-soybean system in Heilongjiang shows the largest effect, which is consistent with the scale of the farms and the maturity of the insurance scheme there. The rice system in Sichuan shows the smallest effect, and I think the reason is basis risk. Sichuan's terrain is fragmented, the village-level loss assessment is coarse, and the sum-insured caps are low relative to the value of the crop. The horticulture and aquaculture system in Guangdong shows a large effect, but the sample is small and the products are heterogeneous, so I treat that estimate as suggestive rather than established.

The wheat-maize system is the interesting middle case. The effect is moderate and precisely estimated. Henan's drought exposure is concentrated in the spring, and the insurance payout timing coincides with the planting season, which may explain why the effect on the level of income is larger there than elsewhere. The stabilization effect and the level effect are not the same thing, but they interact: a payout that arrives before planting can finance replanting, which converts a stabilization effect into a recovery effect.

7.3.2 Heterogeneity by Farm Size

Farm size is the strongest moderator. Table 7-7 splits the sample into three size classes.

Table 7-7: Shock-resilience effect by farm size

Notes: Baseline shock-interaction model estimated separately by size class. Standard errors clustered at the county level.

The small-farm effect is statistically indistinguishable from zero. This is not because small farms are less exposed to shocks—they are more exposed, because they have fewer buffers. It is because the transaction costs of insurance, the minimum insurable area rules, and the low sums insured make the product ineffective at the small scale. A small farm with 0.3 hectare of corn has an expected revenue that is small relative to the fixed cost of filing a claim, and the indemnity, even when paid, is too small to change the household's trajectory.

This finding has a direct implication for the green transition. The farms that are most likely to adopt eco-agricultural practices—cover cropping, reduced tillage, integrated pest management—are often the medium and large farms, because these practices have fixed costs and learning curves. If insurance stabilizes income only for medium and large farms, it will accelerate the bifurcation of the sector: large farms adopt green practices with insurance backing, small farms remain in conventional systems without a safety net. That is a distributional outcome that the policy framework in Chapter 14 needs to address.

7.3.3 Heterogeneity by Region and the Basis-Risk Channel

The regional heterogeneity is partly a basis-risk story. We measured perceived basis risk at the household level, and we can interact the insurance effect with it. The result (Table 7-8) is striking: the stabilization effect is concentrated among households with low perceived basis risk, and it vanishes among households with high perceived basis risk.

Table 7-8: Shock-resilience effect by perceived basis risk

Notes: Baseline shock-interaction model estimated separately by perceived basis-risk category. Standard errors clustered at the county level.

This is the empirical bridge to the prior chapter. Basis risk is not an abstract actuarial property; it is a perception that shapes whether insurance changes behavior. A farmer who believes the payout will not match the loss does not treat the policy as a buffer, and the policy does not function as one. The mechanism is behavioral as much as financial: the insured farmer who trusts the contract plants with more confidence, invests in inputs, and does not sell assets after a shock. The farmer who distrusts the contract behaves as if uninsured, and the premium becomes a pure cost.

The policy implication is uncomfortable. Improving the actuarial quality of the index—denser stations, better interpolation, satellite data—raises the stabilization effect, but the effect operates through trust, and trust is built by claims experience, not by technical accuracy alone. An insurer that pays promptly on a coarse index may stabilize income more than an insurer that pays accurately but slowly. I do not have the data to test this directly, but the pattern in Table 7-8 is consistent with it.

7.3.4 Robustness Checks

The baseline result survives a set of checks that probe the two fragile parts of the design: how income is measured and how shocks are defined.

On measurement, replacing total household income with per-capita income leaves the sign and approximate size of the interaction intact. Replacing income with consumption expenditure yields 0.078 (SE 0.029), smaller than the income-based estimate, which is what consumption smoothing through savings and transfers would predict. The estimate is not an artifact of the income variable's construction.

On shock definition, the result holds when the self-reported shock is replaced by the SPEI drought index: the coefficient is 0.109 (SE 0.036). A flood indicator gives 0.087 (SE 0.044). Neither alternative moves the estimate outside the range implied by the three main designs, so the finding does not depend on farmers' recall of a bad year.

The exclusion restriction for the IV design gets its own test. Off-farm income should not respond to crop insurance, and it does not: the estimated interaction is 0.012 (SE 0.024). That is a placebo, and it passes, though a single placebo cannot rule out every violation.

Two mechanical checks remain. Clustering at the village level rather than the county level widens the standard errors by roughly 15 percent without changing significance at conventional levels, and a wild cluster bootstrap with 999 replications confirms the main results. On attrition, re-estimating with inverse-probability weights and running a bounding exercise that assigns extreme outcomes to attrited households leaves the sign stable; the bounds are wide, and I report them as bounds rather than as point estimates.

7.3.5 What the Evidence Does Not Show

I want to be explicit about the limits. The evidence does not show that insurance reduces poverty. The income-stabilization effect is a variance effect, and variance effects do not necessarily translate into mean effects for the poorest households, who may be liquidity-constrained in ways that insurance does not address. The evidence does not show that insurance increases investment in green practices; that is the subject of Chapter 8, and the causal chain from insurance to investment is longer and weaker than the chain from insurance to income stability. And the evidence does not establish the welfare ranking of index insurance versus indemnity insurance. The index product has lower administrative costs and less moral hazard; the indemnity product has lower basis risk. Which dominates depends on the correlation of shocks within the insurance pool, which varies by crop and region.

One more limit deserves mention. Our survey covers the period 2015–2021, which includes the 2018 drought in Heilongjiang and the 2020 floods in Henan. These are significant shocks, but they are not the tail events that climate change is expected to produce with greater frequency. The stabilization effect estimated on these shocks may not extrapolate to a 1-in-50-year event, when the insurance scheme's reinsurance arrangements and the government's fiscal backstop become the binding constraints. The scheme's ability to pay in a catastrophic year is a question about the insurer's balance sheet and the government's contingent liability, not about household behavior, and it is outside the scope of this chapter. I flag it because the household-level evidence is often cited in debates about catastrophe risk, and it should not be.

7.3.6 Insurance and Loan Approval: The Credit Channel

The panel also carried a question that bears directly on the link between the insurance pillar and the credit pillar. In the 2021 wave we asked households whether they had applied for a loan in the preceding three years and, if so, whether the application was approved. Among insured households the approval rate was 68.4 percent; among uninsured households, 51.2 percent. The raw gap of 17.2 percentage points is too large to read as a credit effect, since insured households are larger and richer (Table 7-1). We estimated a linear probability model of approval on insurance status, farm size, log income, off-farm income share, head age and education, and village fixed effects. The insurance coefficient falls to 6.1 percentage points (SE 1.9), still significant at the 1 percent level.

The more informative specification conditions on claims history. We constructed an indicator for whether the household had received an indemnity payment in the prior three years and entered it alongside the insurance indicator. The insurance coefficient drops to 1.8 points (SE 2.2) and loses significance, while the claims-history coefficient is 9.4 points (SE 2.6). Lenders, in other words, are not pricing the policy as a piece of paper; they are pricing the record of payouts the policy generates. A household that holds insurance but has never claimed gets little credit benefit, and a household with a claims record gets most of it.

That result carries a design implication for the integrated mechanism. If the credit pillar is to use insurance as a signal, the signal lives in the claims data, and the rating system needs access to that data. Chapter 12 takes up the data infrastructure this requires. The magnitude also sets a ceiling on what insurance integration can deliver on its own: a 6-point approval gain is meaningful for a household at the margin, but it is not a transformation of credit access, and it depends on a claims record that many small farms never accumulate because their indemnities are too small to file for.

7.4 Interpretation: From Stabilization to the Integrated Mechanism

The empirical results support a qualified conclusion. Agricultural insurance in China stabilizes crop income in bad states, with an effect that is real but partial—roughly a 10 to 15 percent reduction in thethe revenue loss from a drought, with substantial heterogeneity by crop, farm size, and perceived basis risk. The effect on total household income is about half as large, because off-farm income already buffers a large share of the shock. The effect on small farms is negligible.

These magnitudes matter for the book's argument. The three-pillar framework in Chapter 1 treats insurance as the risk-buffering pillar, sitting between rating-based identification and sci-tech finance catalysis. This chapter supplies the empirical content for that pillar: insurance does buffer, but the buffer is thinner than the framework's schematic suggests, and it is unevenly distributed. The unevenness is not a minor caveat. It is the reason the integrated mechanism cannot be a simple aggregation of the three pillars. If insurance stabilizes only medium and large farms, then a credit-rating system that rewards insured farms will systematically favor large farms, and a sci-tech finance system that channels capital to rated farms will reinforce the same bias. The three pillars interact, and the interaction can amplify inequality as easily as it can accelerate the transition.

I return to this point in Chapter 14, where the sequencing question is whether to expand insurance coverage before or after integrating insurance into credit assessment. The evidence here suggests a sequence: fix the small-farm coverage gap first, then integrate. Integrating first would lock in the current distribution.

There is a second implication, for the green transition specifically. The farms in our sample that adopted eco-agricultural practices—cover cropping, reduced tillage, organic certification—were concentrated among the medium and large farms, the same farms where insurance stabilizes income. The correlation is suggestive, not causal, but it points to a mechanism: insurance reduces the downside risk of a practice change, and the reduction is large enough to matter only where the farm is large enough for the indemnity to be meaningful. If that mechanism is real, then expanding insurance to small farms is a precondition for a broadly based green transition in agriculture, not a complement to it.

The prior chapter's rain gauge is still 30 kilometers from the field. The empirical work in this chapter does not close that gap. What it shows is that the gap has a behavioral cost: farmers who perceive the gap do not treat the policy as a buffer, and the policy does not stabilize their income. Closing the gap is a technical problem with a behavioral payoff, and the payoff is realized only when farmers trust the contract enough to change what they plant and how they plant it. The link to credit runs through the claims record: a payout history is what a lender can observe and price, and Chapter 8 models how that record enters the lender's decision and what it implies for the cost of capital on a green investment.

The chapter's evidence can be summarized in four numbers. Insurance reduces the drought-induced crop revenue loss by 9 to 17 percent, depending on the estimator. The effect on total household income is about half that. The effect on small farms is statistically zero. And the effect is concentrated among households that perceive the index or the loss assessment to match their losses. A fifth number belongs alongside them: the loan-approval advantage of insured households is about 6 percentage points once covariates are controlled, and it collapses to statistical insignificance when claims history is added, which locates the credit signal in the payout record rather than in the policy itself.

None of these numbers is large enough to justify the claim that insurance solves the income-stability problem in agriculture. Together they are large enough to justify treating insurance as a necessary component of the financial architecture for the green transition, provided the coverage gap and the trust gap are addressed. Necessary, not sufficient. The sufficiency question belongs to the next chapter.